System-wide identification and prioritization of enzyme substrates by thermal analysis

Despite the immense importance of enzyme–substrate reactions, there is a lack of general and unbiased tools for identifying and prioritizing substrate proteins that are modified by the enzyme on the structural level. Here we describe a high-throughput unbiased proteomics method called System-wide Identification and prioritization of Enzyme Substrates by Thermal Analysis (SIESTA). The approach assumes that the enzymatic post-translational modification of substrate proteins is likely to change their thermal stability. In our proof-of-concept studies, SIESTA successfully identifies several known and novel substrate candidates for selenoprotein thioredoxin reductase 1, protein kinase B (AKT1) and poly-(ADP-ribose) polymerase-10 systems. Wider application of SIESTA can enhance our understanding of the role of enzymes in homeostasis and disease, opening opportunities to investigate the effect of post-translational modifications on signal transduction and facilitate drug discovery.

'differential' approach. This is certainly an interesting adaptation of the TPP strategy that may address an existing need in screening for enzyme substrates, for instance when studying these enzymes as potential drug targets. Unfortunately, the presentation of the manuscript is far from optimal and a number of points listed below have to be addressed.
Major 1. The authors use a lysate (mild conditions) and add recombinant enzyme + substrate to study in vitro substrates of this enzyme. Although their approach undoubtedly generates interesting data, this strategy may be prone to false positive identifications. PTMs are mainly regulated spatially by bringing substrate and enzyme in close proximity (or not). Now, in a lysate this level of regulation is completely gone. I do not necessarily see a problem in using such a strategy, but I definitely miss a clear statement on this approach in order to make the reader aware of potential shortcomings. For instance, protein/substrate interactions may be specific to a certain organelle. I was first also wondering about secondary effects, which the authors exclude based on the fact that the lysate is 77x fold diluted compared to the cell, but that also means that a huge excess of enzyme is added to drive the reaction which can lead to unspecific reactions. The authors validate some of their findings using recombinant proteins, some of which being expressed in E coli, which may also be problematic due to different PTM patterns compared to human expression. The incubation of recombinant potential substrate with the enzyme and cosubstrate can again lead to artificial modifications that may not occur under physiological conditions and, unfortunately, I cannot see any kind of negative control for any of the three validation experiments, which is essential to ensure that not any protein will be modified in this setting.
2. In the same context, the authors used a method to "track phosphate release" which is not wellexplained, stating that they preferred this over p-proteomics, as the phosphate release represents all p-sites, whereas MS will only show individual sites (and I guess may miss some based on sequence inaccessibility). Indeed, MS would be an important additional validation to ensure that there is not too many different p-sites on the recombinant proteins under the given conditions, as the identification of too many sites would support the note of low specificity in such experiments. Also the sites should be compared with Phosphositeplus.
3. Line 164: The authors speculate that secondary reactions would occur when using NADPH alone, as well, but this is not completely obvious to me ---do the authors refer to the same reactions? 4. Line 330: the authors discuss how the cutoffs for considering a protein as shifted can be changed and how this impacts the list of potential substrates. Using a suitable cutoff is of course a common problem in quantitative proteomics, but the authors have to discuss this in the context of the robustness of the method ---how is the variation in melting temperature between replicates? Indeed, the cutoff being used in the end should be based on this variation in order to produce more robust data, than by applying kind of arbitrary cutoffs.
5. Line 365-372. The authors speculate on the effects of PTMs on protein stability and that this will be hard to generalize. The beginning and end of this 8-line section is somewhat redundant. The authors should mention the concept of PTM crosstalk and the PTM code. Indeed it would be really surprising if there was a general trend, as it seems that the entirety of PTMs dictate a proteins structure and function rather than individual PTMs, which may be one reason why the authors fail to verify some known substrates, they may simply be to heterogeneous within the sample which may even have functional/biological implications.
