ChIP-MS reveals the local chromatin composition by label-free quantitative proteomics

  1. Wai Khang Yong
  2. Grishma Rane
  3. Nurkaiyisah Zaal Anuar
  4. Xiaoman Shao
  5. Chai Yeen Goh
  6. Vartika Khanchandani
  7. Vivian L. S. Kuan
  8. Maya Jeitany
  9. H. Phillip Koeffler
  10. Lih-Wen Deng
  11. Takaomi Sanda
  12. Dennis Kappei

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Abstract

Chromatin immunoprecipitation (ChIP) has been a cornerstone for epigenetic analyses over the last decades, but even coupled to sequencing approaches (ChIP-seq), it is ultimately limited to one protein at a time. In a complementary effort, we here combined ChIP with label-free quantitative (LFQ) mass spectrometry (ChIP-MS) to interrogate local chromatin compositions. We demonstrate the versatility of our approach at telomeres, with transcription factors, in tissue and by dCas9-driven locus-specific enrichment.

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    Reply to the reviewers

    Reply to the reviewers

    Manuscript number: RC-2023-01932

    Corresponding author(s): Dennis KAPPEI

    We would like to thank all reviewers for their recognition of our approach and the quality of our work as well as their constructive criticism.

    Reviewer #1

    Reviewer #1: The manuscript by Yong et. al. describes a comparison of various chromatin immunoprecipitation-mass spectrometric (ChIP-MS) methods targeting human telomeres in a variety of systems. By comparing antibody-based methods, crosslinkers, dCas9 and sgRNA targeted methods, KO cells and various controls, they provide a useful perspective for readers interested in similar experiments to explore protein-DNA interactions in a locus-specific manner.

    Response: We would like to thank the reviewer for the feedback and the appreciation of our work.

    Reviewer #1: While interesting, I found it somewhat difficult to extract a clear comparison of the methods from the text. It was also difficult to compare as data and findings from each method was discussed in its own context. Perhaps it is not in their interest to single out a specific method and it is indeed true that there are caveats with each of the methods.

    Response: Across our manuscript we have established one single workflow, for which we present some technical comparisons (e.g. using single or double cross-linking in Fig. 2a/b), technical recommendations such as the use of loss-of-function controls (e.g. Fig. 1c v. Fig. 2a and Extended Data Fig. 3g vs. 3i) and an application to unique loci using dCas9 (Fig. 3f). Based on the suggestions below, we believe that we will improve the clarity of communicating our approach.

    Reviewer #1: I think the manuscript would be of interest but I believe that there are remaining questions that need to be addressed before publication. In particular, I found it difficult to reconcile the discrepancy in protein IDs between most experiments vs. the WT/KO experiment in Fig 2. The authors make a big deal about the importance of the KO control but I think the fewer proteins identified there may be experiment-specific and not general to the KO system. I ask that this be investigated more carefully by the authors in their revisions.

    Response: We thank the reviewer for highlighting this point. We do not think that the ChIP-MS comparison between U2OS WT and ZBTB48 KO clones (Fig. 2a) has experiment-specific caveats. Instead the KO controls as well as the dTAGV-1 degron system for MYB ChIP-MS (Extended Data Fig. 3) reveal antibody-specific off-targets, which are indeed false-positives. Please see below for further details.

    Reviewer #1: Ln 57: What is "standard double cross-linking ChIP reactions" in this context? Is it the two different crosslinkers? The two proteins? The reciprocal IPs of one protein, and blotting for another? It's not clear here or from Extended Fig 1A. Upon further reading, it seems to pertain to the two crosslinkers - if so, the authors should briefly describe their workflow to help readers.

    Response: As the reviewer correctly concludes, we indeed intended to highlight the use of two separate crosslinkers (formaldehyde/FA and DSP). This combination is important as illustrated in the side-by-side comparison of Fig. 2a and Fig. 2d. Here, we performed ZBTB48 ChIP-MS in five U2OS WT and five U2OS ZBTB48 KO clones. While in both experiments the bait protein ZBTB48 was abundantly enriched in the samples that were fixed with formaldehyde we lose about half of the telomeric proteins that are known to directly bind to telomeric DNA independent of ZBTB48 and all of their interaction partners. For instance, while the FA+DSP reaction in Fig. 2a enriched all six shelterin complex members, the FA only reaction in Fig. 2d only enriches TERF2. These data suggest that the use of a second cross-linker helps to stabilise protein complexes on chromatin fragments. This is a critical message of our manuscript as ChIP-MS only truly lives up its name if we can enrich proteins that genuinely sit on the same chromatin fragment without protein interactions to the bait protein. We will expand on this in both the text and our schematics in Fig. 1a and 3a to make this clearer for the readers.

    Reviewer #1: Ln 95: It is surprising and quite unclear to me why it is that the WT ZBTB48 U2OS pulldown in Fig 1B shows 83 hits for the WT vs Ig control experiment but 27 hits for the WT vs KO condition in Fig 2A. The two WT experiments have the same design and reagents, shouldn't they be as close as technical replicates and provide very similar hits?

    The authors seem to make the claim that most of the 'extra' proteins in WT vs Ig are abundant and false positives, but if this is so, shouldn't they bind non-specifically to the beads and be enriched equally in Ig control and ZBTB48 WT IPs?

