Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In the manuscript entitled "BA.1 and BA.2 sub-lineages of Omicron variant have comparable replication kinetics and susceptibility to neutralization by antibodies" the authors assess the kinetics of growth of SARS-CoV-2 variants in Calu-3 cells and their effects on epithelial junction, and the interferon response. The authors also analyze the capacity of metal salts to block SARS CoV-2 replication in Calu-3 cells. Finally, the authors characterize the ability of vaccinated and/or COVID-19 patients to develop neutralizing antibodies to different variants using FRNT and specific binding assays (ELISA).

The paper largely confirms several previous reports on the replication capacity and interferon responses of the different variants. Although the title and abstract focus on the Omicron sub-lineages, the paper is mostly focused on comparing original CoV2, with Kappa, Delta and Omicron. Figures 1-5 compare the replication kinetics, interferon responses, and epithelial barrier disruption of Kappa, Delta and the original Omicron (B.1.1.529) to the original B6 variant. On a separate note, Figure 7 shows the ability of metal salts (especially iron, copper, and zinc) to block viral RNA-dependent RNA polymerase activity (RdRp) in vitro. The authors also show the effect on virus replication in Calu-3 cells (Delta and Omicron B.1.1.529 only). The data mainly focus on the variants, the Delta and the Omicron (BA.1.1.529 and not the BA.1 and BA.2 sub-lineages) except in Fig 6A, B, G.

Most importantly, a major limitation of the paper is that when human samples are analyzed, the authors assume that the patients have been infected with a specific variant according to the "peak" of infection, but sequencing is never performed. When neutralization and binding of antibodies are analyzed, the information on the patients is unclear - for example, were the patients exposed to Delta or Omicron or any of their sub-lineages? What was the vaccination status of SARS CoV-2 positive patients? And why non-tested individuals showing symptoms were included in the study (lines 302-304)?

The authors show that BA.1 and BA.2 have similar replication kinetics in Calu-3 cells and induce similar neutralizing antibodies in the patients tested. However, there is a large disconnection with the rest of the paper that is mostly focused on Kappa, Delta, and Omicron B.1.1.529. Also, no comparisons between these variants and BA.1 or BA.2 have been shown. Similarly, a large assumption in the paper is that the patients who tested positive for COVID-19 have had "natural Omicron infection" (lines 36-37; lines 307-311) when it could be any other variants or Omicron sub-lineages as well.

Significance

In light of the fact that most of the paper does not look at the subvariants BA.1 and BA.2 of Omicron- either the authors compare BA.1 and BA.2 more comprehensively with Omicron B.1.1.529 or rewrite the conclusions and claims of the current paper. Similar to the experiments comparing B6 with Kappa, Delta and Omicron, Omicron B.1.1.529 should be compared similarly to BA.1 and BA.2 in a separate figure. In any case, the novelty compared to other papers -also cited by the authors- remains limited.

In addition to the concerns mentioned above, there are more pressing variants circulating right now, such as BA.4 and BA.5. These variants are not referred in the paper. It might be beyond the scope of the paper, but including more analyses with BA.1, BA.2 (as the ones done with B.1.1.529) and adding some key data with BA.3, BA.4, BA.5 might substantially increase the relevance and importance of the paper.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary

The authors of this manuscript confirm data found by others by determining replication kinetics of the ancestral B.6 SARS-CoV-2 virus, Delta and Omicron BA.1 and BA.2 in Calu-3 cells. The authors quantify barrier integrity between variants and interferon induction to conclude that Delta is more cytopathic and induced less interferon than Omicron, possibly leading to its increased pathogenesis. In addition the authors identify CuCl2 and FeSO4 as potential antivirals.

Major comments

1. The author's argue that Omicron's slower replication on Calu-3 cells correlates with mild disease, however many publications show that Omicron replicates more efficiently/ rapidly in primary human airway cultures: Hui et al., (Nature, 2022) doi: https://doi.org/10.1038/s41586-022-04479-6 Peacock et al., (bioRxiv) doi: https://doi.org/10.1101/2021.12.31.474653 Lamers et al., (bioRxiv) doi: https://doi.org/10.1101/2022.01.19.476898
2. Can the authors explain why air-liquid grown Calu-3 cells appear to display similar viral titers for Omicron and Delta at 24 and 36 h.p.i (Figure 5B), however lower viral replication in Figure 3B? If the cells in Figure 3B are submerged, then the authors should identify why ALI grown Calu-3 cells are more susceptible to Omicron.
3. The authors suggest that Delta disrupts epithelial barrier integrity to a larger extent compared to B.6 and Omicron, however this may be due to fewer infected cells (despite equal viral titers, the nucleocapsid staining in Figure 2 and 5C suggests fewer infected cells). Have the authors imaged B.6 or Omicron at a later timepoint (or normalized virus input for equal infected cells) to determine barrier integrity when the amount of infected cells is equal? Alternatively, the authors should discuss this as a possible limitation of their study, especially since they argue this is a major reason why Delta has a growth advantage (lines 345 to 349).

Minor comments

Line 118: Implications of this sentence are too strong. The authors have not shown the causality of Ct values and transmission, therefore they should reword the sentence: "indicating a high viral burden in patients during this period resulting in increased transmission of the virus among the contacts" to "likely attributing to increased transmission..."

Line 289: The authors suggest that infection with the Omicron variant generated higher levels of antibodies to the Delta variant, however these individuals are already vaccinated and elicit cross-neutralizing antibodies against Delta even before their Omicron infection. Therefore the Delta response is boosted and the Omicron response is essentially a primary response since vaccination elicits almost no cross-protection in itself. Therefore the authors should compare primary Delta infected individuals to primary Omicron infected individuals to determine cross-protection levels. There appears to be no reference to Figure 6G, however this reference is most likely missing from line 306.

Line 359-362: The authors suggest that waning antibody titers increase susceptibility to new variants of concern, however their cohort already possessed very low antibody titers against Omicron a month after vaccination (Figure 7F) suggesting they could be equally susceptible to Omicron 1 and 6 months after vaccination.

Significance

Many of the conclusions based on replication and barrier integrity may not represent the situation in primary human tissues and does not explain the rapid spread of Omicron. In addition, interferon induction has already been described for these variants and this finding is not novel. The manuscripts most interesting and novel finding is the role of CuCl2 and FeSO4 as antivirals. It would be interesting to test these salts in primary human airway cultures.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a public response at this time.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

Synapses are the sites that mediate chemical signal transduction from axons to the dendrites of other neurons. At the axonal side of the synapse, called the presynapse, the arrival of action potentials triggers the fusion of synaptic vesicles filled with neurotransmitters with the plasma membrane. These neurotransmitters will then be detected by receptors located at the post-synapse at the dendrite.

In this manuscript, the authors set out to study the nanoarchitecture of the actin cytoskeleton at presynapses. They argue that this is challenging due to the much higher density of actin at the postsynapse. Therefore, they use an established approach in which polylysine-coated beads can induce structures at the axon that resemble presynapses. The authors first further characterize these presynapse-like structures by measuring the intensity of different presynaptic proteins. They report the presence bassoon, synapsin, synoptophysin, vamp2 at levels that are about half the level found at real synapses (Figure 1). 67% of induced hemisynapses are enriched for actin and the level of synaptic markers is higher in the presence of actin (Figure 2). Furthermore, actin-enriched hemisynapses also display more vesicle recycling than induced hemisynapses without actin enrichment.

Next, the intensity of synaptic markers is measured after treatment with drugs that stabilize or destabilize actin (Fig. 4), or drugs that inhibit the actin nucleators Arp2/3 or Formin (Fig. 5), which reveals some differences that could suggest the existence of different types of actin-based assemblies. The super-resolution microscopy in Figures 6 and 7 indeed nicely demonstrate that existence of actin as either dense clouds or clearly resolved fibers. Overall, this is an interesting manuscript that uses a simplified model system to study the organization of actin at presynapse-like structures. The super-resolution images provide exciting evidence for the existence of distinct actin structures in different parts of the presynapse, which provides many avenues for further research. Overall, the data appear solid and well-quantified. However, I do have a number of comments about the relevance of the model system and the presentation and interpretation of the data.

Major comments

Model system

1. The authors use the bead-triggered formation of synaptic-like presynaptic structures, because they argue that the post-synaptic actin would overwhelm any actin signal from the presynapses. This is demonstrated in Figure S1, where the authors use 20 div neurons and show that post-synaptic actin is brighter than presynaptic actin. However, this demonstration raises a number of questions. Why did they authors demonstrate this with 20 div neurons, whereas the rest of the manuscript focusses on neurons that are much younger (9 div)? These younger neurons typically have much less dendritic spines and the cultures are easier to navigate due to the lower density of axons. In their examples, the authors also mostly highlight excitatory synapses located at actin-rich dendritic spines and it is not directly evident that this is also true for inhibitory synapses that typically connect to the dendritic shaft. For example, the example shown in Figure 6B suggests that actin density is higher at the pre-synapse than at the post-synapse. According to the authors 20-40% of synapses in their culture are inhibitory synapses, so I would encourage the authors to try to get more data on real synapses, perhaps at 9 div. In my view, demonstration of the existence of the proposed actin structure at bonafide synapses would make the author's claims much stronger.
2. Related to the earlier point, the authors also acknowledge that alternative approaches, such as expression of lifeAct or GFP-actin would be possible to probe presynaptic actin organization at real synapses, but that these constructs can only be used at low levels in order to prevent artefacts. While in principle this is correct, recent successes in establishing knock-in approaches in differentiated neurons (i.e. HITI, ORANGE) have shown that endogenous actin can be tagged with small tags. Therefore knock-in of small epitope tags, such as HA or ALFA, would be a relatively straightforward way to selectively label presynaptic actin in real synapses. As mentioned above, demonstration of the existence of the proposed actin structure at bonafide synapses would make the author's claims much stronger.
3. The authors show that various key presynaptic proteins are about half as abundant on the synaptic-like presynaptic structure compared to real synapses. They argue that this might reflect the fact that the bead-induced synapse-like structures were analyzed two days after addition of the beads, whereas the real synapses might already have matured longer. This could easily be tested by altering the incubation time of beads and/or by analyzing how the average intensity of synapses develops over time. In addition, it is important to know how the intensity of actin compares between real synapses (NS) and induced synapses, because some images suggests that the enrichment at induced synapses is higher than at real synapses. This could suggest that the actin structures found at induced synapses might be specific to these induced hemisynapses. Data presentation
4. In Figure 1, the authors classify induced hemisynapses as either enriched for actin or not and then move on to analyze the intensity of bassoon, synapsin, synoptophysin, vamp2 for the two classes of hemisynapses. This promotes a very binary view of the structures they induce, whereas I assume that the intensity of actin will vary from structure to structure. Therefore, it would be more useful to plot the intensity of bassoon, synapsin, synoptophysin, vamp2 as a function of the intensity of actin. This could reveal that there are two clear regimes, but a least that would provide a justification for the classification into A+ and A-.
5. In Figure 3, vesicular cycling is compared between actin-enriched and non-enriched induced hemisynapses. It would be good to include a comparison with real synapses.

Biological interpretation

1. The title of the manuscript is "Distinct nano-structures support a multifunctional role of actin at presynapses". I agree that the identification of distinct structures supports the idea that they have distinct functions, but I do not think that the current manuscript really demonstrates that the distinct nano-structures support different roles. The result that actin stabilization and disassembly both affect vesicular cycling is taken as support for the idea that distinct actin structures coexist within the presynapse. In my view, it mostly demonstrates that a dynamic actin cytoskeleton is needed for vesicular cycling. Given the role of actin dynamics in endocytosis, this is not really a surprise. Likewise, the authors interpret the experiments in Fig. 5, where different actin nucleators are inhibited, as further evidence for distinct presynaptic structures. Although these might well exist, I am not sure if these experiment reveal that. Inhibition of Arp2/3 has very little effect, whereas inhibition of formins leads to more actin. Overall, these pharmacological experiments are very hard to interpret and do not directly promote the idea that different nucleators generate presynaptic actin networks with distinct functions.
2. The imaging in Figure 6 and 7 is very nice and does provide new insights into the organization of actin at induced hemi-synapses. While I certainly do understand the desire to name these structures, it is currently not clear what the structural difference would be between an actin mesh and an actin corral, and between an actin rail and an actin trail. Intuitively, one would think that meshes and corrals are generated by Arp2/3 based nucleation, while rails and trails are generate by formins. However, the analysis in Figure 7 does not really support this thinking. It could be that the quantification in Figure 7 a bit too coarse grained, because it mostly looks if structures are present or not. A more subtle analysis would analyze the intensities or sizes of meshes, rails and corrals and plot those in different conditions. Did the authors try something like that?
3. I do agree with the speculation that corrals could be used to confine vesicles (and perhaps to fish them out of the flow of axonal transport by actin-binding tethering factors), while the rails could facilitate local transport to the active zone. While the authors hypothesize that the actin mesh could inhibit vesicle release, another option is that it promotes endocytosis.

Questions related to the major comment - Are the key conclusions convincing?

The data is convincing, some of the data is over-interpreted. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

See my specific comments above. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

It would be fantastic if the authors can provide evidence for the structures they describe by the analysis of real synapses, for example by using knock-in approaches. Without additional data, the authors should reconsider some of their claims and interpretations and provide a more balanced discussion. - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

It is my understanding that the team has successfully achieved endogenous tagging of actin, but they might have good reasons for not using it for the current story. - Are the data and the methods presented in such a way that they can be reproduced?

Most procedures are well-documented. Some of the classification strategies are not extensively outlined. - Are the experiments adequately replicated and statistical analysis adequate?

Yes, the supplemental tables with replicate number etc is very useful.

Minor comments

1. In Figure 4, the effect of actin destabilization or stabilization on the level of synaptic proteins is examined. Here the axis labels are a bit confusing. The label "swin A-" suggests that there were also swin A+ synapses that were not analyzed. Similarly, the cuc A+ label suggest the exclusion of cuc A- synapses. Were there still A+ / A- synapses upon treatment of swin/cuc, respectively? If so, what happened to the relative abundance of A+/A- in these conditions?
2. The last paragraph of the result section should be part of the discussion section.

Referees cross-commenting

Overall, all three reviewer provide very similar feedback.

