From the journal RSC Chemical Biology Peer review history

06-May-2020

Dear Dr Olsen:

Manuscript ID: CB-ART-03-2020-000036
TITLE: Selective inhibitors of SIRT2 regulate perinuclear α-tubulin acetylation, migration, and invasion of breast cancer cells

Thank you for your submission to RSC Chemical Biology, published by the Royal Society of Chemistry. I sent your manuscript to two reviewers and I have now received their reports which are copied below.

I have carefully evaluated your manuscript and the reviewers’ reports, and the reports indicate that major revisions are necessary. Both reviewers have raised a number of issues regarding the setup/validation of biochemistry assay and the investigation on target engagement of SIRT2 inhibitor in cells, which are critical to fully address.

Please submit a revised manuscript which addresses all of the reviewers’ comments. Your revised manuscript will be sent to the original reviewer(s) for further peer review. When you submit your revised manuscript please include a point by point response to the reviewers’ comments and highlight the changes you have made. Full details of the files you need to submit are listed at the end of this email.

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Reviewer 1

I have received this paper on SIRT inhibitors. It looks nice and appears to be organized, which is a good start. I commend the authors on making what appears to be a neat paper.

However, there are a huge number of issues here that render it almost impossible for me to even review the in vitro section, at this junction. The in-cell section is better, but there are still issues there. I am thus going to focus on some core issues that must be fixed, mainly in the first two figures, and the authors can revamp all relevant data, and add correct needed data clearly in the light of those issues. For the reasons outlined below, this submission at the present stage is rather a pre-submission.

I believe this to be a fair way to deal with these issues as I also understand that the work in this area has been historically of low technical quality, and so I understand why the authors may be lost. Given these mitigating factors, I would be very happy to re-review a suitably accurate and detailed manuscript, avoiding obvious traps and that was more erudite and correctly conducted. After the authors are able to make headway in bringing this up to speed, another round of revision may be necessary.

In general, inhibition assays are complex; please treat them as such. So the kinetics assays can be interpreted correctly: enzyme concentration (each time) needs to be stated in each sub section of the figure legend (or globally, if this is the same throughout); concentration of competitive ligands, also need to be put in, as does their Km (so it is clear if the authors are saturating the ligands in the assay, or not, and by how much). Submission of this information is necessary for the readers/reviewers to understand if the assays were conducted correctly. When I looked at the SI, I found numerous different enzyme concentrations pertaining to different assays. It is not immediately apparent what was used for what, and a reader should not have to either guess nor forage for parameters that are essential to understand kinetics assays. Finally, Km’s (at least for acetyl substrates) should be calculated by the authors themselves as well, as these values reported in the literature are widely known to be not always reliable, and these parameters can inform if an assay is decent/has been performed with technical rigor/competence.

This leads me onto 3 main issues.
<b>Major issue 1:</b>
The IC50s shown in Scheme 1 are more or less identical and at least bottom out at a relatively standard number, despite severe changes in chemical structure. This observation should have been unsurprising to the authors, as the IC50’s shown are all close to the concentration of the protein used in the assay (~100 nM, or 500 nM?). It is not abundantly clear from the experimental section, but either way, this should have been a red flag). Such a situation is correctly referred to as tight binding and cannot be accurately analyzed using IC50. This is because IC50 cannot be less than 50% of the enzyme concentration, regardless competitive ligands etc, and most mechanisms. (Hence IC50-values can tend to bottleneck around the concentration of the enzyme). Given issues measuring enzyme concentration (e.g., batch to batch variations), there is reason to believe that many of the quoted values in the manuscript could be limited by enzyme concentration, particularly in g, but also in f and e. Indeed, we have 30 compounds all of which lie in a range of 3-fold of 100 nM, (ironically) the enzyme concentration… Please recalculate the SAR using an appropriate concentration of the enzyme (several fold below that of the ultimately calculated IC50 concentration. Start with all compounds with IC50 less, or equal to 120 nM, within error (around 12 compounds); but this may need to be expanded.