6. In general the writing has to be revised, as many statements throughout the manuscript are somewhat confusing or not ideal. a. For instance the section between lines 98 and 101 should be rephrased as it is hard to read.
b. Lines 148-149: What do the authors mean with top 100-400 SIESTA proteins, this is not very specific.
c. What exactly is meant with "variable influence on projection" VIP values? It would be helpful for the reader to get a short statement on that, as it may not be common knowledge.
d. Lines 178-183: Please rephrase this part, it is confusing. e. Line 232: Please summarize the assay to track phosphatase release in one sentence.
f. Line 252: Please mention that NAD is a cosubstrate, this is not obvious from the text.
g. Line 270 (and elsewhere): The term targeted MS is used in a wrong way. This typically refers to SRM/MRM and PRM assays, but what the authors used here is a triggered second MS/MS scan based on a decision-tree. Also the second MS/MS used EThcD ( the term is not used though) while the corresponding figure 4c reads "targeted ETD MS/MS", which is not correct in two ways. h. Line 288: "coverage with trypsin digestion was not complete" -it was also not complete for the previously mentioned examples, and a 100% sequence coverage might be extremely rare.
i. line 307: although the hot spot TPP was briefly mentioned in the introduction, it would be helpful to have a short statement how it actually works, particularly as the authors refer to this repeatedly, e.g. line 318 where the statement is hard to access without actually knowing how it works. j. line 402: I don't think a protein concentration can be distributed in aliquots.
k. line 343 (and was also somewhere else): please exchange 'protein molecules' which could refer to different proteins by 'copies of the same protein' or similar to clarify what is meant here. Minor 1. Line 55: the authors should add work from the Krogan lab (PMID 22817900) to their introduction.
2. Line 59: Please add some references to the statement on using modified substrates as readout.
3. From the main text (e.g. figure 2) it is not obvious that Cys-levels were indeed checked using iodo-TMT. This was confusing and only made sense when reading the method section later.
4. The terms substrate and co-substrate in connection to enzymes are widely used. The authors should rephrase their statement on page 4, lines 88-90, which sounds as if this was specific for the manuscript at hand. 5. Line 322: The authors mention that different PTMs induce different thermal shifts. Please summarize the average/median shifts observed in the 3 different examples given in this study.
6. Line 347: The authors mention sub-cellular fractionation as a way to increase the depth of SIESTA. This implies that the lysis must be so mild, that organelles are still intact. The authors should comment on strengths and limitations of this.
7. The supplemental tables should have more explanations on what is actually presented. It would be good to have a better connection between the "raw" data and the lists of substrates, maybe by combining them as different sheets into a single table rather than having so many individual tables per experiment.
Reviewer #3 (Remarks to the Author): "System-wide identification and prioritization of enzyme substrate by thermal analysis" submitted for publication in Nature Communication.
In this manuscript Amir Ata Saei et al. propose a workflow based on the mass spectrometry CEllular Thermal Shift Assay (MS-CETSA) to discover post-translational modifications produced by enzymes. Their hypothesis is that enzyme-induced post-translational modifications of substrate proteins may change the substrate thermal stability. This assumption is supported by multiple kinase-substrate pairs studied in vitro. Very recently this principle was generalized on a proteome-wide scale, as numerous shifts in protein melting temperatures were observed in response to site-specific phosphorylation events. Building on this concept, the authors aimed to detect post-translational modifications produced by, in principle, any enzymatic activity on its substrates with MS-CETSA. They found candidate protein substrates of three enzymes (TXNRD oxidoreductase, AKT1 kinase and poly-ADP ribose polymerase) by incubating human cell lysates with the enzymes purified in vitro and their co-factors. Their method named SIESTA is an interesting idea that could fill a gap in the field, as the (de)-stabilization events measured in MS-CETSA experiments are often difficult to interpret mechanistically. Although the screening of all potential substrates comes at the cost of producing recombinant enzymes, SIESTA would be very useful to reveal new enzyme-substrate associations. The method described in this manuscript could have an important impact in an area of biology where large scale studies are still scarce. However, I would suggest some conceptual and methodological clarifications of the content of this manuscript.