• a need for more careful interpretation of the induced structures and their relevance to real synapses.
• more characterization of the induced hemi-synapses in terms of localization (mostly on axons), actin density compared to real synapses, intensity of synaptic proteins at different days after induction, etc. A key concern is that the identified actin structures are specific for these induced structures.
• a need for more careful interpretation of the effects of the various drug treatments, as well as the formation and function of the various actin structures
• an encouragement to try to selectively label presynaptic actin using genetic approaches

Significance

This work provides exciting evidence for the existence of distinct actin structures in different parts of the presynapse, which provides many avenues for further research. While the structure and dynamics of the presynapse has been studied for decades, little is known about the organization of the actin cytoskeleton at these key sites of neuronal signal transmission.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Bingham et al., studied the composition and nano-structure of presynaptic elements induced by polylysine beads. By isolating the presynaptic element from the actin-rich postsynaptic compartment, this system makes it possible to study the organization of actin structures at high resolution. Using a combination of pharmacological interventions and super-resolution imaging, the authors distinguish three different types of actin structures at presynaptic elements.

Overall, this is a very careful study, using an innovative approach and state-of-the-art imaging techniques to visualize actin structures in presynaptic structures. The characterization of bead-induced presynaptic structures is elaborate and provides support that these structures can be used as a proxy of 'natural' synapses. The imaging, particularly the super-resolution imaging if of very high standard and convincing. The writing is overall clear and pleasant to read. Nevertheless, a number of concerns prevent strong conclusions from this study about how different actin structures support the structure and function of natural synapses.

• The characterization of bead-induced structures is quite extensive and also literature suggests that these structures are 'functional' in the sense that vesicle recycling çan be detected. Nevertheless, from the images it is not clear that these structures are always formed on axons. It seems the beads also induce presynaptic elements on dendrites, which would be highly artificial and prevent strong conclusions about axonal actin organization. Can the authors provide support that these "presynaptic structures" are preferentially formed on axons?
• The key observation of this paper is the existence of distinct actin structures highlighted in figures 6 and 7. These structures are indeed distinguishable by eye and could be of interest, but it remains unclear how these were defined. This is not described in the methods section, which makes it difficult to interpret the value of this observation. Were any (quantitative) criteria defined to outline these structures?
• The pharmacological intervention experiments in Figure 7D show modest, non-significant effects. More support that these structures are truly distinct and functional is required or conclusions about the existence of distinct actin assemblies should be reworded. Also see points below.
• A main concern is to what extent the contacts with the bead induce specific actin structures that are not representative of actin structures in natural synapses. The artificial, strong recruitment of heparan sulfate glycans could potentially induce the clustering of all kinds of adhesion complexes that promote actin polymerization/branching etc. and overrules the fine scale distribution of adhesion molecules and other presynaptic proteins in natural synapses. It thus remains unclear how specific and relevant these actin assemblies are for synapses. When comparing the natural synapse and induced synapse in Figure 6B and C it seems that particularly the 'actin rails' seem to originate from the bead contact (while similar structures cannot be seen in the natural synapse) and could thus reflect strong actin polymerization induced simply by the contact with the bead. More support that the observation of distinct actin structures is reminiscent of structures found at natural synapses is required. Experiments to show that such structures for instance do not form on non-neuronal cells could be considered. Experiments at natural synapses would of course be preferred. Have the authors considered genetic approaches to label actin in isolated cells? In that manner the presynaptic compartment could also easily be distinguished from the postsynaptic dendritic spines. A number of actin reporters (LifeAct, Ftractin, Utrophin, etc) are available, and albeit these have their limitations, if carefully used, these could be used to demonstrate similar structures. Alternatively, several CRISPR/Cas9 genome editing approaches are now available (HiUGE, ORANGE, TKIT, CRISPIE) that enable visualization of endogenous actin in isolated neurons.
• Since actin structures are responding to changes in neuronal activity, the (selective) modulation of these three types of actin assemblies to short- and/or long-term changes in neuronal activity would be of great interest and help support the functional relevance of this observation.

Minor:

• The term "presynapse" is not very commonly used in literature to indicate the presynaptic compartment. Particularly in this case it is a bit misleading as it suggests there is also a corresponding postsynaptic element. I would recommend to use 'presynaptic compartment' or alike.
• Reference to Glebov et al., Cell Reports 2017 is missing, even though this is a highly relevant study using SMLM to study active zone organization and the role of actin dynamics in regulating AZ composition.
• The labels in the images with the purple font on the black background (e.g., "Bassoon" in Figure 1A) are hardly visible
• The graphs should include an indication of statistical significance
• The term "concentration" is sometimes used when intensity measurements are done, but that is not appropriate in that case and should be rephrased to e.g. "relative amount" or alike.
• In abstract: "dependance" > "dependence
• Page 1: "Decade of research" > "Decades of research
• Page 4: "not at high" > "not as high"
• On page 10, "dependant" > "dependent'
• On page 14, "recruitment of neuroligin1" , the authors mean "neurexin1"?

Referees cross-commenting

I agree with the comments of the other reviewers, I see overall very similar comments. This is a strong and valuable study, but the main conclusions need more experimental support. Particularly, more quantitative characterisation of the induced synapses is needed and more support that the proposed classification of actin structures is representative of structures found in physiological synapses. For the last point, genetic labelling of actin structures in physiologic synapses is indeed strongly encouraged as also indicated by reviewer #3.

Significance

This study provides a detailed characterization of bead-induced presynaptic structures that allow the investigation of presynaptic actin structures at unprecedented resolution. The authors suggest that the presence of distinct actin structures at presynaptic specializations serve different functions to sustain synaptic transmission. These findings are of great interest for molecular and cellular neuroscientists interested in presynaptic mechanisms, but also more generally audience interested in super-resolution microscopy and/or the actin cytoskeleton.

I have experience in molecular and cellular neuroscience, synaptic transmission, and diverse microscopy techniques.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary

While phalloidin has been widely used to stain actin, its major limitation is that it labels both the presynaptic and postsynaptic actin structures, making it difficult to properly the comparatively less dense actin characterize within the presynapse. To overcome these difficulties, Bingham et al. made use of the well-established presynaptic induction model that utilises polylysine-coated beads to induce rapid formation of functionals synapses. They apply wide field fluorescence imaging showing that actin is enriched in these bead-induced synapses and apply actin nucleation and polymerisation inhibitors to characterise essential role of actin in maintaining the levels of other presynaptic components. Further, they apply nanoscale STORM and PAINT imaging to uncover distinct actin structures within the presynapse and how this is regulated by nucleation mechanisms.

Major Comments

• After the seeding beads in DIV 9-10 neurons the authors fix the neurons 48 hours later and indicate that they have functional synapses (S+) with protein presynaptic protein intensity less than natural synapses (Fig. 1). A key argument made by the authors is that the natural synapses are older than the bead-induced S+ ones. The expectation therefore then is that if the fix the neurons 72 or 96 hours after bead treatment, then the S+ should have a higher intensity than synapses after 48 hours. The authors should provide a time graded increase in synaptic component intensity to solidify their argument.
• Based on Fig.2 and Fig.3, the authors indicate actin enrichment in a subset of bead-induced synapses. The authors however did not provide a reasoning for why there is no actin enrichment in up to 30% of beads-induced synapses.
• Does shorter time treatment (for example 30 mins) of the induced synapses with swinholide and cucurbitacin E similarly reduce the intensity of presynaptic components?
• Using the CK666 actin nucleation inhibitor, the authors should provide supplemental information of no changes in intensity to other synaptic vesicle proteins (for example SV2) and to that of other presynaptic plasma membrane proteins such as Syntaxin-1 and Munc13.
• The authors should expand their STORM experiments to verify other data acquired with wide field fluorescence microscope such as actin enrichment (Fig.2) in bead-induced synapses

Minor Comments

• The authors should cite Rust et al., 2006 Nat. Methods as reference to first mention of STORM in paragraph 2 of the introduction.
• In Fig.S1, the authors indicate the dashed yellow lines as the presynapse. A better label, that stains the entire length of the presynapse might be needed to convincingly indicate presynaptic actin (dashed yellow lines) outside the bassoon labelling.
• The authors should provide quantification for the FM1-43 dye loading experiments in Fig.S2E and F.
• The author should provide representative images for the data from natural synapses in Fig.S5 for control, swinholide A, cucurbitacin E, CK666 and SMIFH2 treatments.

Referees cross-commenting

I agree with the comments from the other two reviewers that more work needs to be done to sufficiently justify the conclusions made.

Significance

• A key highlight that Bingham et al brings to the field is that they push the field forward from previous classical work done by the Zhuang lab (Xu et al., 2013 Science) where they showed novel data on the periodic organisation of actin cytoskeleton. This was done especially by provided a mechanism (bead induced synapse production) to narrow down on viewing presynaptic actin without overlapping 'noise' from postsynaptic region.
• Applying multiple nanoscale advanced imaging (STORM and PAINT) also helped solidify their data and provide hitherto unseen characterisation of actin structures.
• This manuscript will provide key insight to all scientists in the field of cell biology and cancer research that work on precisely characterising the cytoskeletal structure of the cell.
• Key words of field of expertise: Super-resolution microscopy, Neuroscience, Dementia, Synapse, Drosophila

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reply to the reviewers

1. General Statements

It is the common view of all three reviewers that we have not utilized adequate in vitro/biochemical evidence to support the idea that SATB1 protein undergoes liquid-liquid phase separation. We do agree with the reviewers that our manuscript lacks biochemical evidence to support such notion. Though we find it quite interesting and we would like to suggest for the first time in the field of chromatin organization and function, based upon the action of SATB1, that this protein does exist in at least two polypeptide isoforms (764 and 795 amino acids long) which display different phase separation propensity and therefore confer different actions in regulating the (patho)physiological properties of a murine T cell.

Every single research group that works on SATB1, considered so far only a single protein isoform, that is, the shorter isoform of 764 amino acids and no tools, such as isoform-specific antibodies have been developed to discriminate the two isoforms and thus being able to assign unique functions to each isoform. We do understand that such a report, suggesting the presence of two protein isoforms, with potentially quite diverse functions, would question (not necessarily by the authors of this manuscript, since no such comment is included in our manuscript) the conclusions drawn in the literature assigning all biochemical properties to a single, short isoform of SATB1. Moreover, all the genetically modified mice that have been analyzed so far (including our group), deleted both Satb1 isoforms. Our future research approaches should, from now on, consider unraveling the isoform-specific functions of SATB1 and their involvement in physiology and disease. This could also deem useful to explain the quite diverse, both positive and negative effects of SATB1 in transcription regulation. Another major objection of the reviewers was that we should provide cumulative supporting evidence for the existence of the long SATB1 isoform, or at least evaluate the specificity of our custom-made antibody.

Taking under consideration the aforementioned constructive criticism of the three reviewers we would like to perform (most of the suggested experiments have already been performed) additional experiments to support our claims in the manuscript. These experiments are described below as a point-by-point reply to each point raised by the reviewers.

In line with the aforementioned rationale, we propose the title of our manuscript to change into “Two SATB1 isoforms display different phase separation propensity”, if our manuscript is considered for publication.

1. Description of the planned revisions

**Reviewer #1**:

4) Lack of in vitro reconstitution experiments with purified long and short SATB1

**PLANNED EXPERIMENT #1**

We do realize this shortcoming of our work. We have to note that purifying recombinant SATB1 protein is quite a challenging task, yet we 1. cloned both Satb1 cDNAs for the long and short isoforms, 2. we successfully expressed both proteins in great quantity and quality and we are willing to perform these experiments if our work is considered for publication.

This proposed experiment has also been requested by Reviewers #2 and #3.

**Reviewer #2**:

1. Moreover, an important and direct experiment would be to clone the long isoform in a suitable vector and overexpress in the cell line (as done for the canonical isoform in Supp Fig 1a). This would unequivocally show the efficacy of the antibody and thus the following usage of the same for various assays.

**PLANNED EXPERIMENT #2**

This is a great suggestion. We have cloned the long and short Satb1 cDNAs in pEGFP-C1 vector. We will transfect these plasmids in NIH 3T3 fibroblasts and we will perform Western blot analysis, utilizing the antibody raised against the extra 31 amino acids long peptide present only in the long SATB1 isoform, for the following samples: 1. NIH-3T3 whole cell protein extracts, 2. protein extracts from NIH 3T3 fibroblasts transiently transfected with the pEGFP-C1 plasmid, 3. protein extracts from NIH 3T3 fibroblasts transiently transfected with the pEGFP-long_Satb1_ plasmid and 4. protein extracts from NIH 3T3 fibroblasts transiently transfected with the pEGFP-short_Satb1_ plasmid.

This experiment will consist another proof regarding the specificity of the antibody raised against the extra 31 amino acids long peptide present only in the long SATB1 isoform.

**Minor comments:**

1. On pg 6, related to Figure 1, the authors mention 'It should also be noted that when investigating the SATB1 protein levels, we have to bear in mind that the antibodies targeting the N-terminus of SATB1 protein cannot discriminate between the short and long isoforms'. The authors reason that their sizes are too close. It is indeed possible, and widely studied in biochemistry to assess various factors on protein migration (such as PTMs). The authors should validate this aspect (as it is important as per their premise) and perform separation based on charge as well and also use a commercial antibody to validate the same.

(Experiments already performed)

We have adapted the text so that it does not imply that the two isoforms cannot be separated by size. This part in lines 102-107 then reads: “It should also be noted that when investigating the SATB1 protein levels, we have to bear in mind that the antibodies targeting the N-terminus of SATB1 protein cannot discriminate between the short and long isoforms, thus we can only compare the amount of the long SATB1 isoform to the total SATB1 protein levels in vivo conditions. To overcome this limitation and to specifically validate the presence of the long SATB1 protein isoform in primary murine T cells, we designed a serial immunodepletion-based experiment (Fig. 1e, Supplementary Fig. 1a).”

Moreover, in the revised version of the manuscript we now provide a number of additional proofs supporting the presence of the long isoform and also the specificity of the long isoform-specific antibody. As evident in the text cited above, in the revised Fig. 1e,f and revised Supplementary Fig. 1a,b; we present two immunodepletion experiments which should alone address the Reviewer’s concerns. Moreover, we added Supplementary Fig. 1c; demonstrating that the long isoform-specific antibody does not detect any protein in cells with conditionally depleted SATB1 (Satb1_fl/fl_Cd4-Cre+), supporting its specificity. The custom-made and publicly available antibodies targeting all SATB1 isoforms were also verified in Supplementary Fig. 1d. Moreover, the long isoform and all isoform antibodies display similar localization in the nucleus (Supplementary Fig. 1e; their co-localization based on super-resolution microscopy is also quantified in Supplementary Fig. 5a).