Please also write out the “concentration response equation” used from Prism (was this cooperative, if so, add cooperativity). Just as a piece of advice, I am not convinced that the tight binding equation could be used in this situation. This is even more apparent as the authors discuss below, the situation is complex, and possibly time dependent. Should affinity of the molecules be so high as to render IC50 essentially unmeasurable, the authors can switch to a higher concentration of substrate to shift the EC50 (see Cheng Prussov below). At worst, if for a few compounds they cannot calculate IC50 that is not enzyme limited, they can state clearly this is the lowest value measurable by the assay, or use the HPLC assay with a few comparison compounds.
In general, suitable application of inhibitor kinetics should allow better and more reliable SAR to be derived. Better and more expansive data will also help the authors avoid divulging large amounts of text to a 5 fold change. Which is overall, minor.

<b>Major Issue 2.</b>
A similar issue appears to occur in Figure 3C. I imagine that the inhibitors more effective against myristoylated substrate (e.g. S2iL5) are actually higher affinity binders to the protein. If they are not higher affinity binders, how can they show better inhibition for demyristoylase activity? However, in C, they all appear to have the same efficacy… Curious, no, as efficacy should correlate with affinity and we are looking at affinity to a substrate binding site? But this is not curious if b were not under tight binding behavior (due to competition with a better substrate shifting IC50 out of tight binding) and C were not so, due to weaker competition (back to tight binding). This is why it is useful to have the Km of the substrates and the concentration at hand, so one can analyze the data easily.

Based on these data, the authors launch into a soliloquy on IC50s. I think that this will be rather viewed as unwarranted by most readers as it should be obvious to anyone with an undergraduate degree, and is true for all inhibitors and modes of binding to some extent, more so when the authors get into issues with tight binding that are missed. Note, in general, the Cheng Prussov relationship shows: IC50 = KI * (L/Km) so given your discussion, this behavior is likely simply a manifestation of one system being above Km and the other being below.

<b>Major Issue 3</b>
We then go to an assay using a different substrate (likely with different Km, and different saturation during the assay) and enzyme concentration of 20 nM, in Figure 3F. Now we are out of tight binding behavior (as IC50’s of the molecules assayed are 80 nM or more, i.e. MUCH higher than enzyme concentration), and the inhibitors show similar behavior to what was shown for the myristylated substrate (yes grey and green are swapped, but they are still less effective than black, and blue is poor). Thus, I believe that the substrate is not so relevant; it is the enzyme concentration relative to the “true” IC50 that is important here. I could well be wrong, but history has shown us that this is a common mistake made and it is not disprovable based on the data currently presented.
This error may also impinge on Figure 3d, selectivity across SIRTs, as if (some) value(s) were limited by being under tight binding, or all curves were shifted (and enzyme concentrations were not even consistent between assays) these values are irrelevant.

<b>Other comments on kinetics</b>
Effect on AMC should be directly assessed by mixing the fluorophore with the compound and measuring fluorescence. Comparison to another assay, esp when you are claiming they are not readily comparable, is not particularly logical. As it stands, the use of the UPLC assay is relevant for other means, so it should be kept. But Amc quenching should be measured as well.

IN Figure S3, in general, a linear or near linear rate for 20 minutes should allow you to fit inhibition curves, should time dependent binding be meaningful. I remind the authors that inhibition is an exponential, so they do not need to plateau to fit anyway. So, I do not take the data provided as being indicative that traditional progress curve analysis could not be applied, especially not to the better inhibitors. I think that the inhibitors the authors chose here were not good, and not particularly time dependent, meaning that the experiment was not set for the right direction from the start, even though linearity for 20 mins should have let the authors know this was a worthwhile pursuit. More effective inhibitors, weighted with the correct amount of competitor substrate /enzyme concentrations with appropriate controls (for inhibition of trypsin inhibition by molecules, quenching of AMC, etc) may have been forth coming here. Furthermore, if the rate does tail off, this should also be fit and accounted for mathematically, especially as the authors’ signal to noise is very high (using dynafit, for instance). Using such analyses, very accurate analysis of unstable enyzmes can be performed and should be performed by the authors.

In SI Figure S3., it states that bending of curves for SIRT2 continuous traces suggests slow, tight binding kinetics. How is tight binding possible if the inhibitor is 100 μM and the enzyme is nM. This is reflected on page 13 where the readers are told there is a tighter conformation.

The effect of NAD+ on the molecules is poorly handled unfortunately. However, I do think that this will no longer be particularly relevant, once the kinetics are done properly. So this may be best to treat as vestigial and remove.

All of these points above should be remedied by both experiments and thoroughly revamping the text/legends, such that the data can be comparable within itself, consistent, and reviewable.