MAJOR POINTS:
CONCEPTUAL 1) The authors stated that the biological relevance of a protein modification correlates to the extent of the Tm shift that is observed in the thermal proteome profiling, and use this principle to prioritize substrates accordingly to their altered stability in their SIESTA assays. This idea follows the phosphorylation sites 'hotspots' theory proposed by Huang et al in a recent manuscript cited by the authors. However, two independent research groups questioned the conclusions of this work arguing that the experimental design was flawed. By reanalyzing the published data and performing independent experiments they showed that the extent of stability-altering phosphorylation is much less prevalent than what Huang et al proposed originally. At present, considering the open debate, I would consider the 'hotspot' theory at least controversial, therefore I would recommend to minimize references to the concepts originating from this paper and mitigate the statements regarding 'biological importance' and its association with 'larger Tm shifts'.
2) The criteria used for the definition of an enzyme substrate hit in SIESTA are not well described. What are the thresholds applied? How does the ranking of the hits work?
I understand that the specificity of the measured responses is calculated from the orthogonal partial least-square discriminant analysis (OPLS-DA) method referenced in the text. However, the authors should guide the readers summarizing what OPLS-DA does in a couple of sentences in the main text, as the audience will likely not know OPLS-DA.
The discrimination of the candidate hits seems to be based on the so called 'VIP value'. This concept is unclear for people who have not done an OPLS-DA analysis but it is the key discriminant for the discovery of the highest stabilized proteins. This should be made more accessible for a non-specialist audience. For instance, with the current format it is not trivial to understand how to interpret the data shown in the figures. For instance, what do the acronyms 'pq[1]' and poso[1] mean in the axes of the plot of figures 2d, S2c and S3c? What is a "negative reference context"? Since these three plots are showing the key results of the paper for the three enzymes under analysis, it is essential that sufficient elements are provided for the evaluation of this data.
3) There is a reference to the interaction databases GeneCards in line 147 of the main text and it is mentioned that GeneCard scores were also used to select putative substrates for validation. How the combination of the VIP and GeneCard scores were objectively used to prioritize or/and rank the candidate substrate? 4) A possible internal quality control for SIESTA could be to use the experiments with vehicle and cosubstrate only. The Nordlund group and others have essentially done the same experiments before in these publications (http://dx.plos.org/10.1371/journal.pone.0208273, http://www.nature.com/articles/s41467-019-09107-y). What is the overlap among the ATP, NADPH and NAD datasets? 5) It is meaningfully pointed out that MS-CETSA experiments with vehicle and co-substrate find cosubstrate binding proteins, as is has been extensively shown before. Can the authors comment whether they also observe significant Tm shifts between vehicle treated and enzyme treated samples? Is there any case in which substrate detection was achievable in absence of the cosubstrate by adding recombinant enzymes to the lysates, as they do? Was any interaction between substrate and enzyme in absence of a post-translational modification observed in this dataset?
6) The duplicates of the 'vehicle only' melting curves figures 2e, 3b, 4b and in the supplementary figures should also be reported for completeness. They would provide a better prospective of how the different components of the binding reaction affect the substrate stability. 7) Adding the enzyme of interest in large quantities to protein lysates could potentially lead to artifact post-translational modification of proteins that are not substrates of the enzymes in physiological conditions. This important issue is not discussed. Was this considered at all when designing the experiments?
8) The text is at times hard to follow due to excessive use of abbreviations (ex lines 166-183). This is also dangerous because it leads to misinterpretation. For instance, line 200, the authors write that "ACTB and MAP2K4 are new ATP binding proteins". I disagree. ACTB and MAPK4 are not novel ATP binding proteins. ACTB is cytoplasmic actin, and it is well known that ATP participates in the polymerization cycle of actin filaments. MAPK4 is a kinase component of the MAP kinase signal transduction pathway, and being a kinase binds ATP by definition. 9) Expressions like: "one could estimate the false positive rate to be not higher than 30%" (line 178) should be avoided if the sample size is 7. Similar issue at lines 300-301.
The discussion about "positive and -negative rates" should be toned down, if clear and objective criteria to define substrate hits are not provided, as discussed above (point 2 and 3).

EXPERIMENTAL:
10) The authors used separate multiplexed TMT10 samples to process and analyze experimental replicates in SIESTA experiments. Since this choice could introduce a certain experimental bias, can the authors show if this was taken into account for instance by examining the consistency between experimental duplicates?
Can the authors also explain why the AKT1 experiment require much more extensive peptide fractionation than the TXNRDq and PARP10 experiments (24 final fractions instead of 8)?
11) The validation of the monomer -dimer transition of GULP1 of supplementary figure 1d lacks a control. The total amount of GULP1 loaded in the two conditions should be shown in a SDS-PAGE gel run in denaturing conditions.
12) It would be interesting to comment about advantages/disadvantages of SIESTA versus REDOX proteomics for analyzing oxidoreductases substrates. The corresponding author's lab has a record of publications in the field of REDOX proteomics, so should be in a good position to briefly revise this in the discussion.