    Response: We again thank the reviewer for raising this point and the need to explain in more detail why we interpret the difference between 83 hits (anti-ZBTB48 antibody vs. IgG; Fig. 1c) and 27 hits (anti-ZBTB48 antibody used in both U2OS WT and ZBTB48 KO cells; Fig. 2a) primarily as false-positives. The KO controls in Fig. 2a allow to keep the ZBTB48 antibody as a constant variable while instead comparing the presence (WT) or absence (KO) of the bait protein. Hence, proteins that were enriched in the IgG comparison in Fig. 1c but that are lost in the WT vs. KO comparison in Fig. 2a are likely directly (or indirectly) recognised by the ZBTB48 antibody, akin to off-targets to this particular reagent. In a Western blot this would be equivalent to seeing multiple bands at different molecular weights with only the band belonging to the protein-of-interest disappearing in KO cells. To illustrate this we would like to refer to Extended Data Fig. 2, in which we have replotted the exact same data from Fig. 2a. However, in addition we have here highlighted proteins that were enriched in the IgG comparison in Fig. 1c. 46 proteins (in pink) are indeed quantified in the WT vs. KO comparison, but these proteins are found below the cut-offs (and most of them with very poor fold changes and p-values). In contrast to the other several hundred proteins common between both experiments that can be considered common background non-specifically bound to the protein G beads, these 46 proteins represent antibody-specific false-positives.

    The above consideration is not unique to ChIP-MS as illustrated by the Western blot example. We also do not claim novelty on the experimental logic, e.g. pre-CRISPR in 2006 Selbach and Mann demonstrated the usefulness of RNAi controls in immunoprecipitations (IPs) (PMID: 17072306). However, our data suggests that ChIP-MS is particularly vulnerable to this type of false-positives given that the approach requires (double-)cross-linking to sufficiently stabilise true-positives on the same chromatin fragment.

    To supplement the WT vs. ZBTB48 KO comparison, we had included a second experiment in the manuscript that illustrates the same point in even more dramatic fashion. First, KO controls are very clean in principle, but they themselves might come with caveats if e.g. the expression levels between WT and KO samples differ greatly. This might create a situation that the reviewer hinted to, i.e. differential expression of abundant proteins that would proportionally to their expression levels stick to the beads, resulting in “fold enrichments”. The resulting false positives could e.g. be controlled by matched expression proteomes. For ZBTB48 we have previously measured this (PMID: 28500257) and demonstrated that only a small number of genes are differentially expressed (~10) and hence we can interpret the WT vs. ZBTB48 KO comparison quite cleanly. However, for other classes of proteins such as transcription factors that regulate a large number of genes, E3 ligases etc. this might present a more serious concern. Therefore, we extended our loss-of-function comparison to such a transcription factor, MYB, by using the dTAGV-1 degron system. Importantly, the MYB antibody has been used in previous work for ChIP-seq applications (e.g. PMID: 25394790). Here, instead of 186 hits in the MYB vs. IgG comparison using the same MYB antibody in control-treated and dTAGV-1-treated cells (upon 30 min of treatment only) we only detect 9 hits. Again, similar to the WT vs. ZBTB48 KO comparison, 180 proteins are quantified in the DMSO vs. dTAGV-1 comparison, but these proteins fall below the cut-offs (Extended Data Fig. 3g vs. 3i). Again, we believe that this quite drastically illustrates how vulnerable ChIP-MS data is to large numbers of false-positives. This is not only a technical consideration as such datasets are frequently used in downstream pathway/gene set enrichment analyses etc. Such large false discovery rates would obviously lead to error-carry-forward and additional (unintended) misinterpretations. We will carefully expand our textual description across the manuscript to make these points much clearer. In addition, we will move the previous Extended Data Fig. 3 into the main manuscript to more clearly highlight this important point.

    Reviewer #1: Volcano plots in Figs 1, 2, and Suppl. Tables etc: Are the plotted points the mean of 5 replicates? Was each run normalized between the replicates in each group, for e.g. by median normalization of the log2 MS intensities? This does not appear to be the case upon inspection of the Suppl Tables. Given the variability in pulldown efficiency, gel digest and peptide recovery, this would certainly be necessary.

    Response: All volcano plots are indeed based on 4-5 biological replicates (most stringently in the WT vs. KO comparisons in Fig. 2 based on each 5 independent WT and ZBTB48 KO single cell clones). The x-axis of each volcano plot represents the ratio of mean MS1-based intensities between both experimental conditions in log2 scale. However, precisely to account for the variation that the reviewer highlighted we did not base our analysis on raw MS1 intensities but we used the MaxLFQ algorithm (PMID: 24942700) as part of the MaxQuant analysis software (PMID: 19029910) for genuine label-free quantitation across experimental conditions and replicates. In this context, we would also like to refer to a related comment by reviewer #2 based on which we will now addd concordance information for each replicate (heatmaps for Pearson correlations and PCA plots). We will improve this both in the text and methods section accordingly.

    Reviewer #1: Ln 125: The authors make the claim that the ChIP-MS experiments are inherently noisy, with examples from WT cells, dTAG system and IgG controls. This is likely the case, yet their experiments with WT vs KO cells do not identify as many proteins overall. I find this inconsistency somewhat unclear and does not seem to match the claim of ChIP-MS experiments and crosslinking adding to non-specificity. Can the authors add the total number of identified proteins in each volcano plot, for easier reference?

    Response: The number of identified proteins does not vary majorly between matched IgG and loss-of-function comparisons and for instance the single cross-linking (FA only) experiment in Fig. 2c has the largest number of quantified proteins among all ZBTB48 IPs. But we will of course add the requested information to all plots.

    Reviewer #1: I think the manuscript is interest as it provides important benchmarks for ChIP-proteomics experiments. I believe that there are remaining questions that need to be addressed before publication. In particular, I found it difficult to reconcile the discrepancy in protein IDs between most experiments vs. the WT/KO experiment in Fig 2. The authors make a big deal about the importance of the KO control but I think the fewer proteins identified there may be experiment-specific and not general to the KO system. I ask that this be investigated more carefully by the authors in their revisions.

    Response: We would like to thank the reviewer for recognising our work as a source for important benchmarks for ChIP-MS experiments. We hope that with a more detailed description and discussion the highlighted aspects will be more clearly communicated. We originally conceived our manuscript as a short report and now realised that some of the information became too condensed and might therefore benefit from more extensive explanations.