Biological assays
Why are the authors looking at stability in human serum? Wouldn’t microsomes be better, or the authors have just set the stall to look for PO drugs already? Should the latter be the case, please specify; otherwise the authors should justify why this was chosen.

What is GI50? Growth inhibition? This correctly refers to the swelling of a cell across the cell cycle, not viability or proliferation. The authors’ protocol for viability assays states that 5000-10000 cells were plated in 96 well plates. Left 1 day (for most cells HeLa and HEK, but not MCF7, that means a doubling, 10000-20000) then left for 72 h. (3 doublings for many lines). Thus, the cells were likely overgrown at the end of the assay. Such conditions tend to underestimate efficacy of molecules and can also be biased based on growth rates of individual cells, etc. Please repeat these assays starting with lower amounts of cells such that they are not confluent at the end of the assay. Be particularly careful of HeLa and HEK which grow fast, and show DMSO control live cells, at sub confluence, as an image at the end of the assay prior to harvesting. I should also state that alamarBlue is a much more reliable assay than what was used here.

Data in Figure 5 need to be quantified for each batch.

Inhibition of SIRT2 reduces breast cancer cell motility. This section is minimal and needs validation of targeting, and protein in observed phenotype, which are currently all lacking.
The authors need to verify phenotypes observed by targeted knockdown or knockout of SIRT2. Given the widely-known off-target issues of sh/siRNAs, knockdown should be performed with 3 different on target shRNA or siRNAs and three different control sh/siRNAs separately, with validation of knockdown performed at protein level (by western blot). Knockout similarly should be performed separately with various on target guide-RNA sequences. These lines should be sensitized or resistant to the compounds, based on the knockdown and phenotypes observed. Rescue should also be attempted, using a plasmid with an immortalized DNA sequence for the gene, for shRNA.
IC50 for proliferation inhibition for MCF7 should be added on the legend to Figure 6 so we are not confused. Please also add points to bar charts, not just “sem”.

Compounds – overall this is OK, but several compounds are worrisome.
- Are the authors claiming that the compound shown (in Page S94, trace in top right panel) is >95% pure? Typically one sees very few peaks if that is the case…


The peak height of the minor peak is around 5-10% of the top peak…

Many of the other compounds used here are also not what one would consider “pure”, based on NMR, at least. I would mark peaks that are egregious, but the authors have done that themselves by ignoring to integrate these themselves. MeOD may prove to be a better solvent to run NMR than DMSO; MeOD will help to flatten the base line at least. But this will not work for compounds such as 22, 19, 18, 11. And it cannot remove errant peaks in the C13 spectrum… Please show HPLC traces for the purified molecules as well, and if needs be, repurify the molecules or do not put them in. As it stands, their import in the SAR is far from secure.
The authors are assigning peaks based on what? Should there not be 2D NMR, please do add assignments. If there are 2D NMR, please put them in.

<b>General points </b>– western blots/imaging
-- All data need to be quantified.
-- All bar charts need to be analyzed by correct statistics. This should be done using corrected t-tests (e.g. Bonferroni etc) post ANOVA test where more than two comparisons are being compared, and a simple t tests were there are only 2 bars.
-- All bars should show individual points.
Please do not use two biological replicates performed in duplicate; the authors need at least N=3 independent biological replicates for each statement/claim made.

Reviewer 2

Olsen et al presents a series of SIRT2 inhibitors against both activities of SIRT2 deacetylation and demyristoylation. Using crystal structures, they analysed the SAR of their compounds at the substrate site, and then tested their effects in vitro and in breast cancer cell lines. The study made great effort on the investigation of potential best-in-class SIRT2 inhibitors, however, some explaination of their results are less than expected.
1. To my opinion, most known SIRT2 inhibitor at the substrate site could compete with substrates(acetylated and myristoylated proteins) even they may be not detected in original papers, the authors shouldnot have highlighted the feature like "no reported probe has been able to inhibit both of these SIRT2 activities".
2. Compared to a large number of previous SIRT2 papers, selectivity of the compounds havenot been extensively explored, such as other members in HDAC family (SIRT4-7 and HDAC1-11), it is not approprate to declare "selectivie SIRT2 inihitor" in the study.
3. Due to the dual effects of their compounds on both deacetylation and demyristoylation, it is very hard to distinguish different SIRT2 activities in breast cancer cells using their compounds; In other words, these compounds have no obvious advantage over the previous ones in the investigation of SIRT2 functions as chemical probes.