MINOR POINTS:
13) The scatter plot of Figure 2a does not show stabilization of known NADPH interacting proteins, rather consistency between replicates.
14) Some sentences are too vague. For instance, lines 135-138: "The analysis of specific ∆Tm shifts in the TXNRD1+NADPH treatment revealed that in the presence of NADPH, TXNRD1 destabilized both known and novel candidate substrate proteins (Supplementary Data 3). In general, the expected asymmetry in Tm shifts in favor of 138 destabilization was well pronounced (Fig. 2c)." Please report the exact number of destabilized and destabilized proteins in the main text to illustrate the content of figure 2c in the main text.
15) Lines 270-274: References to figure 4c and figure S3D appear to be missing. Comment 4. Line 218: "31% (123/396) of the proteins annotated in Uniprot as ATP binders were also verified in our experiment." The authors could also compare their results to previous TPP experiments with ATP, since even in lysate proteins that are stabilized are not necessarily binding ATP directly.
Response: Unfortunately, the processed data has not been made available in the previous studies. However, we present a comparison with UniProt, which has a compiled list of validated ATP, NADPH and NAD binding proteins. We have intentionally used 500 µM of ATP, at which concentration it mainly shows substrate activity, according to PMID: 30858367. Comment 5. In Fig 2-4, when showing melting curves for potential substrates, I think the controls should also be included.

Response:
We have now included the control melting curves for all the enzyme systems.

Andre Mateus
Reviewer #2 (Remarks to the Author): Saei et al. describe an adaptation of the Thermal Proteome Profiling (TPP) methodology, they term SIESTA and which can be used to particularly screen for enzyme substrates. As the authors point out, proteome-wide screening for substrates of a particular enzyme is not necessarily straightforward.
The authors demonstrate the utility and versatility of SIESTA on three model enzymes, namely the thioredoxin reductase TXNRD1, the protein kinase AKT1, and poly-ADP-ribosyltransferase PARP-10 and show that known as well as novel substrates can be identified for these enzymes using a 'differential' approach. This is certainly an interesting adaptation of the TPP strategy that may address an existing need in screening for enzyme substrates, for instance when studying these enzymes as potential drug targets. Unfortunately, the presentation of the manuscript is far from optimal and a number of points listed below have to be addressed.
Response: We thank the reviewer for the positive appraisal of our work and the valuable comments.

Comment 1. [A]
The authors use a lysate (mild conditions) and add recombinant enzyme + substrate to study in vitro substrates of this enzyme. Although their approach undoubtedly generates interesting data, this strategy may be prone to false positive identifications. PTMs are mainly regulated spatially by bringing substrate and enzyme in close proximity (or not). Now, in a lysate this level of regulation is completely gone. I do not necessarily see a problem in using such a strategy, but I definitely miss a clear statement on this approach in order to make the reader aware of potential shortcomings. For instance, protein/substrate interactions may be specific to a certain organelle. [B] I was first also wondering about secondary effects, which the authors exclude based on the fact that the lysate is 77x fold diluted compared to the cell, but that also means that a huge excess of enzyme is added to drive the reaction which can lead to unspecific reactions. [C] The authors validate some of their findings using recombinant proteins, some of which being expressed in E coli, which may also be problematic due to different PTM patterns compared to human expression. [D] The incubation of recombinant potential substrate with the enzyme and cosubstrate can again lead to artificial modifications that may not occur under physiological conditions and, unfortunately, I cannot see any kind of negative control for any of the three validation experiments, which is essential to ensure that not any protein will be modified in this setting.
Response: We thank the reviewer for these critical comments. These issues are now mentioned in the discussion. [A, B] It reads "Furthermore, using lysate might distort the spatial regulation of enzyme substrate interaction and yield substrates that are not active in the biological context. The excess of the enzyme may also lead to unspecific reactions". We tried to keep the conditions as physiological as possible. For example, in the case of ATP, we used 500 µM concentration where it mainly has cosubstrate activity (PMID: 30858367). The amount of added enzymes was not that high; we were actually limited by the amount of available recombinant enzymes. We now present the amount of added enzyme compared to the total amount of enzyme found in untreated cell lysate. Within the current study, for the TXNRD1, AKT1 and PARP10 systems, the ratio of added enzyme was ~10, ~20 and ~ 1.5 fold compared to untreated lysate, respectively. Given the dilution of lysate by ≈77 fold, these ratios are well within the physiological concentrations. The Supplementary Figure 7