    Reviewer #2

    Reviewer #2: Summary: In this manuscript, Yong and colleagues have introduced a optimized technique for studying actors on chromatin in specific regions with a localized approach thanks to revisited ChIP-mass spectrometry (MS) with label-free quantitative (LFQ). The authors exhibited the utility of their approach by demonstrating its effectiveness at telomeres from cell culture (human U2OS cells) to tissue samples (liver, mouse embryonic stem cells). As a proof of concept, this technique was tested by the authors with proteins from complex shelterin specific to telomeres (TERF2 and ZBTB48), transcription factors (MYB), and through dCas9-driven locus-specific enrichment. Notably, the authors created a U2OS dCas9-GFP clone and then introduced sgRNAs to target either telomeric DNA (sgTELO) or an unrelated control (sgGAL4). The cells expressing sgTELO exhibited a significant localization of telomeres and an enriched amount of telomeric DNA in ChIP with dCas9. They also found the proteins previously identified as known to be enriched at telomeres (for example, the 6 shelterin members).

    Moreover, the authors illustrated the importance of double crosslinking (formaldehyde (FA) and dithiobis(succinimidyl propionate) (DSP) in ChIP-MS. Their data demonstrated also that ChIP-MS is inclined towards false-positives, possibly owing to its inherent cross-linking. However, by utilizing loss-of-function conditions specific to the bait, it can be tightly managed.

    • Can you show the concordance between biological replicates for each ChIP with LFQ? (heatmap of Pearson correlation and PCA plot). This will confirm the robustness of the use of LFQ.

    Response: We will add the requested concordance data for all volcano plots both in the form of heatmaps of Pearson correlation and PCA plots. Across our datasets, the replicates from the same experimental condition clearly cluster with each other and replicates have high concordance values of >0.9. As expected replicates for the target/bait samples have slightly higher concordance values compared to the negative controls (IgG or loss-of-function samples). We thank the reviewer for this suggestion as the new Extended Data panel will strengthen the illustration of our robust LFQ data.

    Reviewer #2: You say that your technique is " a simple, robust ChIP-MS workflow based on comparably low input quantities » (line 139). What would be really interesting for a technical paper would be: a schematic and a table illustrating the differences between your method and the previously published methods (amount of material, timeline,...) to really highlight the novelty in your optimized techniques.

    Response: We will add a comparison table with previous publications using ChIP-MS and for reference include some complementary approaches as requested by reviewer #3. On this note, we would like to stress that we are not “only” intending to use less material and to have an easy-to-adopt protocol. A cornerstone of our manuscript is to apply rigorous expectations to ChIP-MS experiments, in particular the ability to enrich proteins that independently bind to the same chromatin fragments as the bait protein (regardless of whether this is an endogenous protein or a exogenous, targeted bait such as dCas9). Otherwise, such experiments risk to be regular protein IPs under cross-linking conditions, which as illustrated by our loss-of-function comparisons are prone to yield particularly large fractions of false-positives.

    Reviewer #2: It would be interesting to perform the dCas9 ChIP experiment in telomeric regions with and without LFQ. Since the novelty lies in this parameter, at no time does the paper show that LFQ really allows to have as many or more proteins identified but in a simpler way and with less material. A table allowing to compare with and without LFQ would be interesting.

    Response: We do not fully understand what the suggestion “without LFQ” refers to exactly. We assume that this reviewer might suggest to use a different quantitative mass spectrometry approach other than LFQ, e.g. SILAC labelling, TMT labelling etc. Please note that we do not claim that LFQ quantification is per se superior to the various quantification methods that had been developed and widely used across the proteomics community especially before instrument setups and analysis pipelines were stable enough for label-free quantification (a name that is strongly owed to this historic order of development). However, a central goal of our workflow is to make robust and rigorous ChIP-MS accessible to the myriad of laboratories using ChIP-qPCR/-seq and that may not be extensively specialised in mass spectrometry. Both metabolic and isobaric labelling come not only at a higher cost but also present an experimental hurdle to non-specialists compared to performing biological replicates without any labelling, essentially the same way as for any ChIP-qPCR etc. experiment. We will further elaborate on these points in the manuscript to more clearly convey these notions.

    In general, with the right effort different quantitative methods should and will likely yield qualitatively similar results. However, comparisons between LFQ approaches (MaxLFQ, iBAQ,…) and labelling approaches (SILAC, TMT, iTRAQ) have already been better explored and verbalised elsewhere (e.g. PMID: 31814417 & 29535314). Therefore, we believe that this will add relatively little value to our manuscript.

    Reviewer #2: Put a sentence to explain "label free quantification". For a reader who is not at all familiar with this technique, it would be interesting to explain it and to quote the advantages compared to PLEX.

    Response: Thanks for highlighting this. In line with the point above as well as a similar comment by reviewer #1 we will improve this both in the main text and manuscript to clearly explain the terminology, the MaxLFQ algorithm (PMID: 24942700) used and to highlight the advantages compared to labelling approaches.

    Reviewer #2: what does the ranking on the right of each volcano plot represent (figure 1 b-e, figure 2a,d,e for example)? top of the most enriched proteins in the mentioned categories? Not very clear when we look on the volcano plot. it must be specified in the legend.

    Response: The numbering these panels is meant to link protein names to the data points on the volcano plots. The order of hits is ranked based on strongest fold enrichment, i.e. from right to center. We will clarify this in the figure legends.

    Reviewer #2: General assessment/Advance: The authors explain in their article that the ChIP exploiting the sequence specificity of nuclease-dead Cas9 (dCas9) to target specific chromatin loci by directly enriching for dCas9 was already published. Here, the novelty of this study lies in the use of LFQ mass spectrometry to optimize the technique and make it easier to handle. Some comparisons with previous papers or data generated by the lab will be interesting to really show the improvement and the advantage to use LFQ and therefore, to highlight better the novelty of the study.