In our accompanying revised manuscript Zelenka et al., 2022 (https://doi.org/10.1101/2021.07.09.451769), we will provide yet another piece of evidence, consisting of bacterially expressed short and long SATB1 protein isoforms detected by western blot using either the long isoform-specific or the non-selective all SATB1 isoform antibodies.

**PLANNED EXPERIMENT #3**

Although we think that in the revised version of the manuscript, we have provided enough proof about the existence of the long isoform in primary murine thymocytes we would like to try the following approach as suggested by this Reviewer.

The pI of the two SATB1 isoform is quite similar. The pI of the short SATB1 isoform is 6.09 and for the long SATB1 isoform is 6.18. We will perform 2D PAGE coupled to Western blotting utilizing the antibodies detecting the long and all SATB1 isoforms. Given the fact that both isoforms are post-translationally modified to a various degree, it will be extremely difficult to discriminate between the long and short unmodified versus the long and short post-translationally modified proteins especially in the absence of a specific antibody only for the short isoform.

**Reviewer #3**

1. Hexanediol is another assay frequently used in phase-separation studies. However, hexanediol has many deleterious effects on the cell, even at a fraction of the concentration normally used in phase-separation studies. Authors should show controls of cell viability, control proteins that do not phase-separate, etc. See https://www.jbc.org/article/S0021-9258(21)00027-2/fulltext.

Secondly, hexanediol treatment should cause phase-separated protein aggregates to disperse. It is difficult to determine from the images whether or not the aggregates actually disperse or there is just less protein. In any case, small aggregates remain even after treatment, and this appears different from most other hexanediol experiments reported in the literature where the signals become more dispersed and uniform. This is likely because the samples are fixed.

One of the main features of using hexanediol in phase-separation is to show that upon washout, LLPS aggregates can reform. Because the cells are fixed, the critical aspect of this assay is not performed. A washout and LLPS recovery would control for cell viability issues described above and would provide the opportunity to show that total SATB1 protein levels did not change, but its distribution did, which is the essence of this assay in the context of LLPS. This review from the Tjian group is very informative and may be a good resource:

http://genesdev.cshlp.org/content/33/23-24/1619

In line with our reply to point #1 of this Reviewer (page 26 of this document), we should again emphasize that we utilized the hexanediol treatment in primary murine developing T cells as this is the only way to investigate the properties of SATB1 speckles under physiological conditions. This also explains why some small insoluble structure remains after the hexanediol treatment. Note that under physiological conditions, there is a contribution of several protein variants (such as differential PTMs) out of which some will tend to form more stable structures while others could undergo LLPS. It is not clear how the washout experiment could be applied in the primary cell conditions that include cell fixation as the heterogeneity and big variation among cells would make such data analysis highly unreliable.

**PLANNED EXPERIMENT #1**

As we answered to point #4 of Reviewer 1 (page 2), we propose the following experiment. Although the purification of recombinant SATB1 protein is quite a challenging task, yet we 1. cloned both Satb1 cDNAs for the long and short isoforms, 2. we successfully expressed both proteins in great quantity and quality and we are willing to perform in vitro reconstitution experiments if our work is considered for publication.

1. The major difference between the long and short isoform of SATB1 is the 31aa segment within the IDR. However the authors find that neither the long or short isoform SATB1 forms LLPS aggregates, and the IDR alone forms aggregates in the cytoplasm (Fig5) but they do not respond to Cry2 light activation. When forced to localize to the nucleus, it does not form aggregates as well (Fig6). The short isoform also did not form any aggregates. These results seem to argue against any isoform specific phase-separation. This experiment seems critical for the story, yet it does not support their overall conclusions. The authors might consider using a different cell line or perhaps do an in vitro assay using purified protein.

I am not certain what to make of the cytoplasmic aggregation, which appears to not form upon localization to the nucleus. Because of this, it is difficult to place weight on the significance of the S635A mutation and the role that a phosphorylation of SATB1 contributes to phase-separation, let alone function There are many additional points of concern, but the ones listed above are perhaps the most significant in terms of the overall conclusions of the paper.

In Fig. 5c we show that the full length long SATB1 isoform often aggregates unlike the short isoform. These data are accompanied with the results for the IDR region, where the situation is even more obvious (Fig. 5f,g). However, in the latter, we have to bear in mind the absence of the multivalent N-terminal part of the protein which seems to be essential for the overall phase behavior of the protein as indicated in Fig. 4b,c.

**PLANNED EXPERIMENT #1**

To further support LLPS of SATB1, we are considering performing the following in vitro experiment, as we answered to point #4 of Reviewer 1 (page 2). Although the purification of recombinant SATB1 protein is quite a challenging task, yet we 1. cloned both Satb1 cDNAs for the long and short isoforms, 2. we successfully expressed both proteins in great quantity and quality and we are willing to perform in vitro reconstitution experiments if our work is considered for publication.

1. Description of the revisions that have already been incorporated in the transferred manuscript

**Reviewer #1 (Evidence, reproducibility and clarity)**:

This paper looks at an important nuclear matrix protein SATB1, which is a well known global chromatin organizer and help chromatin loop attach to the nuclear matrix. The paper starts with identification of novel short and long form of SATB1. Both the isoform consist of a prion like low complexity domains, but the long isoform additionally contain an extra EPF domain next the Prion like low complexity domain. The paper reports that in murine cells the long isoform is 3-4 fold more abundant than the short isoform. By using STED microscopy they show SATB1 foci lie next to transcription sites in the nucleus. They conclude by looking at the spherical shape of the SATB1 foci and the susceptibility of SATB1 staining after 1,6 hexanediol treatment that SATB1 forms the small foci in the nucleus due to LLPS. The authors also use RAMAN spectroscopy to conclude a change in nuclear chemical space in absence of SATB1 but without much explanation about which chemical bond or nuclear sub structure change correspond to the change in principal component analysis from Raman spectroscopy. The authors use the light inducible aggregation cry2 tag with the PrD domain of SATB1 and compare it with the Cry2-FUS-LC domain to conclude that the SATB1 LC domain can undergo LLPS. The authors hint at involvement of RNA and also DNA in the LLPS of the SATB1 but without going into any detail. Reviewer: The paper reports that in murine cells the long isoform is 3-4 fold more abundant than the short isoform.

Actually, in page 5 (lines 94-96) of the manuscript we write: “We confirmed that in murine thymocytes the steady state mRNA levels of the short Satb1 transcripts were about 3-5 fold more abundant compared to the steady state mRNA levels of the long Satb1 transcripts (Fig. 1d).” Although the steady state mRNA levels of the long isoform are less abundant compared to the shorter isoforms, the long isoform protein levels are almost comparable to the short isoform as deduced based on immunofluorescence experiments. Moreover, Using our two immunodepletion experiments we quantified the difference, estimating the long isoform being 1.5× to 2.62× less abundant than the short isoform (Fig. 1f and Supplementary Fig. 1b; compare lanes 2 & 3 at the lower panel). • Regarding the RAMAN spectroscopy experiments please see Minor Comment #1 of this Reviewer (page 10).

The key conclusions of the paper are- A) SATB1 undergoes LLPS. But this conclusion is drawn after correlative experiments as detailed below-

This conclusion is indeed made based on correlative experiments only for the primary murine T cells, which do not allow for any targeted experiments. However, the use of in vitro cell lines allowed us to validate these findings using the optogenetic approaches, utilizing additional experimentation.

1) observation of spherical punctae by STED-which could also seem spherical due to their small size. The resolution limit achieved by the STED microscopy used in this paper is not determined or mentioned clearly.

In the revised version of the manuscript, we have specified the resolution of our systems, for STED in Lines 745-746: ”This system enables super-resolution imaging with 35 nm lateral and 130 nm axial resolution.” and for SIM in Lines 759-761: “Images were acquired over the majority of the cell volume in z-dimension with 15 raw images per plane (five phases, three angles), providing ~120-135 nm lateral and ~340-350 nm axial resolution for 488/568 nm lasers, respectively.” The size of the observed speckles is thus above the resolution limit with sizes ranging between 40-80 nm.

The resolution of our systems is routinely verified by the following methods: The resolution of our OMX (SIM-3D) system was tested using ARGO-SIM slide containing a pattern of 36 µm long lines with gradually increasing spacing ranging from (left to right) 0 to 390 nm, with a step of 30 nm (Fig. 1 below). Our SIM system was able to clearly resolve two lines separated by 120 nm.

2) No live cell FRAP experiment with fluorescent SATB1 long or short isoform to show that these foci are liquid like

We did perform FRAP experiments for the SATB1 N-terminus optogenetic construct as demonstrated in Fig. 4f. We did not perform FRAP in the primary murine T cells as this is not technically feasible without creating a new mouse line with fluorescently labeled protein. In the revised version of the manuscript, we additionally performed FRAP experiments for the full length short and long isoform of SATB1 labeled with EGFP and transfected into the NIH-3T3 cell line (Supplementary Figure 6f).

5) LLPS is strongly coupled to the cellular concentration of the proteins. Authors should quantify the cellular concentration of the long and short isoform in the cells.

We did consider protein concentration in our analyses of optogenetic constructs in Fig. 4b,d,e and Supplementary Fig. 6a,b,c. Quantifying the physiological cellular concentration of short and long SATB1 protein isoforms in primary T cells is impossible due to the inherent inability to discriminate between the isoforms by two antibodies, in the absence of Satb1 isoform-specific knockout mice.

However, an approximation of the cellular concentration can be obtained from our immunodepletion experiments. On top of the original immunodepletion experiment that we now present in Supplementary Fig. 1a,b; in the revised version of the manuscript we have repeated the experiment in Fig. 1e,f. Comparison of the two bands for the long and short SATB1 isoforms in the lower panel of the western blot figures suggest that the long SATB1 isoform protein levels are 1.5× to 2.62× less abundant than the short isoform, according to the original and new immunodepletion experiment, respectively. This is now also included in the main text in Lines 110-116: “This experiment can also be used for approximation of the cellular protein levels of SATB1 isoforms in primary murine thymocytes. Comparison of the two bands for long (lane 2) and short SATB1 (lane 3) isoform in the lower panel of Fig. 1f and Supplementary Fig. 1b, suggests that the long SATB1 isoform protein levels may be about 1.5× to 2.62× less abundant than the short isoform, according to the two replicates of our immunodepletion experiment, respectively.”

Major conclusion B)- SATB1 regulates transcription and splicing.

This was also shown previously and in this paper they show the close proximity of the transcription site and SATB1 foci by microscopy. Hexanediol treatment which lead to loss of colocalization between FU foci and SATB1 is also taken as an evidence in regulation of transcription is not right as the transcription foci itself can be dissolved using 1,6 Hexanediol. Although the rate of transcription is not measured quantitatively.

As mentioned in comment #3 (page 29) of this Reviewer, unfortunately there is no better tool to investigate these questions in primary cells than using microscopy approaches in conjunction with hexanediol treatment. However, we should also note that there is an accompanying manuscript from our group that is currently being under revision in another journal (preprint available: Zelenka et al., 2021; https://doi.org/10.1101/2021.07.09.451769). In the preprint manuscript, we showed that: 1. the long SATB1 isoform binding sites have increased chromatin accessibility than what expected by chance (Fig. 3b), 2. there is a drop in chromatin accessibility at SATB1 binding sites in Satb1 cKO mouse (Fig. 3c) and 3. this drop in chromatin accessibility is especially evident at the transcription start sites of genes (Supplementary Fig. 1i)

We believe that, together these data suggest a direct involvement of SATB1 in transcription regulation. Also note the vast transcriptional deregulation that occurs in Satb1 cKO T cells, affecting the expression of nearly 2000 genes (Fig. 2f, this revised manuscript). That is why we believe that the co-localization analysis, using super-resolution microscopy, presented in Fig. 2c and quantified in Fig. 3g, represents a nice additional support to our claims. Moreover, in the revised version of the manuscript we now present a positive correlation between SATB1 binding and deregulation of splicing (Supplementary Fig. 4d) which also supports its direct involvement in the regulation of transcriptional and co-transcriptional processes.

In the revised version of the manuscript we have made this clear in Lines 182-194: “Satb1 cKO animals display severely impaired T cell development associated with largely deregulated transcriptional programs as previously documented19,37,38. In our accompanying manuscript19, we have demonstrated that long SATB1 isoform-specific binding sites (GSE17344619) were associated with increased chromatin accessibility compared to randomly shuffled binding sites (i.e. what expected by chance), with a visible drop in chromatin accessibility in Satb1 cKO. Moreover, the drop in chromatin accessibility was especially evident at the transcription start site of genes, suggesting that the long SATB1 isoform is directly involved in transcriptional regulation. Consistent with these findings and with SATB1’s nuclear localization at sites of active transcription, we identified a vast transcriptional deregulation in Satb1 cKO with 1,641 (922 down-regulated, 719 up-regulated) differentially expressed genes (Fig. 2f). Specific examples of transcriptionally deregulated genes underlying SATB1-dependent regulation are provided in our accompanying manuscript19. Additionally, there were 2,014 genes with altered splicing efficiency (Supplementary Fig. 4d-e; Supplementary File 3-4). We should also note that the extent of splicing deregulation was directly correlated with long SATB1 isoform binding (Supplementary Fig. 4d).”

Major conclusion C)-Post transcriptional modification is important for SATB1 function.

This point is just barely touched upon in the last figure of the paper

We would not call the identification of the novel phosphorylation site as a main conclusion of our manuscript. Though, it is already known that posttranslational modifications of SATB1 are important for its function as they can function as a molecular switch rendering SATB1 into either an activator or a repressor (Kumar et al., 2006; https://doi.org/10.1016/j.molcel.2006.03.010).

In the revised manuscript, we support the effect of serine phosphorylation on the DNA binding capacity of SATB1 by another experiment. We have performed DNA affinity purification experiments utilizing primary thymocyte nuclear extracts treated with phosphatase (Supplementary Fig. 7b). We found that SATB1’s capacity to bind DNA (RHS6 hypersensitive site of the TH2 LCR) is lost upon treatment with phosphatase (Supplementary Fig. 7c). These results are in line with the data presented in Supplementary Fig. 7d, indicating the lost ability of SATB1 to bind DNA upon mutating the discovered phosphorylation site S635. Given the importance of posttranslational modifications of proteins on LLPS, we found it relevant to include it in our manuscript. Even more so, when we identified SATB1 aggregation, upon mutation of this phospho site (Fig. 6d).