Dear Editor,
Thank you for handling our manuscript and for allowing us the extended time required to generate new data to address the concerns of the two reviewers. These comments were quite critical and, in some cases, phrased in an unnec-essarily arrogant and condescending tone, in my opinion. However, we are grateful for the requested additional experiments, in particular related to clear-ing up issues about compound IC50 values, which revealed much more differentiated SAR than originally anticipated and enabled addition of two new com-pounds that exhibit even higher potency than the original lead compounds.

We have thus reevaluated all compounds in a different assay, added two new compounds, and added data on cellular target engagement through cellular thermal shift assays (CETSA).

Please find a point-by-point response to the referees’ comments attached.
I am happy to provide our highly improved manuscript. I sincerely hope that you will find this revised version worthy of publication in RSC Chem. Biol.

Sincerely yours,

Christian Adam Olsen
Professor, PhD.



Point-by-point response to reviewers.
Reviewer(s)' Comments to Author

Reviewer: 1
1) Enzyme concentration (each time) needs to be stated in each sub section of the figure legend (or globally, if this is the same throughout); concentration of competitive ligands, also need to be put in, as does their Km (so it is clear if the authors are saturating the ligands in the assay, or not, and by how much).

Enzyme concentration and substrate concentration have been added to the figure legends for better clarity.

2) When I looked at the SI, I found numerous different enzyme concentrations pertaining to different assays. It is not immediately apparent what was used for what, and a reader should not have to either guess nor forage for parameters that are essential to understand kinetics assays. Finally, Km’s (at least for acetyl substrates) should be calculated by the authors themselves as well, as these values reported in the literature are widely known to be not always reliable, and these parameters can inform if an assay is decent/has been performed with technical rigor/competence.

The reviewer raises some important points for substrates and in particularly how it differs greatly across published literature. That is also why we benchmark with a number of previous SIRT2i. We di apologize for any confusion the original as-say descriptions may have caused and have now streamlined all protocols (and given values in captions as mentioned above).
Km values for SIRT2 with acetylated substrates are generally very high, which is what landed us in trouble with stoichiometric inhibition here, in the first place. So instead, we profiled all the compounds against a myristoylated substrate, which was made possible by the high affinity of our inhibitors (see more below).

3) Please recalculate the SAR using an appropriate concentration of the enzyme (several fold below that of the ultimately calculated IC50 concentration. Start with all compounds with IC50 less, or equal to 120 nM, within error (around 12 com-pounds).

We agree with the reviewer that all values of around 100 nM or less in the origi-nal manuscript were not providing an accurate picture of potency, due to stoi-chiometric inhibition as also stated by ourselves. Unfortunately, the deacetyla-tion assay (Kac substrate) could not be tweaked/optimized to work around this issue. But gratifyingly, on the other hand, our compounds exhibited strong enough affinity to inhibit the demyristoylase activity of SIRT2 (Kmyr substrate).
Because this exercise revealed differences between compound potencies in the SAR, that were not caught at stoichiometric inhibition, we were able to fur-ther optimize the final scaffolds by inverting the stereocenter at i+1 position. We are therefore grateful to the reviewer for requesting alternative determination of IC50 values.

4) Please also write out the “concentration response equation” used from Prism (was this cooperative, if so, add cooperativity). Just as a piece of advice, I am not convinced that the tight binding equation could be used in this situation.

The IC50 values are determined with a log(inhibitor) vs. response -- Variable slope (four parameters) assuming fast/on-fast/off kinetics. So, no tight binding equations are used for these assays.

5) The authors can switch to a higher concentration of substrate to shift the EC50 (see Cheng Prussov below). At worst, if for a few compounds they cannot calcu-late IC50 that is not enzyme limited, they can state clearly this is the lowest value measurable by the assay, or use the HPLC assay with a few comparison com-pounds.

In general, suitable application of inhibitor kinetics should allow better and more reliable SAR to be derived. Better and more expansive data will also help the au-thors avoid divulging large amounts of text to a 5 fold change. Which is overall, minor.
We strongly agree with this comment. Please see explanation of how we solved this under point 3 above.