    Response: We thank the reviewer for this assessment and as mentioned above we will include such a comparison table. dCas9 has been used previously in a ChIP-MS approach termed CAPTURE (PMID: 28841410). While this is clearly a landmark paper that illustrated the dCas9 enrichment concept across multiple omics applications (i.e. not limited to proteomics) in their application to telomeres, the authors enriched only 3 out of the 6 shelterin proteins with quite moderate fold enrichments (POT1: 0.99, TERF2: 2.13, TERF2IP: 1.06; in log2 scale). Based on this alone, POT1 and TERF2IP would not have qualified for our cut-off criteria. In addition, while the authors had performed three replicates, detection is only reported in 1-2 out of 3 replicates. While it is difficult to reconstruct statistical values based on the publicly accessible data, it is therefore unlikely that even these 3 proteins would have robustly be considered hits in our datasets. Similarly, using recombinant dCas9 with a sgRNA targeting telomeres that was in vitro reconstituted with sonicated chromatin extracts from 500 million HeLa cells (CLASP; PMID: 29507191) the authors identified only up to 3 shelterin subunits (TERF2, TERF2IP and TPP1/ACD) based on 1 unique peptide each only. For comparison, in our dCas9 ChIP-MS dataset all 6 shelterin subunits are identified with 9-19 unique peptides, contributing to our robust quantification. Even when considering cell line-specific differences (HeLa cells have shorter telomeres and hence provide less biochemical material for enrichment per cell), these comparisons illustrate that prior attempts struggled to robustly replicate even the most abundant telomeric complex members.

    Based on these findings, others had suggested that dCas9 “might exclude some relevant proteins from telomeres in vivo” (PMID: 32152500), implying that dCas9 ChIP-MS might inherently not be feasible including at repetitive regions such as telomeres. Therefore, we believe that our dCas9 ChIP-MS data is a proof-of-concept that the method has the genuine ability to robustly enrich key proteins at individual loci. In concordance with the comment above we will include a comparison table with previous papers and expand on these points in the discussion.

    Reviewer #2: By presenting this technical paper, the authors allow laboratories across different fields to use this technique to gain insights into protein enrichment in specific chromatin regions such as the promoter of a gene of interest or a particular open region in ATACseq in a easier way and with less materials. This paper holds value in enabling researchers to answer many pertinent questions in various fields.

    Response: We again thank the reviewer for this encouraging assessment and we do indeed hope that this manuscript makes a contribution to a much wider use of ChIP-MS approaches as a promising complement to existing genome-wide epigenetics analyses.

    Reviewer #3

    Reviewer #3: Strengths of the study:

    The study is well-structured and provides a robust workflow for the application of ChIP-MS to investigate chromatin composition in various contexts.

    The use of telomeres as a model locus for testing the developed ChIP-MS approach is appropriate due to its well-characterized protein composition.

    The comparison of WT vs KO lines for ZBTB48 is a rigorous way to control for false-positives, providing more confidence in the results.

    The direct comparison of double vs only FA-crosslinking provides valuable insights into the benefit of additional protein-protein crosslinking in ChIP-MS workflows.

    Response: We thank the reviewer for this assessment and we agree that the above are several of the key features of our manuscript.

    Reviewer #3: Areas for improvement: The novelty of the method is more than questionable as both ChIP-MS coupled to LFQ and dCas9 usage for locus-specific proteomics have been previously reported. The fact that the authors directly pulldown dCas9 instead of using a dCas9-fused biotin ligase and subsequent streptavidin pulldown is only a very minor change to previous methods (not even improvement). It would be more accurate for the authors to present their study as an optimization and rigorous validation of existing techniques rather than a novel approach.

    Response: While we appreciate where the reviewer is coming from, it occurs to us that most of the reviewer’s comments equate ChIP approaches with other complementary methods, in particular proximity labelling. The latter is indeed a powerful experimental strategy and in fact we are ourselves avid users. As highlighted to reviewer #1 as well, our manuscript was originally conceived as a shorter report and based on the feedback we will now expand our discussion to more broadly incorporate related approaches.

    However, we would like to stress that dCas9 ChIP-MS and dCas9-biotin ligase fusions are not the same thing and this is not a minor tweak to an existing protocol. While both approaches have converging aims – to identify proteins that associate with individual genomic loci – the experimental workflows differ fundamentally. Biotin ligases use a “tag and run” approach by promiscuously leaving a biotin tag on encountered proteins. Subsequently, cellular proteins are extracted and in fact proteins can even be denatured prior to enrichment with streptavidin beads. While this is an in vivo workflow that (depending on the biotin ligase used) may provide sensitivity advantages, it does not retain complex information. The latter is inherently part of ChIP workflows due to the use of cross-linkers. One obvious future application would be to maintain (= not to reverse as we have done here) the crosslink during the mass spectrometry sample preparation in order to read out cross-linked peptides to gain insights into interactions and structural features. We will now more clearly incorporate such notions into our discussion.

    In addition, we would like to stress that while this reviewer focuses primarily on the dCas9 aspect of our manuscript, we believe that our general ChIP-MS workflow including the combination with label-free quantitation is useful and important already by itself as e.g. recognised by both reviewers #1 and #2.

    Reviewer #3: The authors should more thoroughly discuss previous works using ChIP-MS and dCas9 for locus-specific proteomics. This would give readers a better understanding of how the current work builds on and improves these earlier methods. For a paper that aims on presenting an optimized ChIP-MS workflow it is crucial to showcase in which use cases it outperforms previously published methods.

    E.g., compare locus-specific dCas9 ChIP-MS to CasID (doi.org/10.1080/19491034.2016.1239000) and C-Berst (doi.org/10.1038/s41592- 018-0006-2); how does your method perform in comparison to these?