Overall I find that the major conclusion-point A and B, is based on very indirect experiments and needs much more convincing data and the role of SATB1 LLPS in cells should be demonstrated more rigorously. And conclusion C is barely described and needs a lot more cell biological and genetic evidence.

One of the major assets of our work is that most of our data are based on the analysis of primary murine T cells and thus investigating the biological roles of the endogenous SATB1 protein, under physiological conditions. We apologize that we did not make it clear to this Reviewer, that our system has certain inherent limitations due to the utilization of primary cells.

I do not recommend publishing the paper in current state. The story needs much more experiment to convincingly prove the major conclusions. Further, the MS needs more careful thinking and presentation to make it streamlined.

We hope that in the revised version we have significantly improved the quality of our manuscript by implementing the suggested changes.

Minor comments: One of the major flaw of the paper is the use too many techniques without proper explanation. E.g. use of STED and RAMAN microscopy need controls and explanation on what is being quantified. The use of Raman microscopy to quantify the nuclear environment of nucleus is not related to the chromatin organization or LLPS of SATB1 at all. And no information is provided at all which aspect of nuclear organization is being measured in Raman and what it means for the LLPS of SATB1.

We do provide quite a thorough explanation of Raman spectroscopy and the underlying quantification in Lines 224-231: “we employed Raman spectroscopy, a non-invasive label-free approach, which is able to detect changes in chemical bonding. Raman spectroscopy was already used in many biological studies, such as to predict global transcriptomic profiles from living cells42, and also in research of protein LLPS and aggregation43–47. Thus we reasoned that it may also be used to study phase separation in primary T cells. We measured Raman spectra in primary thymocytes derived from both WT and Satb1 cKO animals and compared them with spectra from cells upon 1,6-hexanediol treatment. Principal component analysis of the resulting Raman spectra clustered the treated and non-treated Satb1 cKO cells together, while the WT cells clustered separately (Fig. 3h).” We also do provide controls as the method was performed on both treated and untreated WT and Satb1 cKO cells.

Regarding the RAMAN spectroscopy experiments we now provide more information on the changes of chemical bonds altered between wild type and Satb1 cKO thymocytes. Following principal component analysis, we have extracted the two main principal components that were used for the clustering of our data. The differences are presented in Supplementary Fig. 5d.

We do realize that RAMAN spectroscopy, although a quite novel approach utilized to study LLPS, has not been used to study LLPS in live cells. If deemed proper we are willing to avoid presenting these results in this manuscript.

Similarly for Hexanediol treatment, duration of treatment is missing. Hexanediol can also dissolve the liquid like transcription foci. And hence a decrease in correlation between SATB1 foci and FU foci cannot be taken as a measure of SATB1 foci connection to transcription alone

The duration of hexanediol treatment was 5 minutes as presented in Line 724 and in the revised version of the manuscript also in Lines 1206-1207. We should also note that additionally, we performed experiments with different hexanediol concentrations and timing varying from 1 minute to 10 minutes with results consistent with the data presented.

It is not very clear how many times the STED or Raman microscopy is done on how many samples and biological replicates. Similarly for RNA sequencing number of samples and description of controls are missing. Also if the sequencing data is made publicly available is not clear.

Data availability is clearly stated in Lines 506-509: “RNA-seq experiments and SATB1 binding sites are deposited in Gene Expression Omnibus database under accession number GSE173470 and GSE173446, respectively. The other datasets generated and/or analyzed during the current study are available upon request.”

The Reviewer’s token is “wjwtmeeeppovzqx”.

RNA sequencing was performed in a biological triplicate for each genotype as stated in the GEO repository and now also in Line 566 of the revised manuscript.

In Lines 180-181, we also state that it was performed on Satb1 cKO animals and WT mice as a control: “we performed stranded-total-RNA-seq experiments in wild type (WT) and Satb1fl/flCd4-Cre+ (Satb1 cKO) murine thymocytes”.

In Lines 739-740, we now also state that all imaging approaches were performed on at least two biological replicates (different mice) and please also note the fact that all findings were based on data from both STED and 3D-SIM methods, allowing to minimize detection of artifacts. In the Raman spectroscopy figure, each point represents measurements from an individual cell and for each condition we used 2-5 biological replicates (Lines 831-832 & Line 1169).

Similarly, in Lines 129-132 we provided a quite detailed description of differences between STED and 3D-SIM, even though these techniques are not that rare as Raman spectroscopy in biology research.

Additional control is needed to report the resolution limit of Superresolution techniques-STED and 3D-SIM systems used by them.

We have already provided this information in our reply to comment #1 of this Reviewer (pages 6-7): In the revised version of the manuscript, we have specified the resolution of our systems, for STED in Lines 745-746: ”This system enables super-resolution imaging with 35 nm lateral and 130 nm axial resolution.” and for SIM in Lines 759-761: “Images were acquired over the majority of the cell volume in z-dimension with 15 raw images per plane (five phases, three angles), providing ~120-135 nm lateral and ~340-350 nm axial resolution for 488/568 nm lasers, respectively.” The resolution of our systems is routinely verified by the following methods: The resolution of our OMX (SIM-3D) system was tested using ARGO-SIM slide containing a pattern of 36 µm long lines with gradually increasing spacing ranging from (left to right) 0 to 390 nm, with a step of 30 nm (Fig. 1 below). Our SIM system was able to clearly resolve two lines separated by 120 nm.

Would be very helpful if the zonation was plotted for the FluoroUridine (FU) also to show that Zone1 (heterochromatin) is completely depleted of FU, and is present in other regions.

In the revised version of the manuscript, we performed the suggested analysis and in Supplementary Fig. 3a we now show that indeed FU is significantly less localized to Zone 1 (heterochromatin) and has the most abundant localization in Zones 3 and 4, similar to the localization of SATB1 protein, as demonstrated in Fig. 2b.

Scale bar needed figure 3d

In the revised version of the manuscript, we included scale bars which are both 0.5 µm (line 1213).

Perfectly rounded SATB1 foci- this does not mean LLPS. For LLPs measurement, protein condensate dynamics measurement by FRAP or fusion experiments is required. What is the size of condensates? and cellular concentration of SATB1? Will SATB1 undergo LLPS in vitro at similar concentrations? does SATB1 interact with DNA or RNA to undergo LLPS ?

We toned down this sentence which now reads: “Here we demonstrated its connection to transcription and found that it forms spherical speckles (Fig. 1g), markedly resembling phase separated transcriptional condensates. (Lines 200-202)”.

Moreover, as explained in earlier replies to comments of this Reviewer, we cannot perform FRAP on primary murine T cells without generating a new mouse line. We did, however, use FRAP and other in vitro approaches including visualization of droplet fusion in ex vivo experiments utilizing cell lines. Moreover, we are willing to demonstrate the LLPS properties of SATB1 on in vitro purified SATB1 protein as indicated in the suggested experiment of Point#4 (page 2).

After careful reading of the MS I conclude that the main conclusions of the paper are very preliminary and need much more detailed experiments. So does not qualify to get published at all at this stage.

**Reviewer #1 (Significance)**:

The present manuscript tries to connect the phase separation of SATB1 to understanding the mechanism of SATB1 function in cells. One of the major hallmarks of phase separation is dynamic, liquid-like behaviour and in absence of these measurements, it is very difficult to say that the current manuscript has made any contribution to showing that SATB1 can phase separate.

The presence of 2 isoforms of SATB1 is a novel finding and the paper could have focused more on this. E.g. elucidate expression of the isoform during thymocyte development and maturation.

As a reviewer my expertise are cell biology experiments, microscopy, in vitro reconstitution assays, RNA binding proteins, RNA and RBP condensate formation. And I feel that the reconstitution experiments are an important tool for understanding phase behaviour of proteins and also to gauge if this behaviour can occur or not in cellular concentration and conditions.

I do not have sufficient expertise in Raman microscopy and hence the information provided in the MS on this part was not enough to understand the experiment and conclusions drawn from it.

**Reviewer #2 (Evidence, reproducibility and clarity)**:

The authors have reported the existence of a 'long' SATB1 isoform which also undergoes LLPS. The authors tried to draw multiple comparisons and pointed out distinction between phase properties of SATB1 isoforms. The authors also touch upon two functional roles of SATB1. Although a wide array of assays are used, the data presented and hence the manuscript makes multiple transitions into disparate hypotheses without diving deep into a single hypothesis. As a result, the connections drawn are unclear, and do not converge at best. The authors have used number of techniques, however, the results do not support their conclusions and they appear hastily drawn. It is not clear why the authors jump from one context to the other, discussing LLPS first, then transcription, splicing, post-translational modification and finally cancer. The link between all of these isn't clear and not fully supported by data. It appears that the authors wish to focus on Satb1's physiological role in development, hence the data on breast cancer is confusing. Thus, this work suffers from multiple pitfalls. Specific comments are given below:

Major comments 1. Importantly, in Fig 1d, there is no statistics shown. There is no mention of number of replicates as well in the legends. Proper statistical evaluation is critical for interpreting this result.

Please note that Fig. 1d only serves as a control to the sequencing experiment in Fig. 1b. In Line 566, we now state that for the RNA-seq: “A biological triplicate was used for each genotype.” To validate these data, we further designed a RT-qPCR experiment which was performed on three technical replicates from a male and female mouse. We now state this in Line 636. For the low number of samples, statistical tests are not accurate but we still added t test into the figure Fig. 1d and specified it also in the figure legend in Line 1169-1170.

1. Figure 1f presents one of the weakest evidences in the manuscript. There are a number of corrections needed. Firstly, being their major and only validation figure for their custom antibody, the immunoblot is not clean, bands are fuzzy. Importantly, as the authors claim that the antibody is highly specific to 'long' SATB1, after the IP there should be only a single band (like input) of Satb1 long. But that does not seem to be the case, rather an array of bands are visible below (lane 2 top panel). This could easily mean that the shorter isoforms or non-specific protein bands are also pulled down with the 'long' form specific antibody. Therefore, raising a critical concern regarding the specificity of the antibody.

• The long antibody was raised in mice inoculated with the extra peptide present in the long isoform only. Therefore, the capacity of this antibody precipitating the shorter isoforms, which do not express the sequence of the extra peptide (EP, Figure 1a) in not possible. • We have repeated the immunodepletion experiment and we now provide the results in Fig. 1f and Supplementary Fig. 1b. The western blot in Fig. 1f is now cleaner and supports quite convincingly the presence of a long SATB1 isoform. Given the lack of isoform-specific knockouts which we could utilize to immunoprecipitate or detect the different isoforms in a single cell (or cell population), the utilized approach of immunodepletion and subsequent western blotting is the approach we thought of implementing. • As shown in Fig. 1f and Supplementary Figure 1b, the long isoform SATB1 antibody has the capacity to recognize the long isoform in murine thymocyte protein extracts but not the short SATB1 isoform (please compare lane 3 in the two western blots utilizing either the antibody for the long isoform -top panel - or the antibody that detects both isoforms (lower panel). • We have performed Immunofluorescence experiments utilizing the antibody detecting the long SATB1 isoform in thymocytes isolated from either C57BL/6 or Satb1 cKO mice. The antibody is specific to the SATB1 protein since there is no signal in immunofluorescence experiments utilizing the knockout cells (Supplementary Figure 1c). • We have performed Immunofluorescence experiments utilizing thymocytes and the antibody detecting the long SATB1 or a commercially available antibody detecting all SATB1 isoforms. The pattern of SATB1 subnuclear localization is similar for both antibodies (Supplementary Figure 1e). • In our accompanying revised manuscript Zelenka et al., 2022 (https://doi.org/10.1101/2021.07.09.451769), we provide yet another piece of evidence, consisting of bacterially expressed short and long SATB1 protein isoforms detected by western blot using either the long isoform-specific or the non-selective all SATB1 isoforms antibodies. • Regarding the additional bands detected in the immunoprecipitation experiment presented in the original Supplementary Figure 1b (lane 2), it is not surprising that additional bands appear in a sample of protein extracts that is used for several hours for the immunoprecipitation experiments, while the “input” sample simply denotes protein extract that is frozen at -80oC right after the preparation of protein extracts until use. It is well-established that SATB1 is the target of proteases which might as well be active during the immunoprecipitation steps (2 consecutive immunoprecipitation steps take place). Therefore, the immunoprecipitated material cannot necessarily be a copy of the input material displaying a single protein band even if protease inhibitors are included in the buffers.

Taken together the experiments described here we showed that the antibody raised against the extra 31 aa long peptide, present only in the long SATB1 isoform, is specific for this isoform.

1. Related to Fig. 2 a, the authors state on Pg 5, '....the euchromatin and interchromatin regions (zones 3 & 4, Fig. 2a, b).' Although the DAPI correlation seems clear, there is no mention on how they reached the above said correlation. They should at least show a parallel speckle staining for HP1 or signature modification such as H3K4me9 STEDs for making supporting such a claim. DAPI alone is not sufficient. The authors should rectify the text thoroughly for many such interpretations without validation/reference or provide relevant data.

This is a great suggestion we have again taken under consideration and we added the following experiments and the appropriate changes in the revised version of our manuscript. • We modified the text and added a reference to Miron et al., 2020 (https://doi.org/10.1126/sciadv.aba8811) supporting our claims regarding SATB1 localization in relation to DAPI staining. • We have also added new microscopy images for HP1, H3K4me3 and fibrillarin staining and quantified the localization of FU-stained sites of active transcription in nuclear zones, to further support our claims. • This whole modified part in Lines 139-167 then reads: “ “The quantification of SATB1 speckles in four nuclear zones, derived based on the relative intensity of DAPI staining, highlighted the localization of SATB1 mainly to the regions with medium to low DAPI staining (zones 3 & 4, Fig. 2a, b). A similar distribution of the SATB1 signal could also be seen from the fluorocytogram of the pixel-based colocalization analysis between the SATB1 and DAPI signals (Supplementary Fig. 2a). SATB1’s preference to localize outside heterochromatin regions was supported by its negative correlation with HP1β staining (Supplementary Fig. 2b). Localization of SATB1 speckles detected by antibodies targeting all SATB1 isoforms and/or only the long SATB1 isoform, revealed a significant difference in the heterochromatin areas (zone 1, Fig. 2b), where the long isoform was less frequently present (see also Fig. 2a and Fig. 3c). Although, this could indicate a potential difference in localization between the two isoforms, due to the inherent difficulty to distinguish the two based on antibody staining, we refrain to draw any conclusions. The prevailing localization of SATB1 corresponded with the localization of RNA-associated and nuclear scaffold factors, architectural proteins such as CTCF and cohesin, and generally features associated with euchromatin and active transcription32. This was also supported by colocalization of SATB1 with H3K4me3 histone mark (Supplementary Fig. 2c), which is known to be associated with transcriptionally active/poised chromatin. Given the localization of SATB1 to the nuclear zones with estimated transcriptional activity32 (Fig. 2b, zone 3), we investigated the potential association between SATB1 and transcription. We unraveled the localization of SATB1 isoforms and the sites of active transcription labeled with 5-fluorouridine. Sites of active transcription displayed a significant enrichment in the nuclear zones 3 & 4 (Supplementary Fig. 3a), similar to SATB1. As detected by fibrillarin staining, SATB1 also colocalized with nucleoli which are associated with active transcription and RNA presence (Supplementary Fig. 3b). Moreover, we found that the SATB1 signal was found in close proximity to nascent transcripts as detected by the STED microscopy (Fig. 2c). Similarly, the 3D-SIM approach indicated that even SATB1 speckles that appeared not to be in proximity with FU-labeled sites in one z-stack, were found in proximity in another z-stack (Supplementary Fig. 3c). Additionally, a pixel-based colocalization of SATB1 and sites of active transcription is quantified later in the text in Fig. 3g, supporting their colocalization.”