6) A similar issue appears to occur in Figure 3C. I imagine that the inhibitors more effective against myristoylated substrate (e.g. S2iL5) are actually higher affinity binders to the protein. If they are not higher affinity binders, how can they show better inhibition for demyristoylase activity? However, in C, they all appear to have the same efficacy… Curious, no, as efficacy should correlate with affinity and we are looking at affinity to a substrate binding site? But this is not curious if b were not under tight binding behavior (due to competition with a better substrate shift-ing IC50 out of tight binding) and C were not so, due to weaker competition (back to tight binding). This is why it is useful to have the Km of the substrates and the concentration at hand, so one can analyze the data easily.

We again strongly agree with the reviewer that what is important regarding abil-ity to inhibit demyristoylation activity is simply the degree of affinity of the inhibi-tor, because it is simply competing against a substrate with substantially lower Km. Again, as discussed for the initial SAR, the seeming discrepancies arose because IC values were not predicted accurately due to the stoichiometric con-ditions in the original Kac assay. So, we agree that this is indeed not curious at all.
On the second part of the comment, I am afraid that the reviewer starts confus-ing the concept of tight-binding inhibitor kinetics with predictions one can make using the Cheng-Prusoff equation. Further explanation follows under point (7) below.

7) Based on these data, the authors launch into a soliloquy on IC50s. I think that this will be rather viewed as unwarranted by most readers as it should be obvious to anyone with an undergraduate degree, and is true for all inhibitors and modes of binding to some extent, more so when the authors get into issues with tight binding that are missed. Note, in general, the Cheng Prussov relationship shows: IC50 = KI * (L/Km) so given your discussion, this behavior is likely simply a mani-festation of one system being above Km and the other being below.
Thus, I believe that the substrate is not so relevant; it is the enzyme concentration relative to the “true” IC50 that is important here. I could well be wrong, but history has shown us that this is a common mistake made and it is not disprovable based on the data currently presented.

Again, we agree with the reviewer that operating at an enzyme concentration that is too high and therefore reaching inhibitor–enzyme stoichiometry is prob-lematic. We also agree that estimating Ki values requires determination of the Km value of the substrate, for both fast-on, fast-off and tight-binding kinetics. However, the Cheng-Prusoff equation does of course not accurately predict Ki values for slow, tight-binding inhibitors, which was the point we wanted to make. Based on the original data, this point may have gotten somewhat lost, because it was only substantiated by the preincubation experiments, due to continuous, progress curve experiments not being compatible with SIRT2 deacetylation (Kac). However, now realizing that our compounds are potent enough for inhibi-tion of the more challenging Kmyr substrates, we could indeed perform these types of experiments, which has now been included as a new Fig. 3. These ex-periments clearly show slow, tight-binding inhibition kinetics.

8) This error may also impinge on Figure 3d, selectivity across SIRTs, as if (some) value(s) were limited by being under tight binding, or all curves were shifted (and enzyme concentrations were not even consistent between assays) these values are irrelevant.

The panel has been removed and selectivity is addressed in Table 1 and Table S2 and S3. Conditions are noted in the footnotes for each table.

9) Effect on AMC should be directly assessed by mixing the fluorophore with the compound and measuring fluorescence. Comparison to another assay, esp when you are claiming they are not readily comparable, is not particularly logical. As it stands, the use of the UPLC assay is relevant for other means, so it should be kept. But Amc quenching should be measured as well.

We agree that there could potentially be a risk of quenching. However, none of thedata suggest this and this exact experiment has already been performed with the same AMC substrate and trypsin development for thioamide com-pounds by Mellini et al. Chem. Sci. 2017, 8, 6400. We therefore haven’t re-peated their experiment.

10) IN Figure S3, in general, a linear or near linear rate for 20 minutes should al-low you to fit inhibition curves, should time dependent binding be meaningful. I remind the authors that inhibition is an exponential, so they do not need to plat-eau to fit anyway. So, I do not take the data provided as being indicative that tra-ditional progress curve analysis could not be applied, especially not to the better inhibitors. I think that the inhibitors the authors chose here were not good, and not particularly time dependent, meaning that the experiment was not set for the right direction from the start, even though linearity for 20 mins should have let the authors know this was a worthwhile pursuit. More effective inhibitors, weighted with the correct amount of competitor substrate /enzyme concentrations with ap-propriate controls (for inhibition of trypsin inhibition by molecules, quenching of AMC, etc) may have been forth coming here. Furthermore, if the rate does tail off, this should also be fit and accounted for mathematically, especially as the authors’ signal to noise is very high (using dynafit, for instance). Using such analyses, very accurate analysis of unstable enyzmes can be performed and should be performed by the authors.
In SI Figure S3., it states that bending of curves for SIRT2 continuous traces suggests slow, tight binding kinetics. How is tight binding possible if the inhibitor is 100 μM and the enzyme is nM. This is reflected on page 13 where the readers are told there is a tighter conformation.
The effect of NAD+ on the molecules is poorly handled unfortunately. However, I do think that this will no longer be particularly relevant, once the kinetics are done properly. So this may be best to treat as vestigial and remove.