    Response: Again, while we will now incorporate more extensively comparisons with previous ChIP-MS publications (and the few prior manuscripts that included dCas9) as well as related techniques, we would like to stress that dCas9 ChIP-MS is not the same approach as CasID and C-BERST, which rely on dCas9 fusions to BirA* and APEX2, respectively. dCas9-APEX2 strategies were also published by two additional groups as CASPEX (back-to-back with the C-BERST manuscript; PMID: 29735997) and CAPLOCUS (PMID: 30805613). All of these methods target specific loci with dCas9 and promiscuously biotinylate proteins that are in proximity to the dCas9-biotin ligase fusion protein. As described above, while the application of the BioID principle (PMID: 22412018) to chromatin regions has converging aims with the dCas9 ChIP-MS part of our manuscript, they do not test the same. ChIP carries chromatin complexes through the entire workflow while the CasID approaches are independent of that. This is the same scenario if we were to compare IP-MS reactions (such as the ChIP-MS reactions presented here for endogenous proteins) and BioID-type experiments for proximity partners of the same bait proteins.

    Reviewer #3: Compare likewise the described protein interactomes to previously published interactomes.

    Response: We will add comparisons in form of Venn diagrams with previously published interactomes. However, we would like to stress that a key aspect of our manuscript is the smaller yet rigorous hit lists based on e.g. loss-of-function controls, higher stringencies and specificity. Simply comparing final interactomes remains reductionist relative to the importance of other variables such as experimental design, number of replicates, data analysis etc.

    Reviewer #3: The authors use sgGAL4 as a control for the telomeric targeting of dCas9. The IF results (Fig3b) show that sgGAL4 barely localizes to the nucleus with very faint signals. It would be helpful to use a control with homogenous nuclear localization of dCas9 to further strengthen the author's conclusions.

    Response: dCas9-EGFP in the presence of sgGAL4 localises diffusely to the nucleus as expected. We have here used a very widely used non-targeting sgRNA control that has been originally used for imaging purposes (PMID: 24360272) and has since been used in a variety of studies (e.g. PMID: 26082495, 32540968, 28427715) including a previous dCas9 ChIP-MS attempt (PMID: 28841410). In addition, to the diffuse nuclear, non-telomeric localisation we provide complementary validation of clean enrichment of telomeric DNA specifically in the sgTELO samples. Therefore, we do not see how other non-targeting sgRNAs would provide for better controls or improve our data.

    Reviewer #3: The extrapolation of results from the use of telomeres as a proof-of-concept to other loci is not a given considering the highly repetitive structure of telomeric DNA. The authors should either be more cautious about generalizing the results to other loci or demonstrate that their method can also capture locus-specific interactomes at non-repetitive regions.

    Response: We agree that the adoption of any locus-specific approach to single genomic loci is a steep additional hurdle and warrants rigorous data on well characterised loci with very clear positive controls. We will expand on these challenges in our discussion. However, we would like to stress that we did not make any such statement in our original manuscript apart from simply referring to our telomeric experiment as proof-of-concept evidence that locus-specific approaches are feasible by ChIP.

    Reviewer #3: What are concrete biological insights from this optimized ChIP-MS workflow that previous methods failed to show?

    Response: We explicitly used telomeres as an extensively studied locus with clear positive controls that at the same time allows us to evaluate likely false positives. As such the intention of the manuscript was not to yield concrete biological insights but to develop a new methodological workflow.

    As also highlighted in a response to reviewer #2, based on other prior attempts to enrich telomers in ChIP-like approaches with dCas9 (PMID: 28841410 & 29507191), it had been suggested that dCas9 “might exclude some relevant proteins from telomeres in vivo” (PMID: 32152500), implying that dCas9 ChIP-MS might inherently not be feasible including at repetitive regions such as telomeres. Therefore, recapitulating the set of well-described telomeric proteins was no trivial feat and our ChIP-MS workflow (both targeted and applied to individual proteins) represents a well-validated method to in the future systematically interrogate changes in chromatin composition. As one example at telomeres, this may include chromatin changes upon the induction of telomeric fusions or general DNA damage.

    Reviewer #3: For instance, the authors could compare their mouse and human TERF2 interactomes and discuss similarities and differences between both species.

    Response: We thank the reviewer for this suggestion, but the comparison between mouse and human TERF2 interactomes is not suitable across the datasets that we generated. U2OS is a human osteosarcoma cell line that relies on the Alternative Lengthening of Telomeres (ALT) pathway while our mouse data is based on embryonic stem cells (mESCs) and mouse liver tissue. Even the latter, in contrast to adult human tissue, expresses telomerase. We can certainly still pinpoint (as already done in our original manuscript) individual differences among known factors, e.g. the fact that proteins such as NR2C2 are more abundantly found at ALT telomeres (PMID: 19135898, 23229897, 25723166) vs. the detection of the CST complex as telomerase terminator (PMID: 22763445) in the mouse samples. However, the TERF2 datasets contain hundreds of proteins as “hits” above our cut-offs and a key message of our manuscript is that the majority of them are likely false positives. Here, differences are likely extending to expression differences between U2OS cells, mESCs and liver samples. So while appealing in theory, this cross data set comparison would remain rather superficial and error prone at this point. As a biology focused follow-up study, this would need to be rigorously conceived based on an appropriate choice of human and murine cell line models. In addition, this would likely require the generation of FKBP12-TERF2 knock-in fusion clones to allow for rapid depletion of TERF2 for a clean loss-of-function control since sustained loss of TERF2 leads to chromosomal fusions and eventually cell death in most cell types.

    Reviewer #3: The authors should also describe which interaction partners are novel and try to validate some of these using orthogonal methods.

    Response: We will now highlight more explicitly two proteins, POGZ and UBTF, that are most robustly and reproducibly enriched on telomeric chromatin across datasets, including the U2OS WT vs. ZBTB48 KO comparison (Fig. 2a). However, we would like to abstain from a molecular characterization at this point. As mentioned above, the discovery of novel telomeric proteins is not the focus of this manuscript, which is primarily dedicated to method development. In addition, these type of validations in methods papers are often limited to a few assays (e.g. can 1 or 2 proteins be enriched by ChIP? Do you see some localisation by IF? etc.). However, our research group has a history of publishing in-depth mechanistic papers on the characterisation of novel telomeric proteins (e.g. PMID: 23685356, 28500257, 20639181, doi.org/10.1101/2022.11.30.518500). Therefore, a genuine validation of such factors would require functional insights and clearly warrants independent follow-up work.