was added to illustrate the results. [C] We added "Moreover, recombinant proteins expressed in E. coli may lack some important PTMs necessary for their activity in human cells". [D] We did not include an unrelated protein as a negative control during the incubation of recombinant potential substrate with the enzyme and cosubstrate (as it might create a bias). However, we
have done other validation experiments on the same day and under the same exact conditions. For example, 7 redox proteomics experiments were performed in parallel for validating TXNRD1 substrates, with only 5/7 validated. For PARP10, we could not validate Caspase 6, meaning that our validation experiments did rule out false positives. For AKT1, we now complement our study with phosphoproteomics validation experiments where we use AKT1 inhibitors in cells. The results are presented in Fig. 3. In Figure 1 we included validation as a crucial step in the SIESTA workflow. Comment 2. In the same context, the authors used a method to "track phosphate release" which is not wellexplained, stating that they preferred this over p-proteomics, as the phosphate release represents all p-sites, whereas MS will only show individual sites (and I guess may miss some based on sequence inaccessibility). Indeed, MS would be an important additional validation to ensure that there is not too many different p-sites on the recombinant proteins under the given conditions, as the identification of too many sites would support the note of low specificity in such experiments. Also the sites should be compared with Phosphositeplus.
Response: In response to the reviewer comment, we performed phosphoproteomics experiments with AKT1 inhibitors added to living cells and now provide in several cases the potential sites of modifications changing protein stability. The validated proteins included some of the genuine substrates of AKT1 such as BCL3, TRIP12 and MEF2D, confirming our findings. This statement was also added: "For example, in two direct microarray screenings of human cells, 165 and 51 AKT1 substrates have been found, respectively, with no overlap between them. In the PhosphoSitePlus database containing an accumulated list of 206 human protein substrates for AKT1, there are 4 and 7 overlapping proteins with the two mentioned studies, respectively, while the 72 SIESTA substrates obtained with a 0.5°C cutoff, similarly gave 4 overlaps." Comment 3. Line 164: The authors speculate that secondary reactions would occur when using NADPH alone, as well, but this is not completely obvious to me ---do the authors refer to the same reactions?
Response: For better clarity, we rephrased this sentence that now reads: "Furthermore, if secondary reactions were present, they would also occur in lysates treated with NADPH alone (as the basal levels of cellular TXNRD1 was also present there), and thus would be filtered away in our analysis". Comment 4. Line 330: the authors discuss how the cutoffs for considering a protein as shifted can be changed and how this impacts the list of potential substrates. Using a suitable cutoff is of course a common problem in quantitative proteomics, but the authors have to discuss this in the context of the robustness of the method --how is the variation in melting temperature between replicates? Indeed, the cutoff being used in the end should be based on this variation in order to produce more robust data, than by applying kind of arbitrary cutoffs.
Response: In choosing the final cutoff, we had also calculated the median variation between the replicates for different treatments for each enzyme system. This statement is now added: "The 1°C cutoff was chosen by analysis of the variation in Tm between replicates. In TXNRD1, AKT1 and PARP10 systems, the median Tm variation for different treatments was 0.50, 0.45 and 0.59 °C, respectively." Furthermore, as now detailed in the text, our final cutoffs allow for a minimum false discovery rate, and are thus robust.
Comment 5. Line 365-372. The authors speculate on the effects of PTMs on protein stability and that this will be hard to generalize. The beginning and end of this 8-line section is somewhat redundant. The authors should mention the concept of PTM crosstalk and the PTM code. Indeed it would be really surprising if there was a general trend, as it seems that the entirety of PTMs dictate a proteins structure and function rather than individual PTMs, which may be one reason why the authors fail to verify some known substrates, they may simply be to heterogeneous within the sample which may even have functional/biological implications. 7 Comment 7. The supplemental tables should have more explanations on what is actually presented. It would be good to have a better connection between the "raw" data and the lists of substrates, maybe by combining them as different sheets into a single table rather than having so many individual tables per experiment.