1. The authors mention, '...of the different SATB1 isoforms, uncovered by the use of the two different antibodies, relied in the heterochromatin areas (zone 1), where the long isoform was less frequently...' There is no supporting figure number mentioned. The authors need to show a zone-by-zone comparison images for 'all iso' vs 'long' iso of SATB1. Just to reiterate, there is a need for a heterochromatin mark to unambiguously call out the distinction.

We should remind that there is an inherent difficulty to accurately compare localization of short and long SATB1 isoforms in primary cells, especially due to the lack of Satb1 isoform-specific knockout mice. There is no way to detect only the short isoform in these primary cells as there are only antibodies targeting the long or all SATB1 isoforms. Therefore, we cannot set up additional experiments probing these questions.

In line with this, in the revised version of the manuscript, we toned down our statements regarding the differential localization of the two isoforms in primary cells. We only refer to it as an indication and we support it by adding references to the relevant figures. This part now reads: “Localization of SATB1 speckles detected by antibodies targeting all SATB1 isoforms and/or only the long SATB1 isoform, revealed a significant difference in the heterochromatin areas (zone 1, Fig. 2b), where the long isoform was less frequently present (see also Fig. 2a and Fig. 3c). Although, this could indicate a potential difference in localization between the two isoforms, due to the inherent difficulty to distinguish the two based on antibody staining, we refrain to draw any conclusions. (Lines 145-150)”

1. On the same lines, '....Given the localization of SATB1 to the nuclear zones with estimated transcriptional activity (Fig. 2b, zone 3)....' How was the region labelled as transcriptionally active? For the statistical analysis of speckle count for the two antibodies' staining, the claim posited is a bit bigger. This could simply be true for that cell. The authors thus need to statistically analyse the speckle counts for multiple cells. This needs to be done for all imaging statistics done in multiple figures throughout the manuscript.

As mentioned in our reply to the two previous comments of this Reviewer, transcriptional activity in relation to the nuclear zonation is well established in the literature. To make this clear, we have now added the reference to Miron et al., 2020 (https://doi.org/10.1126/sciadv.aba8811) supporting our claims and additionally we have also included HP1, H3K4me3 and fibrillarin staining and quantification of FU signal in the nuclear zones. Moreover, it is not clear to which particular cell the comment refers to. The presented dots in Fig. 2b represent individual cells and the relative proportions of speckles in each nuclear zone are plotted on the y axis. In the revised version of the manuscript, we added into the figure the number of cells scored and we adapted the figure legend so that it is absolutely clear that we have analyzed multiple cells:

“Nuclei of primary murine thymocytes were categorized into four zones based on the intensity of DAPI staining and SATB1 speckles in each zone were counted. Images used represented a middle z-stack from the 3D-SIM experiments. The graph depicts the differences between the long and all SATB1 isoforms’ zonal localization in nuclei of primary murine thymocytes. (Lines 1189-1193)”

1. For figure 2c. the authors have used 5 Fluorouridine for nascent RNA speckles. 5FU is known to have a spread signal type (with strong association to nucleolus as well). This is not the case for the image presented 2c. The authors should resolve this by showing different sets of images.

Developing and naive T cells are very unique in terms of their metabolic features and thus they should not be directly compared with other cell types. Therefore, we would not expect to see such a spread FU pattern as previously shown for other cell types. Having said that, we could not find any reference publication that utilized super-resolution microscopy to detect localization of FU-stained sites of active transcription in developing primary T cells. However, we performed additional immunofluorescence experiments to demonstrate the colocalization or its lack between SATB1 and HP1 (Supplementary Fig. 2b), H3K4me3 (Supplementary Fig. 2c) and fibrillarin (Supplementary Fig. 3b). Moreover, we provide additional regions of SATB1 and FU staining in Supplementary Fig. 3c. The modified text reads:

“We unraveled the localization of SATB1 isoforms and the sites of active transcription labeled with 5-fluorouridine. Sites of active transcription displayed a significant enrichment in the nuclear zones 3 & 4 (Supplementary Fig. 3a), similar to SATB1. As detected by fibrillarin staining, SATB1 also colocalized with nucleoli which are associated with active transcription and RNA presence (Supplementary Fig. 3b). Moreover, we found that the SATB1 signal was found in close proximity to nascent transcripts as detected by the STED microscopy (Fig. 2c). Similarly, the 3D-SIM approach indicated that even SATB1 speckles that appeared not to be in proximity with FU-labeled sites in one z-stack, were found in proximity in another z-stack (Supplementary Fig. 3c). Additionally, a pixel-based colocalization of SATB1 and sites of active transcription is quantified later in the text in Fig. 3g, supporting their colocalization. (Lines 157-167)”

1. Fig 2 d., the authors have suddenly jumped solely to 'all iso' Satb1 here for IP MS. Is there a reason for that? The authors either need to do this with 'long iso' antibody or remove the analysis from the manuscript as it does not add to their primary aim of the manuscript. Also, the authors have only selectively talked about two clusters? What about chromatin related proteins? It is quite intuitive to have highest enrichment of these given previous literature and even IP MS data by other groups. Thus, it is necessary to revise this thoroughly or remove it.

We appreciate the acknowledgment by the Reviewer that our IP-MS data identified anticipated factors. In the revised version of the manuscript we modified the underlying text to accommodate references to these former findings revealing interactions between SATB1 and chromatin modifying complexes: “Apart from subunits of chromatin modifying complexes that were also detected in previous reports25,33–36, unbiased k-means clustering of the significantly enriched SATB1 interactors revealed two major clusters consisting mostly of proteins involved in transcription (blue cluster 1; Fig. 2d and Supplementary Fig. 4c) and splicing (yellow cluster 2; Fig. 2d and Supplementary Fig. 4c). (Lines 170-174)”

Please note that many subunits of chromatin modifying and chromatin-related complexes are in fact characterized as transcription-related factors, therefore our statements are not in disagreement with the former findings. Note also that we provide Supplementary File 1 & 2 with comprehensive description of our IP-MS data for the readers’ convenience. Please also note that we are the first group to report on the existence of the long isoform. Therefore, we find it absolutely reasonable to perform IP-MS experiment for all SATB1 isoforms which can then be used for a comparison with other publicly available datasets. We believe that there is no contradiction in this experimental setup in relation to the rest of the manuscript. We discuss the two major clusters simply because they are the two major clusters identified as indicated in Fig. 2d. Additionally, in Supplementary Fig. 4c, we provide a comprehensive description of all significantly enriched interactors including their cluster annotation and thus anyone can investigate the data if needed.

1. In relation to Fig. 2f, the authors have not mentioned any of the previously published work on Satb1 CD4 specific KO, not even the RNA seq studies the other groups have reported under the same condition. Only an unpublished reference of their own (preprint) is cited. It is imperative to show how much their data corroborates with other published studies. Additionally, what is the binding site status of dysregulated genes?

In the revised version of the manuscript, we have included the references to other studies using the same Satb1 conditional knockout. Moreover, we have clarified the relationship between SATB1 binding and gene transcription. The modified part in Lines 182-194 now reads: “Satb1 cKO animals display severely impaired T cell development associated with largely deregulated transcriptional programs as previously documented19,37,38. In our accompanying manuscript19, we have demonstrated that long SATB1 isoform specific binding sites (GSE17344619) were associated with increased chromatin accessibility compared to randomly shuffled binding sites (i.e. what expected by chance), with a visible drop in chromatin accessibility in Satb1 cKO. Moreover, the drop in chromatin accessibility was especially evident at the transcription start site of genes, suggesting that the long SATB1 isoform is directly involved in transcriptional regulation. Consistent with these findings and with SATB1’s nuclear localization at sites of active transcription, we identified a vast transcriptional deregulation in Satb1 cKO with 1,641 (922 down-regulated, 719 up-regulated) differentially expressed genes (Fig. 2f). Specific examples of transcriptionally deregulated genes underlying SATB1-dependent regulation are provided in our accompanying manuscript19. Additionally, there were 2,014 genes with altered splicing efficiency (Supplementary Fig. 4d-e; Supplementary File 3-4). We should also note that the extent of splicing deregulation was directly correlated with long SATB1 isoform binding (Supplementary Fig. 4d).”

1. In context of Figure 3a and b, the authors write .'...The long SATB1 isoform speckles evinced such sensitivity as demonstrated by a titration series with increasing concentrations of 1,6-hexanediol treatment followed...' Whereas it is apparent from the image at least that overall numbers of individual speckles are instead increased at both 2 and 5%. There is although a clear spreading of restricted speckles compared to the controls. The authors should revise their figures to substantiate the associated text. Furthermore, there needs to be 'all iso' SATB1 3D SIM imaging and not just quantitation for comparison. This is also true for panel c in order to demonstrate the effect.

In the revised Fig. 3a we provide new images which better reflect the underlying data analysis. Moreover, in Fig. 3c and Fig. 3d we provide an additional comparison between SATB1 all isoforms and long isoform staining and their changes upon hexanediol treatment, detected by both the 3D-SIM and STED approaches. It is true that upon treatment, there tend to be more speckles, however these are much smaller as they are gradually being dissolved. Depending on the treatment duration, the cells are swollen which is reflected in increased spreading of speckles. Nevertheless, the nuclear size was considered in all the quantification analyses. We believe that the new images provide better evidence of SATB1’s sensitivity to hexanediol treatment.

1. Fig. 3 d also does not clearly demonstrate what the authors have claimed '...hexanediol treatment highly decreased colocalization between...' The figure shows at best decreased signal intensity for both SATB1 and FU. We suggest that the authors should give a statistical analysis as well for the colocalization points between the two using multiple source images. Lastly, the two images shown (control and treated), there seems to be a clearly visible magnification difference. The authors should clarify this.

• In the revised version of the manuscript in Figure 3d, we have provided scale bars, which are both 0.5 µm (line 1213). The difference observed by this Reviewer is actually the main reason why we provided this image. Figure 3d demonstrates that upon hexanediol treatment, the speckles are mostly missing or significantly reduced in size, for both FU and SATB1 staining. • Moreover, the suggested statistical analysis is also provided – in Figure 3e. In Figure 3e, we performed pixel-based colocalization analysis which is a method that allows both quantification and statistical comparison of colocalization between two factors and between different conditions. Please note especially the decreased colocalization between long SATB1 isoform and FU-stained sites of active transcription in the left graph, which is in agreement with our claims in the manuscript. • Moreover, our data are compared to a negative control, i.e. 90 degrees rotated samples, which is a common method in colocalization experiments as described for example in Dunn et al., 2011 (https://doi.org/10.1152/ajpcell.00462.2010). • Additionally, we provide Costes’ P values which are based on randomly scrambling the blocks of pixels (instead of individual pixels, because each pixel’s intensity is correlated with its neighboring pixels) in one image, and then measuring the correlation of this image with the other (unscrambled) image. Please see Costes et al., 2004 (https://doi.org/10.1529%2Fbiophysj.103.038422) for more details.

1. Figure 3f. The authors show the PC plot for Raman spectroscopy for phase behaviour due to Satb1. The experiment and its related text seems misinterpreted; the authors write...' ese bonds were probably enriched for weak interactions responsible for LLPS that are susceptible to hexanediol treatment. This shifted the cluster of WT treated cells towards the Satb1 cKO cells. However, the remaining covalent bonds differentiated the WT samples from Satb1 cKO cells......' whereas the clusters are clearly far away in 3D for both WT and KO while being closer to their respective treatments. Which is also intuitive given the sensitivity of Raman spectroscopy. Thus, it is more likely to be treatment effect and KO effect as separate. Treatment of WT leads to KO like spectra is far-fetched. Thus, the authors need to show separate PCs and modify their text thoroughly.

We do not present any 3D graph hence it is not clear what the Reviewer refers to. Please also note that as stated in Lines 817-818, we used a customized Raman Spectrometer. Therefore, this approach allowed us to measure Raman spectra at cellular and even sub-cellular levels. For example, solely by utilizing Raman spectroscopy, we can now distinguish euchromatin and heterochromatin, methylated and unmethylated DNA and RNA, etc. This, together with other reports, such as Kobayashi-Kirschvink et al., 2018 (https://doi.org/10.1016/j.cels.2018.05.015) and Kobayashi-Kirschvink et al., 2022 (https://doi.org/10.1101/2021.11.30.470655), indicate a potential use of Raman in biological research. In our manuscript, we used this method as a supplementary approach, however we do find it noteworthy. We should also emphasize that in the revised Raman spectroscopy Fig. 3h, each point represents measurements from an individual cell and for each condition we used 2-5 biological replicates (Lines 831-832 & Lines 1225-1226). We specifically refer to the principal component 1 (PC1) that differentiates the samples. Therefore, there are certain spectra (representing certain chemical bonding) that allowed us to differentiate between WT and Satb1 cKO. The same type of bonding was then affected when WT samples were treated with hexanediol and we also had controls to rule out the impact of hexanediol on the resulting spectra.

1. In Fig 4. b, The authors have shown the propensity of SATB1 N terminus to phase separate using different optodroplet constructs. Although the imaging is clear, why are the regions selected not uniform when comparing various constructs?

We have selected images that would best represent each category. Please note that this was live cell imaging of photo-responsive constructs, thus there are many limitations regarding the area selection. Very often, even the brief time of bright light exposure to localize cells may trigger protein clustering. Upon disassembly, every new light exposure of the same cell then triggers much faster assembly which skews the overall results. It is therefore desired to work fast, while neglecting selection of equally sized cells. Moreover, it is not clear how would the proposed change improve the quality of our manuscript.