We withstand that continuous assays using Kac as substrate for SIRT2 is chal-lenging and that our problems were not due to lack of potency of the inhibitors. Nevertheless, kinetic insight has now been added by way of Kmyr based as-says instead.
Pre-incubation assays are very common and provides an easy to do and fast way of addressing whether inhibitors are slow binders. We have therefore kept these data in the SI for selected inhibitors from the early part of the SAR. How-ever, as discussed above, the discussion of our final candidates and their kinet-ics of inhibition do not rely on simple pre-incubation anymore.

11) Why are the authors looking at stability in human serum? Wouldn’t micro-somes be better, or the authors have just set the stall to look for PO drugs al-ready? Should the latter be the case, please specify; otherwise the authors should justify why this was chosen.

We believe that compound stability is a relevant measure to consider. Many dif-ferent systems could be chosen, enzymatic degradation, liver microsome, renal clearance, mouse PK etc etc. However, in this case we simple chose chemical stability in buffer and serum, which are relevant for the experiments performed in this report, and additionally in the more complex mixture of human serum. We believe that an exhaustive profiling of compound stability and PK would be far beyond the scope of this manuscript.

12) What is GI50? Growth inhibition? This correctly refers to the swelling of a cell across the cell cycle, not viability or proliferation. The authors’ protocol for viability assays states that 5000-10000 cells were plated in 96 well plates. Left 1 day (for most cells HeLa and HEK, but not MCF7, that means a doubling, 10000-20000) then left for 72 h. (3 doublings for many lines). Thus, the cells were likely over-grown at the end of the assay. Such conditions tend to underestimate efficacy of molecules and can also be biased based on growth rates of individual cells, etc. Please repeat these assays starting with lower amounts of cells such that they are not confluent at the end of the assay. Be particularly careful of HeLa and HEK which grow fast, and show DMSO control live cells, at sub confluence, as an image at the end of the assay prior to harvesting. I should also state that ala-marBlue is a much more reliable assay than what was used here.

We agree that original terminology was not accurate and have changed the discussion to mention cell-viability and EC50 values instead of GI50.
For HEK and HeLa, which grow the fastest we seeded only 5,000 cells and have never had any issues with over confluency. We have now specified number of cells for each cell line to clarify instead of a range for all.

13) Inhibition of SIRT2 reduces breast cancer cell motility. This section is minimal and needs validation of targeting, and protein in observed phenotype, which are currently all lacking. The authors need to verify phenotypes observed by targeted knockdown or knockout of SIRT2. Given the widely-known off-target issues of sh/siRNAs, knockdown should be performed with 3 different on target shRNA or siRNAs and three different control sh/siRNAs separately, with validation of knockdown performed at protein level (by western blot). Knockout similarly should be performed separately with various on target guide-RNA sequences. These lines should be sensitized or resistant to the compounds, based on the knock-down and phenotypes observed. Rescue should also be attempted, using a plasmid with an immortalized DNA sequence for the gene, for shRNA.

Clearly, the suggested experiments are highly valid and would be important to perform if aiming to prove that SIRT2 is responsible for the phenotype in ques-tion in MCF-7 cells. However, in our manuscript we simple describe our observa-tion that our potent SIRT2 inhibitors cause this effect in MCF-7 cells in culture. We also state that further work is required to investigate this phenotype in detail, which we consider beyond the scope of this work.

14) IC50 for proliferation inhibition for MCF7 should be added on the legend to Figure 6 so we are not confused. Please also add points to bar charts, not just “sem”.

This has been corrected

15a )Regarding compound purity

We have added the analytical HPLC traces for all final compounds

15b) Many of the other compounds used here are also not what one would con-sider “pure”, based on NMR, at least. I would mark peaks that are egregious, but the authors have done that themselves by ignoring to integrate these themselves. MeOD may prove to be a better solvent to run NMR than DMSO; MeOD will help to flatten the base line at least. But this will not work for compounds such as 22, 19, 18, 11. And it cannot remove errant peaks in the C13 spectrum… As it stands, their import in the SAR is far from secure.