Response: We merged the tables in the revised version of the manuscript.
Reviewer #3 (Remarks to the Author): "System-wide identification and prioritization of enzyme substrate by thermal analysis" submitted for publication in Nature Communication.
In this manuscript Amir Ata Saei et al. propose a workflow based on the mass spectrometry CEllular Thermal Shift Assay (MS-CETSA) to discover post-translational modifications produced by enzymes. Their hypothesis is that enzyme-induced post-translational modifications of substrate proteins may change the substrate thermal stability. This assumption is supported by multiple kinase-substrate pairs studied in vitro. Very recently this principle was generalized on a proteome-wide scale, as numerous shifts in protein melting temperatures were observed in response to site-specific phosphorylation events. Building on this concept, the authors aimed to detect post-translational modifications produced by, in principle, any enzymatic activity on its substrates with MS-CETSA. They found candidate protein substrates of three enzymes (TXNRD oxidoreductase, AKT1 kinase and poly-ADP ribose polymerase) by incubating human cell lysates with the enzymes purified in vitro and their co-factors. Their method named SIESTA is an interesting idea that could fill a gap in the field, as the (de)stabilization events measured in MS-CETSA experiments are often difficult to interpret mechanistically. Although the screening of all potential substrates comes at the cost of producing recombinant enzymes, SIESTA would be very useful to reveal new enzyme-substrate associations. The method described in this manuscript could have an important impact in an area of biology where large scale studies are still scarce. However, I would suggest some conceptual and methodological clarifications of the content of this manuscript.

MAJOR POINTS:
CONCEPTUAL Comment 1. The authors stated that the biological relevance of a protein modification correlates to the extent of the Tm shift that is observed in the thermal proteome profiling, and use this principle to prioritize substrates accordingly to their altered stability in their SIESTA assays. This idea follows the phosphorylation sites 'hotspots' theory proposed by Huang et al in a recent manuscript cited by the authors. However, two independent research groups questioned the conclusions of this work arguing that the experimental design was flawed. By reanalyzing the published data and performing independent experiments they showed that the extent of stabilityaltering phosphorylation is much less prevalent than what Huang et al proposed originally. At present, considering the open debate, I would consider the 'hotspot' theory at least controversial, therefore I would recommend to minimize references to the concepts originating from this paper and mitigate the statements regarding 'biological importance' and its association with 'larger Tm shifts'.
Response: Thanks for the comment. We also noticed the debates over the "hotspot" theory after we submitted the manuscript and have mitigated our citations to this paper in this version. Thus we added to the discussions: "In should be noted that recent findings from two independent groups raised doubts in the extent of stability-altering phosphorylation postulated by Huang et al.". However, we still believe that substrates can be prioritized based on the size of the shift they exhibit in SIESTA.
Comment 2. The criteria used for the definition of an enzyme substrate hit in SIESTA are not well described. What are the thresholds applied? How does the ranking of the hits work?
Response: The selection criteria are now clearly stated in materials and methods: "For selection of putative substrates, the following criteria were used: 1) R2 > 0.7 between the measurement and the fitted curve, 2) the standard deviation between the replicates was <2.5°C, 3) p values between the Enzyme-Cosubstrate treatment against Enzyme and Cosubstrate treatments < 0.05 for one condition and <0.1 for the other; 4) the absolute mean ΔTm was larger than 1°C for both conditions (a similar approach was used for selection of cosubstrate binding proteins). We also now added: "The 1°C cutoff was chosen by analysis of the variation in Tm between replicates. In TXNRD1, AKT1 and PARP10 systems, the median Tm variation for different treatments was 0.50, 0.45 and 0.59 °C, respectively." We also added "The proteins passing the significance thresholds were ranked by absolute ΔTm or VIP values obtained from OPLS-DA analysis".
I understand that the specificity of the measured responses is calculated from the orthogonal partial least-square discriminant analysis (OPLS-DA) method referenced in the text. However, the authors should guide the readers summarizing what OPLS-DA does in a couple of sentences in the main text, as the audience will likely not know OPLS-DA.
The discrimination of the candidate hits seems to be based on the so called 'VIP value'. This concept is unclear for people who have not done an OPLS-DA analysis but it is the key discriminant for the discovery of the highest stabilized proteins. This should be made more accessible for a non-specialist audience. For instance, with the current format it is not trivial to understand how to interpret the data shown in the figures. For instance, what do the acronyms 'pq[1]' and poso[1] mean in the axes of the plot of figures 2d, S2c and S3c? What is a "negative reference context"? Since these three plots are showing the key results of the paper for the three enzymes under analysis, it is essential that sufficient elements are provided for the evaluation of this data.
Response: We have now described the OPLS-DA approach and the attributed parameters in the TXNRD1 results section (on the first use) and included the Supplementary Figure 1 to explain the approach and the way data must be interpreted. "pq[1]" and "poso[1]" were components 1 and 2 of the OPLS-DA model, and were changed accordingly in the new figures for clarity. The following paragraph was also added: "OPLS-DA is a multivariate supervised modeling tool for pinpointing the variables (here proteins) that have the largest discriminatory power between the two or more statistical groups (samples) 26. In the "loading plot" or "score scatter plot" for two-group comparison models, the predictive component is the x-axis, while y-axis is related to the orthogonal components that is irrelevant in this study ( Supplementary  Fig. 1a). In the loading plot ( Supplementary Fig. 1b), each protein is represented by a dot. In SIESTA, the protein Tm for single treatments is contrasted with those from the combination treatment. The large dots on either side of the plot are the reference points for the treatments. Therefore, proteins specifically stabilized by the modification will move close to the reference point of the combination treatment and the destabilized proteins will be further away on the opposite side. The proximity of a protein to the reference point on either side of the x-axis is a measure of the magnitude of the thermal stability change upon modification and its reproducibility among the replicates. Each protein can also be characterized by the variable influence on projection (VIP-value). The VIP-values quantify the impact each variable (i.e., protein) has on the OPLS-DA model, with a higher value corresponding to a greater contribution. Thus the proteins with the highest VIP values are suitable as candidates for validation. For more detailed explanation, see Umetrics documentation." Comment 3. There is a reference to the interaction databases GeneCards in line 147 of the main text and it is mentioned that GeneCard scores were also used to select putative substrates for validation. How the combination of the VIP and GeneCard scores were objectively used to prioritize or/and rank the candidate substrate?
Response: We deleted this analysis from the manuscript due to the collective comments from reviewers.