1. Figure 5a, the disassembly should be shown for 'long' SATB1 as well. On pg 13, the authors write '....cytoplasmic protein aggregation has been previously described for proteins containing poly-Q domains and PrLDs..' no reference given.

• In the revised version of the manuscript, we present the assembly and disassembly for both short and long full length SATB1 optogenetic constructs. To increase clarity, we present the behavior of the short and long isoforms as two separate images in Figure 5a and Figure 5b, respectively. • Moreover, we provided references to the statement regarding aggregation of PrLD and poly-Q-containing proteins in Lines 305-309, which now reads: ”Since protein aggregation has been previously described for proteins containing poly-Q domains and PrLDs8,11,38,39, we next generated truncated SATB1 constructs encoding two of its IDR regions, the PrLD and poly-Q domain and in the case of the long SATB1 isoform also the extra peptide neighboring the poly-Q domain (Fig. 1a and 4a).”

1. Fig. 5d, Is there an amino-acid specific reasoning to support the authors claim of the phase behaviour due to extra peptide? They need to show a proper control with equal extra (unrelated) peptide to show the specificity. Are the shorter isoform aggregates responsive to light?

• We have referred to the amino acid composition bias in Fig. 5c. In the revised version of the manuscript, we made this clear by showing the composition bias in the new revised Fig. 5e. The related part of the main text then reads: “Computational analysis, using the algorithm catGRANULE37, of the protein sequence for both murine SATB1 isoforms indicated a higher propensity of the long SATB1 isoform to undergo LLPS with a propensity score of 0.390, compared to 0.379 for the short isoform (Fig. 5d). This difference was dependent on the extra peptide of the long isoform. Out of the 31 amino acids comprising the murine extra peptide, there are six prolines, five serines and three glycines – all of which contribute to the low complexity of the peptide region3 (Fig. 5e).” (Lines 298-304) • Moreover, we should note that the low complexity extra peptide of the long SATB1 isoform directly extends the PrLD and IDR regions as indicated in Fig. 4a and which we now directly state in Lines 304-305: “Moreover, the extra peptide of the long SATB1 isoform directly extends the PrLD and IDR regions as indicated in the Fig. 4a.” • We show in Fig. 4, that the N terminus of SATB1 undergoes LLPS. Since this part of SATB1 is shared by both isoforms, it is reasonable to assume that both isoforms would undergo LLPS. This is also in line with the observed photo-responsiveness of both short and long full length SATB1 isoforms in CRY2 optogenetic constructs in revised Fig. 5a,b, and similar FRAP results for both short and long full length SATB1 isoform constructs transiently transfected in NIH-3T3 cells in the revised Supplementary Fig. 6f. However, the main reason why we think that the difference in LLPS propensity between the isoforms is important is because the long isoform is more prone to aggregate compared to the short isoform, as documented in Fig 5c,f,g and Supplementary Fig. 5f.

1. Fig 6c., It is important that authors show the data for NLS+short iso data as well to prove their hypothesis.

As shown in original Figure 5d, the long SATB1 isoform undergoes cytoplasmic aggregation, unlike the short SATB1 isoform (as shown in the same Figure). Therefore, an image of the NLS + short isoform would not be related to our hypothesis. Actually, we wanted to reverse the long SATB1 isoform’s relocation, from the aggregated form in the cytoplasm into the nucleus. Nevertheless, to show the complete picture, in the revised version of the manuscript in Figure 6c, we now provide data for both short and long SATB1 isoforms.

1. Fig 6d., The authors claim that mutating a specific P site changes the phase behaviour of the 'short iso'. Does it also increase for the long isoform? The authors need to confirm this in order to verify the effect of a single P site outside of oligomerization domain. ...' phosphorylation status; when phosphorylated it remains diffused, whereas unphosphorylated SATB1 is localized to PML bodies....' This being an important premise, thus should be moved to the results text.

In the revised version of the manuscript, we moved the part regarding PML in the results section, as suggested by the Reviewer. Moreover, we included additional experiments probing the impact of association between PML and two SATB1 full length isoforms on their dynamics. The modified section in Lines 357-368 now reads: “In relation to this, a functional association between SATB1 and PML bodies was already described in Jurkat cells64. We should note that PML bodies represent an example of phase separated nuclear bodies65 associated with SATB1. Targeting of SATB1 into PML bodies depends on its phosphorylation status; when phosphorylated it remains diffused, whereas unphosphorylated SATB1 is localized to PML bodies66. This is in line with the phase separation model as well as with our results from S635A mutated SATB1, which has a phosphorylation blockade promoting its phase transitions and inducing aggregation. To further test whether SATB1 dynamics are affected by its association with PML, we co-transfected short and long full length SATB1 isoforms with PML isoform IV. The dynamics of long SATB1 isoform was affected more dramatically by the association with PML than the short isoform (Supplementary Fig. 7e), which again supports a differential behavior of the two SATB1 isoforms.”

Moreover, given the localization of the discussed phosphorylation site in the DNA binding region of SATB1 we did test its impact on DNA binding as documented in the revised Supplementary Fig. 7d. Additionally, as we have noted in our answer in Major Comment C of this reviewer, to further support the effect of serine phosphorylation on the DNA binding capacity of SATB1 we have performed DNA affinity purification experiments utilizing primary thymocyte nuclear extracts treated with phosphatase (Supplementary Fig. 7b) We found that SATB1’s capacity to bind DNA (RHS6 hypersensitive site of the TH2 LCR) is lost upon treatment with phosphatase (Supplementary Fig. 7c).

1. Pg 16,. The authors have tried to explain multiple things (concepts of self-regulation, accessibility) which is quite tangential. There is no inference to Fig 6f., which is showing the opposite to what the authors had postulated. This portion should either be removed or explained with a rationale. The writing also needs to be revised thoroughly in this section. Similarly, the discussion should also be modified.

The rationale for the original Fig. 6f (revised Fig. 6g) was described in great detail in Lines 330-343 of the original manuscript. It is not clear why the Reviewer assumes that it shows the opposite to our hypothesis. As we explained, the increased accessibility allows faster read-through by RNA polymerase, and thus the exon with higher accessibility is more likely to be skipped. The exact relationship is shown in the revised Fig. 6g where the increased accessibility is associated with the expression of the short isoform, whereas the long isoform expression needs lower chromatin accessibility which allows the splicing machinery to act on the specific exon to be included. We reason that these findings are important and relevant because: 1) we suggest a potential regulatory mechanism for the SATB1 isoforms production. This is highly relevant to this manuscript given the fact that this is the first report on the existence of the long SATB1 isoform, and 2) the differential production of the long/short SATB1 isoforms has a potential relevance to breast cancer prognosis. In the revised version of the manuscript we added Fig. 6f, which now indicates the differential chromatin accessibility in human breast cancer patients and accordingly the expression of the long SATB1 isoform are associated with worse patient prognosis as indicated in Fig. 6h and Supplementary Fig. 8a,b. In the revised version of the manuscript, we substantially modified the text in Lines 374-408, to make the relevance of all these conclusions clear. The modified text now reads: “Therefore, we reasoned that a more plausible hypothesis would be based on the regulation of alternative splicing. In our accompanying manuscript19, we have reported that the long SATB1 isoform DNA binding sites display increased chromatin accessibility than what expected by chance (Fig. 3b in 19), and chromatin accessibility at long SATB1 isoform binding sites is reduced in Satb1 cKO (Fig. 3c in 19), collectively indicating that long SATB1 isoform binding promotes increased chromatin accessibility. We identified a binding site specific to the long SATB1 isoform19 right at the extra exon of the long isoform (Fig. 6e). Moreover, the study of alternative splicing based on our RNA-seq analysis revealed a deregulation in the usage of the extra exon of the long Satb1 isoform (the only Satb1 exon affected) in Satb1 cKO cells (deltaPsi = 0.12, probability = 0.974; Supplementary File 4). These data suggest that SATB1 itself is able to control the levels of the short and long Satb1 isoforms. A possible mechanism controlling the alternative splicing of Satb1 gene is based on its kinetic coupling with transcription. Several studies indicated how histone acetylation and generally increased chromatin accessibility may lead to exon skipping, due to enhanced RNA polymerase II elongation48,49. Thus the increased chromatin accessibility promoted by long SATB1 isoform binding at the extra exon of the long isoform, would increase RNA polymerase II read-through leading to decreased time available to splice-in the extra exon and thus favoring the production of the short SATB1 isoform in a negative feedback loop manner. This potential regulatory mechanism of SATB1 isoform production is supported by the increased usage of the extra exon in the absence of SATB1 in Satb1 cKO (Supplementary File 4). To further address this, we utilized the TCGA breast cancer dataset (BRCA) as a cell type expressing SATB150. ATAC-seq experiments for a series of human patients with aggressive breast cancer51 revealed differences in chromatin accessibility at the extra exon of the SATB1 gene (Fig. 6f). In line with the “kinetic coupling” model of alternative splicing, the increased chromatin accessibility at the extra exon (allowing faster read-through by RNA polymerase) was positively correlated with the expression of the short SATB1 isoform and slightly negatively correlated with the expression of the long SATB1 isoform (Fig. 6f). Moreover, we investigated whether the differential expression of SATB1 isoforms was associated with poor disease prognosis. Worse pathological stages of breast cancer and expression of SATB1 isoforms displayed a positive correlation for the long isoform but not for the short isoform (Fig. 6g and Supplementary Fig. 6c). This was further supported by worse survival of patients with increased levels of long SATB1 isoform and low levels of estrogen receptor (Supplementary Fig. 6d). Overall, these observations not only supported the existence of the long SATB1 isoform in humans, but they also shed light at the potential link between the regulation of SATB1 isoforms production and their involvement in pathological conditions.”

1. The authors should not draw conclusions based on any data which is not shown '....ed differences in chromatin accessibility at the extra exon of the SATB1 gene (data not shown), suggesting its potential involvement in alternative splicing regulation according to the "kinetic coupling" model...'. This has led to overspeculation and needs correction.

In the revised version of the manuscript, we included the ATAC-seq data from human breast cancer patients in the revised Fig. 6f. The legend of this figure now reads: “Human TCGA breast cancer (BRCA) patient-specific ATAC-seq peaks51 span the extra exon (EE: extra exon; labeled in green) of the long SATB1 isoform. Note the differential chromatin accessibility in seven selected patients, emphasizing the heterogeneity of SATB1 chromatin accessibility in cancer. Chromatin accessibility at the promoter of the housekeeping gene DNMT1 is shown as a control. (Lines 1281-1285)” Accordingly, we have also modified the main text: “ATAC-seq experiments for a series of human patients with aggressive breast cancer68 revealed differences in chromatin accessibility at the extra exon of the SATB1 gene (Fig. 6f). In line with the “kinetic coupling” model of alternative splicing, the increased chromatin accessibility at the extra exon (allowing faster read-through by RNA polymerase) was positively correlated with the expression of the short SATB1 isoform and slightly negatively correlated with expression of the long SATB1 isoform (Fig. 6g).” (Lines 395-339)”

Minor comments: 1. On pg 4, the authors state 'Here, we utilized primary murine T cells, in which we have identified two full-length SATB1 protein isoforms.' Whereas only one 'long' isoform is identified and the other is the canonical version. The authors should correct the statement.

In the revised version of the manuscript, we modified this statement as follows: ”In this work, we utilized primary developing murine T cells, in which we have identified a novel full-length long SATB1 isoform and compared it to the canonical “short” SATB1 isoform.” (Lines 64-66)”

1. Fig. 1 a , Is there a specific reason to generate a custom-made antibody for 'all' SATB1, using similar regions that are already commercially available. This becomes redundant otherwise, because there is no apparent difference in detection compared to the commercial one (Suppl. Fig 1a). Antibody generation strategy (1a) should be moved to supplementary. Additionally, authors have obtained the custom antibodies from a commercial source, therefore, the text should reflect the same alongside relevant details.

The custom-made SATB1 antibody targeting the amino-terminal region of the protein has been developed in order to be utilized for detecting the native form of the protein. Unlike commercially available antibodies raised against either short peptides or denatured forms of the protein we have utilized the native form of the amino-terminal part of the protein for raising this antibody. To be honest, this antibody has been raised in order to be utilized in ChIP-seq experiments since no commercially available antibody is of high quality for this approach. Moreover, the original Figure 1a was utilized in order to provide an overview of the SATB1 protein structure which is highly relevant to understand its biophysical properties and not for presenting the strategy for raising a custom-made antibody for SATB1.

1. Fig 3e: what is the control used here? In their Pearson correlation analysis, there seem to be significant reduction in control sets as well upon treatment. This needs to be clarified.

We used scans rotated by 90° which served as a negative control, as stated in Line 769: “SATB1 scans rotated by 90° served as a negative control for the colocalization with FU.” Note that this is a commonly used control in colocalization experiments as described for example in Dunn et al., 2011 (https://doi.org/10.1152/ajpcell.00462.2010).

Additionally, we provide Costes’ P values which are based on randomly scrambling the blocks of pixels (instead of individual pixels, because each pixel’s intensity is correlated with its neighboring pixels) in one image, and then measuring the correlation of this image with the other (unscrambled) image. Please see Costes et al., 2004 (https://doi.org/10.1529%2Fbiophysj.103.038422) for more details. Moreover, it was actually anticipated to see a decrease in colocalization upon hexanediol treatment even in the negative control, as hexanediol significantly reduces both SATB1 and FU speckles as established in Fig. 3a-d.

1. Pg 10, the authors claim that '..., thus we reasoned that it may also be used to study phase separation...' But there have been numerous reports starting from 2018, which have utilized this technique in corelation to phase behaviour (albeit individual proteins). The authors should include proper citations as they are extending an idea from the same field to their specific need.

In the revised version of the manuscript, we included relevant citations to support the use of Raman spectroscopy in LLPS research: “Raman spectroscopy was already used in many biological studies, such as to predict global transcriptomic profiles from living cells42, and also in research of protein LLPS and aggregation43–47. Thus we reasoned that it may also be used to study phase separation in primary T cells.” (Lines 225-228)”

1. For Fig 5b, there should be a comparative image for 'short' isoform.

In the revised Figure 5c we have included a comparative image for the short SATB1 isoform.

1. In the context of Figure 5c, the authors claim ...' Note also the higher LLPS propensity of the human long SATB1 isoform compared to the murine SATB1...' Why suddenly human and mouse comparisons are drawn? This figure should be moved to supplementary.