We disagree with this comment. In our opinion, DMSO is indeed a much better solvent for peptides than MeOD, because one is not interested in exchanging the NH protons. CD3OH could be an alternative option but we have never had good experience with that solvent.
I should also mention that there are no “egregious” peaks in our spectra in general. For compound 22, there is a small impurity in the 1H NMR, which has now been denoted with asterisks. We do not see this as particular problematic since the purity is based on HPLC chromatography (97% for this particular com-pound). What the reviewer seemingly has failed to realize, is that compound 19 contains a proline giving rise to rotamers, as also mentioned in the data section for this compound. The two rotamers give rise to individual spin systems on the 1H NMR time scale (in this case at a ratio of approx. 10:1). I am not sure what the reviewer refers to in other spectra, but we have now picked out the peaks related to TFA counter ions from the HPLC purification (two quartets in 13C NMR spectra).
As mentioned above HPLC chromatograms have been added as proof of purity of all compounds.

16) The authors are assigning peaks based on what? Should there not be 2D NMR, please do add assignments. If there are 2D NMR, please put them in.

As stated on page S45 in the General experimental methods (now page S25): Assignments of NMR spectra are based on 2D correlation spectroscopy (COSY, HSQC, TOCSY and HMBC spectra). We have supplied raw mnova files includ-ing 2D experiments for all compounds 2–26D in as supplementary information (zip file) and have added copies of the 2D spectra for lead compounds 25, 25D, 26 and 26D in the ESI file.

17) All data need to be quantified. All bar charts need to be analyzed by correct statistics. This should be done using corrected t-tests (e.g. Bonferroni etc) post ANOVA test where more than two comparisons are being compared, and a sim-ple t tests were there are only 2 bars. All bars should show individual points. Please do not use two biological replicates performed in duplicate; the authors need at least N=3 independent biological replicates for each statement/claim made.

We did not find it relevant to generate additional negative data and have there-fore removed the attempts at evaluating tubulin deacetylation using Western blotting instead.

Reviewer: 2

1)To my opinion, most known SIRT2 inhibitor at the substrate site could compete with substrates(acetylated and myristoylated proteins) even they may be not de-tected in original papers, the authors should not have highlighted the feature like "no reported probe has been able to inhibit both of these SIRT2 activities".

We have rephrased this point to clarify that demyristoylation has not been investi-gated much in the past and mention that the fact that our inhibitors inhibit the enzymatic activity against Kmyr substrates merely highlights their high affinity, ena-bling competition against this low Km substrate.

2. Compared to a large number of previous SIRT2 papers, selectivity of the com-pounds havenot been extensively explored, such as other members in HDAC family (SIRT4-7 and HDAC1-11), it is not approprate to declare "selectivie SIRT2 inihitor" in the study.

Unfortunately, commercially available SIRT4 and SIRT7 are catalytically inactive, so we have profiled against SIRT1–3, 5, and 6 only. This is now clarified in the discussion. We have ample experience with the zinc-dependent HDAC enzymes and thio-carbonyl based mechanism-based SIRT inhibitors have never inhibited those enzymes in our assays. Therefore, we have chosen not to include these rather expensive experiments.

3. Due to the dual effects of their compounds on both deacetylation and de-myristoylation, it is very hard to distinguish different SIRT2 activities in breast can-cer cells using their compounds; In other words, these compounds have no ob-vious advantage over the previous ones in the investigation of SIRT2 functions as chemical probes.

We apologize that this has not been communicated clearly enough, but the point is that the compounds target the same binding site of SIRT2 and there-fore being able to inhibit both activities in vitro simply speaks to the inhibitor po-tency. Thus, the advantage is really just that these compounds are more potent against the target. We sincerely hope that the newly added data and discus-sion has helped clarify this.

21-Dec-2020

Dear Dr Olsen:

Manuscript ID: CB-ART-03-2020-000036.R1
TITLE: Mechanism-based inhibitors of SIRT2: structure–activity relationship, X-ray structures, target engagement, regulation of -tubulin acetylation and inhibition of breast cancer cell migration

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Reviewer 2

It is suitable for publication.