    Reviewer #3: Human Terf2 ChIP-MS (Fig1A) seems to be much more specific than the mouse counterpart (Fig1D) (32 TERF2 interactors out of 176 hits in human vs 12 TERF2 interactors out of 500 hits in mouse). Could the authors explain this notable difference?

    Response: As eluded to above, Fig. 1A and 1D cannot be directly compared, starting with the difference in complexity in the input material – cell line vs. tissue. For comparison, the Terf2 ChIP-MS data from mouse embryonic stem cells tallies up to 19 out of 169 hits, which is much closer to the U2OS results. Again, we deem the majority of hits from the TERF2 ChIP-MS data to be false-positives and the more complex input material from mouse livers likely accounts for the difference in these numbers.

    Reviewer #3: The authors used much higher cell numbers than previously published ChIP-MS experiments; while this is understandable for dCas9-based pulldowns, the cell number is expected to be down-scalable for the other IPs (TERF2, ZBTB48, MYB). Since this work primarily describes an optimized Chip-MS workflow, the authors should show that they can reasonably downscale to at least 15 Mio cells per replicate; one way of achieving this could be through digesting on the beads and not in-gel.

    Response: As we will illustrate in the comparison table that was also requested by reviewer 2, our approach does not use higher cell numbers than previous ChIP-MS approaches – quite the contrary. In addition, we would like to highlight that while we state 50 million cells in Fig. 1a, we only inject 50% of our samples for MS analysis to retain a back-up sample in case of technical issues with the instruments. In other words, our workflow is already effectively based on 25 million cells and thereby pretty close to the requested 15 million cells while simultaneously requiring substantially less reagents.

    Importantly, our examples are based on rather lowly expressed bait proteins such as ZBTB48 (not detected within DDA-based proteomes of ~10,000 proteins in U2OS cells). While the workflow can be applied across proteins, exact input numbers might vary depending on the bait protein, e.g. histones and its modifications would likely require less for the same absolute sample enrichment. For instance, PMID 25990348 and 25755260 performed ChIP-MS on common histone modifications but still used 300-800 million cells per replicate. Considering that we worked on substantially less abundant proteins, we here present a workflow with comparably low input samples.

    Reviewer #3: It is not clear from the text or figure what the authors are trying to show in Fig2c. They should either explain this further or take the figure out.

    Response: We are trying to illustrate the following: As in any IP reaction the bait protein is the most enriched protein with very high relative intensities, e.g. TERF2 in the TERF2 ChIP-MS data. Direct protein interaction partners – here the other shelterin members – follow at about 1 order of magnitude lower signal intensities. In contrast, proteins that are enriched via an interaction with the same DNA molecule (i.e. that do not physically interact with the bait protein) such as NR2C2, HMBOX1 and ZBTB48 further trail by at least 1 more order of magnitude. These are information that are not easily visualised within the volcano plots and mainly “buried” within the Supplementary Tables. However, these relative intensities displayed in Fig. 2c clearly illustrate the dynamic range challenge that ChIP-MS poses for proteins that independently bind to the same chromatin fragment. We have now modified our text to make this point more clear.

    *Reviewer #3: *Was there any benefit in using a Q Exactive HF vs timsTOF flex?

    Response: Yes, measuring the same samples (e.g. the 50% backup mentioned above) on both instruments enriches more telomeric proteins/shelterin proteins in e.g. the dCas9 ChIP-MS data set on the timsTOF fleX. However, given the difference in age of these instruments/technologies between a Q Exactive HF and a timsTOF fleX (in the context of these experiments the equivalent of a timsTOF Pro 2), this is not a fair comparison beyond concluding that a more recent instrument like the timsTOF fleX achieves better coverage and is more sensitive with otherwise comparable measurement parameters. As we did not have the opportunity to run matched samples on e.g. an Exploris 480, we would not want to make claims across vendors. As stated in the discussion we are expecting that even newer generation of mass spectrometers, such as the very recently released Orbitrap Astral or timsTOF Ultra would further improve the sensitivity and/or allow to reduce the amount of input material. Therefore, the main conclusion is that improvements in the mass spec generations improve proteomics data quality and our samples are no exception, i.e. this is not specifically pertinent to our approach.

    *Reviewer #3: *How did the authors analyze the PTM data? This is not described in the methods section. In addition, it would be important to validate the novel PTMs described for NR2C2.

    Response: We apologise for the oversight and we will add the description of PTMs as variable modifications during our MaxQuant search in the methods section. The originally deposited datasets already include this and we had simply missed this in our methods text.

    While we are not 100% sure to understand the request for validation correctly, we would like to point out that the PTMs on NR2C2 have been previously reported in several high-throughput datasets and for S19 in functional work on NR2C2 (PMID: 16887930). However, the relevance in our data set is as follows: While the PTMs on TERF2 as the bait protein could occur both on telomere-bound TERF2 as well as on nucleoplasmic TERF2, NR2C2 is only enriched in the TERF2 ChIP-MS reactions due to its direct interaction with telomeric DNA. The co-detection of its modifications therefore implies that at least some of the telomere-bound NR2C2 carries these modifications. We showcase this example as an additional angle of how such ChIP-MS datasets can be analysed.

    While the robust, MS2-based detection of these modified peptides in our data set and several other publicly available datasets provides strong evidence that these modifications are genuine, further functional validation would involve rather labour-intensive experiments and resource generation (e.g. phospho-site specific antibodies). We hope that the reviewer agrees with us that this would require an independent follow-up study and that this goes beyond the scope of our current manuscript.

    *Reviewer #3: *For this kind of methods paper one would expect to see the shearing results of the ChIP-MS experiments since variations in DNA shearing can impact the detection of false-positives in the ChIP-MS experiments

    Response: We will include agarose gel pictures of our sonicates, which we indeed routinely quality controlled prior to ChIP experiments as stated in our methods description.