The comparison between the human and mouse SATB1 isoforms has been implemented because it is relevant for our claims regarding the increased SATB1 aggregation in human cells in relation to the revised Fig. 6f,g,h and Supplementary Fig. 6c,d. This is also discussed in Lines 479-482, which read: “This is particularly important given the higher LLPS propensity of the human long SATB1 isoform compared to the murine SATB1 (Fig. 5d). Therefore, human cells could be more susceptible to the formation of aggregated SATB1 structures which could be associated with physiological defects.”

**Reviewer #3 (Evidence, reproducibility and clarity):**

Zelenka et al., focus on a T cell genome-organizing protein, SATB1, to show that SATB1 undergoes liquid liquid phase-separation (LLPS), and distinct isoforms confer different LLPS-related biophysical properties. They generate a long-isoform specific antibody and conduct several experiments to test for LLPS and compare LLPS properties between the long-isoform relative to the whole SATB1 protein population. Given that SATB1 plays important roles in T cell development and in cancer, interrogating SATB1 biophysical properties is an important question. However, there are multiple problems with the experimental setup and data that weaken their support of the conclusions. I will detail some of the major issues below:

Regarding phase-separation There are several assays to determine whether a protein undergoes LLPS. 1. One of the first the authors address is the spherocity or roundness. Indeed, formation of spherical droplets is one evidence of the liquid nature of a protein. However, the authors use fixed preparations (which can introduce artifacts), not free-floating protein, and determine roundness by showing a 2D image. Roundness should take into account the diffraction-limits of fluorescent imaging, as many structures can be imaged to appear round by the detector. There are quantifiable measurements that can be taken on 3D images to show roundness. This would best be shown using non-fixed protein.

• We thank this Reviewer for several insightful comments. Although, we agree with most of them, we should highlight the main goal of our manuscript, i.e. to investigate the SATB1 protein with an emphasis on its physiological roles in primary developing murine T cells. We highlight this already in the introduction in Line 64 “In this work, we utilized primary developing murine T cells,...” and mainly also in the respective part of the result section: “To probe differences in phase separation in mouse primary cells, without any intervention to SATB1 structure and expression, we first utilized 1,6-hexanediol treatment, which was previously shown to dissolve the liquid-like droplets34.(Lines 203-205)”

• We believe that this is a very important aspect of our study that should not be overlooked. The majority of proteins perhaps behave differently under physiological and in vitro conditions. However, due to the extensive post-translational modifications affecting the properties of SATB1, its completely different localization patterns between primary developing T cells and other cell types but especially cell lines and many other aspects, it was of utmost importance to focus our research on primary T cells. Unfortunately, this was accompanied with multiple difficulties, such as that we have to use fixed cells as this is the only way to visualize SATB1 in these cells. Alternatively, one could create a new mouse line expressing a fluorescently tagged SATB1 protein, but this is beyond the scope of our work.

• However, we should also note that many LLPS-related studies do not pay any focus on primary physiological functions of proteins and they simply focus on the investigation of protein’s artificial behavior in in vitro conditions. Having said that, we too extended our experiments in primary cells to the ex vivo studies in cell lines to further support our claims. In these experiments, we utilized live cell imaging in Fig. 4-6, quantified the spherocity in Supplementary Fig. 6, showed the ability of speckles to coalesce in Fig. 4c and also used FRAP in Fig. 4f and also in the revised version of the manuscript in Supplementary Figure 6f. Moreover, we should note that most of these experiments were designed and performed during 2017 and 2018 conforming with the standards. We are well aware of the progress in the field and impact of fixation on LLPS, as described in Irgen-Gioro et al., 2022 (https://doi.org/10.1101/2022.05.06.490956), but after over seven months of review process in another journal we also believe that these aspects should be considered not to delay further progress of the SATB1 field.

Regarding the isoform specificity of SATB1 biophysical properties 1. The authors generate a long isoform-specific antibody. However, the western blot is not convincing that this is indeed specific to the long isoform as there is a rather large smear. Can this be improved with antibody preabsorption? Since this is a key reagent for the manuscript, improvement in antibody quality is essential.

The custom-made antibody for the long isoform has been raised against the unique 31 amino acids long peptide present in the long SATB1 isoform. The polyclonal serum has undergone affinity chromatography utilizing the immobilized peptide (antigen) to purify the antibody. In the revised version of the manuscript we have included another immunodepletion experiment with cleaner bands (Fig. 1f). Moreover, please read our answer to Major comment #2 of Reviewer 1 that follows: • The long antibody was raised in mice inoculated with the extra peptide present in the long isoform only. Therefore, the capacity of this antibody precipitating the shorter isoforms, which do not express the sequence of the extra peptide (EP, Figure 1a) in not possible.

• We have repeated the immunodepletion experiment and we now provide the results in Fig. 1f and Supplementary Fig. 1b. The western blot in Fig. 1f is now cleaner and supports quite convincingly the presence of a long SATB1 isoform. Given the lack of isoform-specific knockouts which we could utilize to immunoprecipitate or detect the different isoforms in a single cell (or cell population), the utilized approach of immunodepletion and subsequent western blotting is the approach we thought of implementing.

• As shown in Fig. 1f and Supplementary Figure 1b, the long isoform SATB1 antibody has the capacity to recognize the long isoform in murine thymocyte protein extracts but not the short SATB1 isoform (please compare lane 3 in the two western blots utilizing either the antibody for the long isoform -top panel - or the antibody that detects both isoforms (lower panel).

• We have performed Immunofluorescence experiments utilizing the antibody detecting the long SATB1 isoform in thymocytes isolated from either C57BL/6 or Satb1 cKO mice. The antibody is specific to the SATB1 protein since there is no signal in immunofluorescence experiments utilizing the knockout cells (Supplementary Figure 1c).

• We have performed Immunofluorescence experiments utilizing thymocytes and the antibody detecting the long SATB1 or a commercially available antibody detecting all SATB1 isoforms. The pattern of SATB1 subnuclear localization is similar for both antibodies (Supplementary Figure 1e).

• In our accompanying revised manuscript Zelenka et al., 2022 (https://doi.org/10.1101/2021.07.09.451769), we provide yet another piece of evidence, consisting of bacterially expressed short and long SATB1 protein isoforms detected by western blot using either the long isoform-specific or the non-selective all SATB1 isoforms antibodies.

• Regarding the additional bands detected in the immunoprecipitation experiment presented in the original Supplementary Figure 1b (lane 2), it is not surprising that additional bands appear in a sample of protein extracts that is used for several hours for the immunoprecipitation experiments, while the “input” sample simply denotes protein extract that is frozen at -80oC right after the preparation of protein extracts until use. It is well-established that SATB1 is the target of proteases which might as well be active during the immunoprecipitation steps (2 consecutive immunoprecipitation steps take place). Therefore, the immunoprecipitated material cannot necessarily be a copy of the input material displaying a single protein band even if protease inhibitors are included in the buffers.

Taken together the experiments described here we showed that the antibody raised against the extra 31 aa long peptide, present only in the long SATB1 isoform, is specific for this isoform.

1. Fig 4 Optodroplet experiment appears to show that the N-terminus of SATB1 can undergo LLPS. The results of this assay show that SATB1 has a domain that can undergo phase-separation in isolation, but it does not show that the protein itself is a phase-separating protein. The FRAP assay methods are not provided by the authors, but this is important, as continued light activation means proteins are continuously forming aggregates, and the bleaching for FRAP should be balanced with the levels of Cry2 activation. A very good description of the methods is described in the original Optodroplet paper: https://www.sciencedirect.com/science/article/pii/S009286741631666X?via%3Dihub#sec4

We should note that we did follow the FRAP protocol provided by the recommended study Shin et al., 2017 (https://doi.org/10.1016/j.cell.2016.11.054). Indeed, these experiments are very tricky to perform and interpret, as every cell expresses slightly different amounts of protein which is directly associated with the different speed of optoDroplet formation, and thus its propensity to aggregate upon overactivation. On the other hand, there need to be continuous activation during the FRAP experiment as the lack of activation laser would result in fast disassembly of the optoDroplets, counteracting the FRAP results. Moreover, the optoDroplets actively move around the cell in all dimensions which makes the accurate measurement of signal intensity really challenging, even with an adjusted pinhole. Therefore, we do not think that FRAP is the best approach to examine the behavior of optoDroplets.

Either way, we have now described the detailed FRAP protocol in Lines 889-898, which read: “For the FRAP experiments, cells were first globally activated by 488 nm Argon laser illumination (alongside with DPSS 561 nm laser illumination for mCherry detection) every 2 s for 180 s to reach a desirable supersaturation depth. Immediately after termination of the activation phase, light-induced clusters were bleached with a spot of ∼1.5 μm in diameter. The scanning speed was set to 1,000 Hz, bidirectionally (0.54 s / scan) and every time a selected point was photobleached for 300 ms. Fluorescence recovery was monitored in a series of 180 images while maintaining identical activation conditions used to induce clustering. Bleach point mean values were background subtracted and corrected for fluorescence loss using the intensity values from the entire cell. The data were then normalized to mean pre-bleach intensity and fitted with exponential recovery curve in Fiji or in frapplot package in R.”

1. Description of analyses that authors prefer not to carry out

**Reviewer #1**:

Can they use the all and long isoform antibodies together, then subtract the signal from long isoform to conclude about the localization of the shorth isoform ?

We thank the Reviewer for the suggestion, though given the differential efficiency of antibodies and other limitations of imaging experiments, we do not find the suggested experiment to have a potential to improve the quality of our manuscript. However, we should note that we have performed a pixel-based colocalization experiment between the signal detected by all isoform and long isoform SATB1 antibodies. Fluorocytogram of the pixel-based colocalization, based on 3D-SIM data is provided on the left, with quantified colocalization on the right of the revised Supplementary Fig. 5a.

3) Lack of better staining with antibody against the long and short SATB1 isoforms after treatment with 1,6 Hexanediol. 1,6 Hexanediol treatment can change many other chromatin associated proteins to which SATB1 can be bound to indirectly. This experiment can

We do understand the controversy and difficulties of experiments using 1,6-hexanediol treatment. However, we have to note that there is no better approach available for the investigation of LLPS in our primary murine T cells. We did use alternative approaches in ex vivo experiments, utilizing cell lines to validate our hypothesis without the involvement of 1,6-hexanediol.

**Reviewer #2**:

1. The authors mention, '...of the different SATB1 isoforms, uncovered by the use of the two different antibodies, relied in the heterochromatin areas (zone 1), where the long isoform was less frequently...' There is no supporting figure number mentioned. The authors need to show a zone-by-zone comparison images for 'all iso' vs 'long' iso of SATB1. Just to reiterate, there is a need for a heterochromatin mark to unambiguously call out the distinction.

We should remind that there is an inherent difficulty to accurately compare localization of short and long SATB1 isoforms in primary cells, especially due to the lack of Satb1 isoform-specific knockout mice. There is no way to detect only the short isoform in these primary cells as there are only antibodies targeting the long or all SATB1 isoforms. Therefore, we cannot set up additional experiments probing these questions.

In line with this, in the revised version of the manuscript, we toned down our statements regarding the differential localization of the two isoforms in primary cells. We only refer to it as an indication and we support it by adding references to the relevant figures. This part now reads: “Localization of SATB1 speckles detected by antibodies targeting all SATB1 isoforms and/or only the long SATB1 isoform, revealed a significant difference in the heterochromatin areas (zone 1, Fig. 2b), where the long isoform was less frequently present (see also Fig. 2a and Fig. 3c). Although, this could indicate a potential difference in localization between the two isoforms, due to the inherent difficulty to distinguish the two based on antibody staining, we refrain to draw any conclusions. (Lines 145-150)”

1. Fig. 6a, The authors wished to see the effect of RNA on Satb1 nuclear localization. This is not related to the main theme of the paper, thus should be moved to supplementary (true for b as well). Importantly, the experiments should be performed with total cells to show the divergence of localization (like the paper the authors referred to) instead of matrix for clarity.

• We did not wish to see the effect of RNA on SATB1 localization. In fact, there is a long history of SATB1 research that is inherently linked with the concept of nuclear matrix, a putative nuclear structure which is highly associated with nuclear RNAs. SATB1 was described many times as a nuclear matrix protein (https://doi.org/10.1016/0092-8674(92)90432-c; https://doi.org/10.1128/mcb.14.3.1852-1860.1994; https://doi.org/10.1074/jbc.272.17.11463; https://doi.org/10.1128/mcb.17.9.5275; https://doi.org/10.1021/bi971444j; https://doi.org/10.1083/jcb.141.2.335; https://doi.org/10.1101/gad.14.5.521; https://doi.org/10.1038/ng1146).

• Moreover, our data discussed in comments 4-7 of this Reviewer, such as i. the localization of SATB1 to the nuclear zones associated with RNA and nuclear scaffold factors (Fig. 2b, Supplementary Fig. 1c), ii. colocalization of SATB1 with actively transcribed RNAs (Fig. 2c, Fig. 3g, Supplementary Fig. 2a, Supplementary Fig. 2c), iii. including its association with nucleoli (Supplementary Fig. 3b), and also iv. its computationally predicted interaction with Xist lncRNA (Agostini et al., 2013; https://doi.org/10.1093/nar/gks968) as a notable factor of nuclear matrix, all suggest that the interaction between RNA and SATB1 is plausible and potentially relevant for its function and/or at least its subnuclear localization. It is relevant even more so, when considering numerous reports on the ability of RNA-binding, poly-Q and PrLD-containing proteins to undergo LLPS https://doi.org/10.1016/j.molcel.2015.08.018; https://doi.org/10.1042/bcj20160499; https://doi.org/10.1016/j.cell.2018.03.002; https://doi.org/10.1016/j.cell.2018.06.006; https://doi.org/10.1093/nar/gkaa681), including RNAs specifically regulating LLPS behavior, especially for poly-Q and PrLD-containing proteins, such as SATB1 (https://doi.org/10.1126/science.aar7366; https://doi.org/10.1126/science.aar7432; https://doi.org/10.1016/j.ceb.2019.03.007; https://doi.org/10.1038/s41598-020-57994-9; https://doi.org/10.1016/j.molcel.2015.09.017; https://doi.org/10.1038/s41598-019-48883-x; https://doi.org/10.1038/s41467-019-11241-6).