Comment 4.
A possible internal quality control for SIESTA could be to use the experiments with vehicle and co-substrate only. The Nordlund group and others have essentially done the same experiments before in these publications (http://dx.plos.org/10.1371/journal.pone.0208273, http://www.nature.com/articles/s41467-019-09107-y). What is the overlap among the ATP, NADPH and NAD datasets?
Response: This is a valuable suggestion, but unfortunately, the processed data has not been made available in these studies. However, we present a comparison with UniProt, which has a compiled list of validated ATP, NADPH and NAD binding proteins. Comment 5. It is meaningfully pointed out that MS-CETSA experiments with vehicle and co-substrate find cosubstrate binding proteins, as is has been extensively shown before. [A] Can the authors comment whether they also observe significant Tm shifts between vehicle treated and enzyme treated samples? [B] Is there any case in which substrate detection was achievable in absence of the co-substrate by adding recombinant enzymes to the lysates, as they do? [C] Was any interaction between substrate and enzyme in absence of a post-translational modification observed in this dataset?
Response: [A] Yes, we have. Please see our response to the Comment 3 Reviewer 1. [B] Yes, there is. For instance, four proteins were known to interact with AKT1 in the literature. We performed a pulldown experiment using PARP10 and analyzed the overlap in PARP10 interactors with SIESTA results. These results are now fully described in the paper and Fig. 5 and supplementary Fig. 6 are added. Some of the identified hits were indeed known substrates of the enzymes under study, for example MAZ for AKT1 system. [C] Yes, there might be a few known substrates such as MAZ that interact with an enzyme, but do not show the additional stability change upon modification, but we have noticed that the reverse is more likely; i.e. a protein identified as a substrate be known as an interacting protein. The latter is discussed for AKT1 system in the text. Comment 6. The duplicates of the 'vehicle only' melting curves figures 2e, 3b, 4b and in the supplementary figures should also be reported for completeness. They would provide a better prospective of how the different components of the binding reaction affect the substrate stability.

Response: We have now included the control melting curves for all the enzyme systems in all the figures.
Comment 7. Adding the enzyme of interest in large quantities to protein lysates could potentially lead to artifact post-translational modification of proteins that are not substrates of the enzymes in physiological conditions. This important issue is not discussed. Was this considered at all when designing the experiments?