    *Reviewer #3: *Overall, the current state of the manuscript neither provides direct evidence that the "optimized" ChIP-MS workflow is better in certain aspects/use cases than previously published methods nor does it provide novel biological insights. At the current state it even cannot be considered as a validation of previously published methods since it does not discuss them.

    Response: We politely disagree with this conclusion. Again, as mentioned above we are under the impression that this reviewer somehow equates our entire manuscript to a comparison with dCas9-biotin ligase fusions.

    Instead, we here provide a workflow for ChIP-MS that incorporates label-free quantification as the experimentally easiest, most intuitive quantification method for non-mass spectrometry experts. This offers a particularly low barrier to entry aimed at making ChIP-MS more widely accessible as a complement to commonly used ChIP-seq applications. Furthermore, we showcase that as a gold standard ChIP-MS – to truly live up to its name – should have the ability to enrich proteins independently binding to the same chromatin fragment. We demonstrated that double cross-linking is critical for these assays and in return illustrate how rigorous loss-of-function controls (both KOs and degron systems) can mitigate prevalent false-positives that are exacerbated due to the cross-linking. Finally, we applied this workflow to different types of endogenous proteins (transcription factors, telomeric proteins) in cell lines and tissue and extend our work to dCas9 ChIP-MS as a targeted method.

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    Referee #3

    Evidence, reproducibility and clarity

    Strengths of the study:

    • The study is well-structured and provides a robust workflow for the application of ChIP-MS to investigate chromatin composition in various contexts.
    • The use of telomeres as a model locus for testing the developed ChIP-MS approach is appropriate due to its well-characterized protein composition.
    • The comparison of WT vs KO lines for ZBTB48 is a rigorous way to control for false-positives, providing more confidence in the results.
    • The direct comparison of double vs only FA-crosslinking provides valuable insights into the benefit of additional protein-protein crosslinking in ChIP-MS workflows.

    Areas for improvement:

    • The novelty of the method is more than questionable as both ChIP-MS coupled to LFQ and dCas9 usage for locus-specific proteomics have been previously reported. The fact that the authors directly pulldown dCas9 instead of using a dCas9-fused biotin ligase and subsequent streptavidin pulldown is only a very minor change to previous methods (not even improvement). It would be more accurate for the authors to present their study as an optimization and rigorous validation of existing techniques rather than a novel approach.
    • The authors should more thoroughly discuss previous works using ChIP-MS and dCas9 for locus-specific proteomics. This would give readers a better understanding of how the current work builds on and improves these earlier methods. For a paper that aims on presenting an optimized ChIP-MS workflow it is crucial to showcase in which use cases it outperforms previously published methods.
      • E.g., compare locus-specific dCas9 ChIP-MS to CasID (doi.org/10.1080/19491034.2016.1239000) and C-Berst (doi.org/10.1038/s41592-018-0006-2); how does your method perform in comparison to these?
      • Compare likewise the described protein interactomes to previously published interactomes.
    • The authors use sgGAL4 as a control for the telomeric targeting of dCas9. The IF results (Fig3b) show that sgGAL4 barely localizes to the nucleus with very faint signals. It would be helpful to use a control with homogenous nuclear localization of dCas9 to further strengthen the author's conclusions.
    • The extrapolation of results from the use of telomeres as a proof-of-concept to other loci is not a given considering the highly repetitive structure of telomeric DNA. The authors should either be more cautious about generalizing the results to other loci or demonstrate that their method can also capture locus-specific interactomes at non-repetitive regions.
    • What are concrete biological insights from this optimized ChIP-MS workflow that previous methods failed to show?
      • For instance, the authors could compare their mouse and human TERF2 interactomes and discuss similarities and differences between both species.
      • The authors should also describe which interaction partners are novel and try to validate some of these using orthogonal methods.
    • Human Terf2 ChIP-MS (Fig1A) seems to be much more specific than the mouse counterpart (Fig1D) (32 TERF2 interactors out of 176 hits in human vs 12 TERF2 interactors out of 500 hits in mouse). Could the authors explain this notable difference?
    • The authors used much higher cell numbers than previously published ChIP-MS experiments; while this is understandable for dCas9-based pulldowns, the cell number is expected to be down-scalable for the other IPs (TERF2, ZBTB48, MYB). Since this work primarily describes an optimized Chip-MS workflow, the authors should show that they can reasonably downscale to at least 15 Mio cells per replicate; one way of achieving this could be through digesting on the beads and not in-gel.
    • It is not clear from the text or figure what the authors are trying to show in Fig2c. They should either explain this further or take the figure out.
    • Was there any benefit in using a Q Exactive HF vs timsTOF flex?
    • How did the authors analyze the PTM data? This is not described in the methods section. In addition, it would be important to validate the novel PTMs described for NR2C2.
    • For this kind of methods paper one would expect to see the shearing results of the ChIP-MS experiments since variations in DNA shearing can impact the detection of false-positives in the ChIP-MS experiments

    Significance

    Overall, the current state of the manuscript neither provides direct evidence that the "optimized" ChIP-MS workflow is better in certain aspects/use cases than previously published methods nor does it provide novel biological insights. At the current state it even cannot be considered as a validation of previously published methods since it does not discuss them.

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    Referee #2

    Evidence, reproducibility and clarity

    Summary: In this manuscript, Yong and colleagues have introduced a optimized technique for studying actors on chromatin in specific regions with a localized approach thanks to revisited ChIP-mass spectrometry (MS) with label-free quantitative (LFQ). The authors exhibited the utility of their approach by demonstrating its effectiveness at telomeres from cell culture (human U2OS cells) to tissue samples (liver, mouse embryonic stem cells). As a proof of concept, this technique was tested by the authors with proteins from complex shelterin specific to telomeres (TERF2 and ZBTB48), transcription factors (MYB), and through dCas9-driven locus-specific enrichment. Notably, the authors created a U2OS dCas9-GFP clone and then introduced sgRNAs to target either telomeric DNA (sgTELO) or an unrelated control (sgGAL4). The cells expressing sgTELO exhibited a significant localization of telomeres and an enriched amount of telomeric DNA in ChIP with dCas9. They also found the proteins previously identified as known to be enriched at telomeres (for example, the 6 shelterin members). Moreover, the authors illustrated the importance of double crosslinking (formaldehyde (FA) and dithiobis(succinimidyl propionate) (DSP) in ChIP-MS. Their data demonstrated also that ChIP-MS is inclined towards false-positives, possibly owing to its inherent cross-linking. However, by utilizing loss-of-function conditions specific to the bait, it can be tightly managed.

    Major comments:

    • Can you show the concordance between biological replicates for each ChIP with LFQ? (heatmap of Pearson correlation and PCA plot). This will confirm the robustness of the use of LFQ.
    • You say that your technique is " a simple, robust ChIP-MS workflow based on comparably low input quantities » (line 139). What would be really interesting for a technical paper would be: a schematic and a table illustrating the differences between your method and the previously published methods (amount of material, timeline,...) to really highlight the novelty in your optimized techniques.
    • It would be interesting to perform the dCas9 ChIP experiment in telomeric regions with and without LFQ. Since the novelty lies in this parameter, at no time does the paper show that LFQ really allows to have as many or more proteins identified but in a simpler way and with less material. A table allowing to compare with and without LFQ would be interesting.

    Minor comments:

    • Put a sentence to explain "label free quantification". For a reader who is not at all familiar with this technique, it would be interesting to explain it and to quote the advantages compared to PLEX.
    • what does the ranking on the right of each volcano plot represent (figure 1 b-e, figure 2a,d,e for example)? top of the most enriched proteins in the mentioned categories? Not very clear when we look on the volcano plot. it must be specified in the legend.

    Significance

    General assessment/Advance: The authors explain in their article that the ChIP exploiting the sequence specificity of nuclease-dead Cas9 (dCas9) to target specific chromatin loci by directly enriching for dCas9 was already published. Here, the novelty of this study lies in the use of LFQ mass spectrometry to optimize the technique and make it easier to handle. Some comparisons with previous papers or data generated by the lab will be interesting to really show the improvement and the advantage to use LFQ and therefore, to highlight better the novelty of the study.

    Audience: By presenting this technical paper, the authors allow laboratories across different fields to use this technique to gain insights into protein enrichment in specific chromatin regions such as the promoter of a gene of interest or a particular open region in ATACseq in a easier way and with less materials. This paper holds value in enabling researchers to answer many pertinent questions in various fields.

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    Referee #1

    Evidence, reproducibility and clarity

    The manuscript by Yong et. al. describes a comparison of various chromatin immunoprecipitation-mass spectrometric (ChIP-MS) methods targeting human telomeres in a variety of systems. By comparing antibody-based methods, crosslinkers, dCas9 and sgRNA targeted methods, KO cells and various controls, they provide a useful perspective for readers interested in similar experiments to explore protein-DNA interactions in a locus-specific manner.

    While interesting, I found it somewhat difficult to extract a clear comparison of the methods from the text. It was also difficult to compare as data and findings from each method was discussed in its own context. Perhaps it is not in their interest to single out a specific method and it is indeed true that there are caveats with each of the methods.

    I think the manuscript would be of interest but I believe that there are remaining questions that need to be addressed before publication. In particular, I found it difficult to reconcile the discrepancy in protein IDs between most experiments vs. the WT/KO experiment in Fig 2. The authors make a big deal about the importance of the KO control but I think the fewer proteins identified there may be experiment-specific and not general to the KO system. I ask that this be investigated more carefully by the authors in their revisions.

    Specific comments:

    Ln 57: What is "standard double cross-linking ChIP reactions" in this context? Is it the two different crosslinkers? The two proteins? The reciprocal IPs of one protein, and blotting for another? It's not clear here or from Extended Fig 1A. Upon further reading, it seems to pertain to the two crosslinkers - if so, the authors should briefly describe their workflow to help readers.

    Ln 95: It is surprising and quite unclear to me why it is that the WT ZBTB48 U2OS pulldown in Fig 1B shows 83 hits for the WT vs Ig control experiment but 27 hits for the WT vs KO condition in Fig 2A. The two WT experiments have the same design and reagents, shouldn't they be as close as technical replicates and provide very similar hits? The authors seem to make the claim that most of the 'extra' proteins in WT vs Ig are abundant and false positives, but if this is so, shouldn't they bind non-specifically to the beads and be enriched equally in Ig control and ZBTB48 WT IPs?

    Volcano plots in Figs 1, 2, and Suppl. Tables etc: Are the plotted points the mean of 5 replicates? Was each run normalized between the replicates in each group, for e.g. by median normalization of the log2 MS intensities? This does not appear to be the case upon inspection of the Suppl Tables. Given the variability in pulldown efficiency, gel digest and peptide recovery, this would certainly be necessary.

    Ln 125: The authors make the claim that the ChIP-MS experiments are inherently noisy, with examples from WT cells, dTAG system and IgG controls. This is likely the case, yet their experiments with WT vs KO cells do not identify as many proteins overall. I find this inconsistency somewhat unclear and does not seem to match the claim of ChIP-MS experiments and crosslinking adding to non-specificity. Can the authors add the total number of identified proteins in each volcano plot, for easier reference?

    Significance

    I think the manuscript is interest as it provides important benchmarks for ChIP-proteomics experiments. I believe that there are remaining questions that need to be addressed before publication. In particular, I found it difficult to reconcile the discrepancy in protein IDs between most experiments vs. the WT/KO experiment in Fig 2. The authors make a big deal about the importance of the KO control but I think the fewer proteins identified there may be experiment-specific and not general to the KO system. I ask that this be investigated more carefully by the authors in their revisions.

  5. Version published to 10.1101/2023.01.27.525999v1 on bioRxiv