• It should also be noted that SAF and various hnRNPs, as the most prominent proteins of nuclear matrix were many times reported to phase separate (https://doi.org/10.1016/j.molcel.2019.10.001; https://doi.org/10.1074/jbc.ra118.005120; https://doi.org/10.1016/j.celrep.2019.12.080; https://doi.org/10.1038/s41467-019-09902-7; https://doi.org/10.1016/j.molcel.2017.12.022; https://doi.org/10.1074/jbc.tm118.001189). All these aspects show that the relation between nuclear matrix, SATB1 and RNA are quite relevant to our manuscript.

• Moreover, in light of the aforementioned information, we believe that it is much clearer to follow the protocol we did – i.e. to remove soluble proteins by CSK treatment and then, upon RNase treatment, extract the released proteins using ammonium sulfate. In an experiment utilizing whole cells, one would need to microinject RNase A into the nucleus, which 1. is very challenging for primary T cells having a radius of 3-5 micrometers, 2. is of low throughput, 3. would not allow for released protein removal which would thus make the results hard to interpret. Please note that in the reference paper, the authors used cell lines overexpressing heterologous GFP-tagged proteins, which is not related to our setup.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Reply to the Reviewers

I thank the Referees for their...

Referee #1

1. The authors should provide more information when...

Responses + The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A). + Though this is not stated in the MS 2. Figure 6: Why has only...

Response: We expanded the comparison

Minor comments:

1. The text contains several...

Response: We added...

Referee #2

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Zelenka et al., focus on a T cell genome-organizing protein, SATB1, to show that SATB1 undergoes liquid liquid phase-separation (LLPS), and distinct isoforms confer different LLPS-related biophysical properties. They generate a long-isoform specific antibody and conduct several experiments to test for LLPS and compare LLPS properties between the long-isoform relative to the whole SATB1 protein population. Given that SATB1 plays important roles in T cell development and in cancer, interrogating SATB1 biophysical properties is an important question. However, there are multiple problems with the experimental setup and data that weaken their support of the conclusions.

I will detail some of the major issues below:

Regarding phase-separation There are several assays to determine whether a protein undergoes LLPS.

1. One of the first the authors address is the spherocity or roundness. Indeed, formation of spherical droplets is one evidence of the liquid nature of a protein. However, the authors use fixed preparations (which can introduce artifacts), not free-floating protein, and determine roundness by showing a 2D image. Roundness should take into account the diffraction-limits of fluorescent imaging, as many structures can be imaged to appear round by the detector. There are quantifiable measurements that can be taken on 3D images to show roundness. This would best be shown using non-fixed protein.
2. Hexanediol is another assay frequently used in phase-separation studies. However, hexanediol has many deleterious effects on the cell, even at a fraction of the concentration normally used in phase-separation studies. Authors should show controls of cell viability, control proteins that do not phase-separate, etc. See https://www.jbc.org/article/S0021-9258(21)00027-2/fulltext. Secondly, hexanediol treatment should cause phase-separated protein aggregates to disperse. It is difficult to determine from the images whether or not the aggregates actually disperse or there is just less protein. In any case, small aggregates remain even after treatment, and this appears different from most other hexanediol experiments reported in the literature where the signals become more dispersed and uniform. This is likely because the samples are fixed. One of the main features of using hexanediol in phase-separation is to show that upon washout, LLPS aggregates can reform. Because the cells are fixed, the critical aspect of this assay is not performed. A washout and LLPS recovery would control for cell viability issues described above and would provide the opportunity to show that total SATB1 protein levels did not change, but its distribution did, which is the essence of this assay in the context of LLPS.

This review from the Tjian group is very informative and may be a good resource: http://genesdev.cshlp.org/content/33/23-24/1619

Regarding the isoform specificity of SATB1 biophysical properties

1. The authors generate a long isoform-specific antibody. However, the western blot is not convincing that this is indeed specific to the long isoform as there is a rather large smear. Can this be improved with antibody preabsorption? Since this is a key reagent for the manuscript, improvement in antibody quality is essential.
2. Fig 4 Optodroplet experiment appears to show that the N-terminus of SATB1 can undergo LLPS. The results of this assay show that SATB1 has a domain that can undergo phase-separation in isolation, but it does not show that the protein itself is a phase-separating protein. The FRAP assay methods are not provided by the authors, but this is important, as continued light activation means proteins are continuously forming aggregates, and the bleaching for FRAP should be balanced with the levels of Cry2 activation. A very good description of the methods is described in the original Optodroplet paper: https://www.sciencedirect.com/science/article/pii/S009286741631666X?via%3Dihub#sec4
3. The major difference between the long and short isoform of SATB1 is the 31aa segment within the IDR. However the authors find that neither the long or short isoform SATB1 forms LLPS aggregates, and the IDR alone forms aggregates in the cytoplasm (Fig5) but they do not respond to Cry2 light activation. When forced to localize to the nucleus, it does not form aggregates as well (Fig6). The short isoform also did not form any aggregates. These results seem to argue against any isoform specific phase-separation. This experiment seems critical for the story, yet it does not support their overall conclusions. The authors might consider using a different cell line or perhaps do an in vitro assay using purified protein. I am not certain what to make of the cytoplasmic aggregation, which appears to not form upon localization to the nucleus. Because of this, it is difficult to place weight on the significance of the S635A mutation and the role that a phosphorylation of SATB1 contributes to phase-separation, let alone function.

There are many additional points of concern, but the ones listed above are perhaps the most significant in terms of the overall conclusions of the paper.

Significance

If convincingly demonstrated, it can advance the field by understanding how SATB1 functions. However, the data are premature to relate SATB1 to the phase separation field. Audience interested in gene regulation and phase separation would pay attention to this paper, if successfully prepared.

The field of expertise is phase separation, development, regulation of gene expression.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors have reported the existence of a 'long' SATB1 isoform which also undergoes LLPS. The authors tried to draw multiple comparisons and pointed out distinction between phase properties of SATB1 isoforms. The authors also touch upon two functional roles of SATB1. Although a wide array of assays are used, the data presented and hence the manuscript makes multiple transitions into disparate hypotheses without diving deep into a single hypothesis. As a result, the connections drawn are unclear, and do not converge at best. The authors have used number of techniques, however, the results do not support their conclusions and they appear hastily drawn. It is not clear why the authors jump from one context to the other, discussing LLPS first, then transcription, splicing, post-translational modification and finally cancer. The link between all of these isn't clear and not fully supported by data. It appears that the authors wish to focus on Satb1's physiological role in development, hence the data on breast cancer is confusing. Thus, this work suffers from multiple pitfalls. Specific comments are given below:

Major comments

1. Importantly, in Fig 1d, there is no statistics shown. There is no mention of number of replicates as well in the legends. Proper statistical evaluation is critical for interpreting this result.
2. Figure 1f presents one of the weakest evidences in the manuscript. There are a number of corrections needed. Firstly, being their major and only validation figure for their custom antibody, the immunoblot is not clean, bands are fuzzy. Importantly, as the authors claim that the antibody is highly specific to 'long' SATB1, after the IP there should be only a single band (like input) of Satb1 long. But that does not seem to be the case, rather an array of bands are visible below (lane 2 top panel). This could easily mean that the shorter isoforms or non-specific protein bands are also pulled down with the 'long' form specific antibody. Therefore, raising a critical concern regarding the specificity of the antibody.
3. Moreover, an important and direct experiment would be to clone the long isoform in a suitable vector and overexpress in the cell line (as done for the canonical isoform in Supp Fig 1a). This would unequivocally show the efficacy of the antibody and thus the following usage of the same for various assays.
4. Related to Fig. 2 a, the authors state on Pg 5, '....the euchromatin and interchromatin regions (zones 3 & 4, Fig. 2a, b).' Although the DAPI correlation seems clear, there is no mention on how they reached the above said correlation. They should at least show a parallel speckle staining for HP1 or signature modification such as H3K4me9 STEDs for making supporting such a claim. DAPI alone is not sufficient. The authors should rectify the text thoroughly for many such interpretations without validation/reference or provide relevant data.
5. The authors mention, '...of the different SATB1 isoforms, uncovered by the use of the two different antibodies, relied in the heterochromatin areas (zone 1), where the long isoform was less frequently...' There is no supporting figure number mentioned. The authors need to show a zone-by-zone comparison images for 'all iso' vs 'long' iso of SATB1. Just to reiterate, there is a need for a heterochromatin mark to unambiguously call out the distinction.
6. On the same lines, '....Given the localization of SATB1 to the nuclear zones with estimated transcriptional activity (Fig. 2b, zone 3)....' How was the region labelled as transcriptionally active? For the statistical analysis of speckle count for the two antibodies' staining, the claim posited is a bit bigger. This could simply be true for that cell. The authors thus need to statistically analyse the speckle counts for multiple cells. This needs to be done for all imaging statistics done in multiple figures throughout the manuscript.
7. For figure 2c. the authors have used 5 Fluorouridine for nascent RNA speckles. 5FU is known to have a spread signal type (with strong association to nucleolus as well). This is not the case for the image presented 2c. The authors should resolve this by showing different sets of images.
8. Fig 2 d., the authors have suddenly jumped solely to 'all iso' Satb1 here for IP MS. Is there a reason for that? The authors either need to do this with 'long iso' antibody or remove the analysis from the manuscript as it does not add to their primary aim of the manuscript. Also, the authors have only selectively talked about two clusters? What about chromatin related proteins? It is quite intuitive to have highest enrichment of these given previous literature and even IP MS data by other groups. Thus, it is necessary to revise this thoroughly or remove it.
9. In relation to Fig. 2f, the authors have not mentioned any of the previously published work on Satb1 CD4 specific KO, not even the RNA seq studies the other groups have reported under the same condition. Only an unpublished reference of their own (preprint) is cited. It is imperative to show how much their data corroborates with other published studies. Additionally, what is the binding site status of dysregulated genes?
10. In context of Figure 3a and b, the authors write .'...The long SATB1 isoform speckles evinced such sensitivity as demonstrated by a titration series with increasing concentrations of 1,6-hexanediol treatment followed...' Whereas it is apparent from the image at least that overall numbers of individual speckles are instead increased at both 2 and 5%. There is although a clear spreading of restricted speckles compared to the controls. The authors should revise their figures to substantiate the associated text. Furthermore, there needs to be 'all iso' SATB1 3D SIM imaging and not just quantitation for comparison. This is also true for panel c in order to demonstrate the effect.
11. Fig. 3 d also does not clearly demonstrate what the authors have claimed '...hexanediol treatment highly decreased colocalization between...' The figure shows at best decreased signal intensity for both SATB1 and FU. We suggest that the authors should give a statistical analysis as well for the colocalization points between the two using multiple source images. Lastly, the two images shown (control and treated), there seems to be a clearly visible magnification difference. The authors should clarify this.
12. Figure 3f. The authors show the PC plot for Raman spectroscopy for phase behaviour due to Satb1. The experiment and its related text seems misinterpreted; the authors write...' ese bonds were probably enriched for weak interactions responsible for LLPS that are susceptible to hexanediol treatment. This shifted the cluster of WT treated cells towards the Satb1 cKO cells. However, the remaining covalent bonds differentiated the WT samples from Satb1 cKO cells......' whereas the clusters are clearly far away in 3D for both WT and KO while being closer to their respective treatments. Which is also intuitive given the sensitivity of Raman spectroscopy. Thus, it is more likely to be treatment effect and KO effect as separate. Treatment of WT leads to KO like spectra is far-fetched. Thus, the authors need to show separate PCs and modify their text thoroughly.
13. In Fig 4. b, The authors have shown the propensity of SATB1 N terminus to phase separate using different optodroplet constructs. Although the imaging is clear, why are the regions selected not uniform when comparing various constructs?
14. Figure 5a, the disassembly should be shown for 'long' SATB1 as well. On pg 13, the authors write '....cytoplasmic protein aggregation has been previously described for proteins containing poly-Q domains and PrLDs..' no reference given.
15. Fig. 5d, Is there an amino-acid specific reasoning to support the authors claim of the phase behaviour due to extra peptide? They need to show a proper control with equal extra (unrelated) peptide to show the specificity. Are the shorter isoform aggregates responsive to light?
16. Fig. 6a, The authors wished to see the effect of RNA on Satb1 nuclear localization. This is not related to the main theme of the paper, thus should be moved to supplementary (true for b as well). Importantly, the experiments should be performed with total cells to show the divergence of localization (like the paper the authors referred to) instead of matrix for clarity.
17. Fig 6c., It is important that authors show the data for NLS+short iso data as well to prove their hypothesis.
18. Fig 6d., The authors claim that mutating a specific P site changes the phase behaviour of the 'short iso'. Does it also increase for the long isoform? The authors need to confirm this in order to verify the effect of a single P site outside of oligomerization domain. ...' phosphorylation status; when phosphorylated it remains diffused, whereas unphosphorylated SATB1 is localized to PML bodies....' This being an important premise, thus should be moved to the results text.
19. Pg 16,. The authors have tried to explain multiple things (concepts of self-regulation, accessibility) which is quite tangential. There is no inference to Fig 6f., which is showing the opposite to what the authors had postulated. This portion should either be removed or explained with a rationale. The writing also needs to be revised thoroughly in this section. Similarly, the discussion should also be modified.
20. The authors should not draw conclusions based on any data which is not shown '....ed differences in chromatin accessibility at the extra exon of the SATB1 gene (data not shown), suggesting its potential involvement in alternative splicing regulation according to the "kinetic coupling" model...'. This has led to overspeculation and needs correction.

Minor comments:

1. On pg 4, the authors state 'Here, we utilized primary murine T cells, in which we have identified two full-length SATB1 protein isoforms.' Whereas only one 'long' isoform is identified and the other is the canonical version. The authors should correct the statement.
2. On pg 6, related to Figure 1, the authors mention 'It should also be noted that when investigating the SATB1 protein levels, we have to bear in mind that the antibodies targeting the N-terminus of SATB1 protein cannot discriminate between the short and long isoforms'. The authors reason that their sizes are too close. It is indeed possible, and widely studied in biochemistry to assess various factors on protein migration (such as PTMs). The authors should validate this aspect (as it is important as per their premise) and perform separation based on charge as well and also use a commercial antibody to validate the same.
3. Fig. 1 a , Is there a specific reason to generate a custom-made antibody for 'all' SATB1, using similar regions that are already commercially available. This becomes redundant otherwise, because there is no apparent difference in detection compared to the commercial one (Suppl. Fig 1a). Antibody generation strategy (1a) should be moved to supplementary. Additionally, authors have obtained the custom antibodies from a commercial source, therefore, the text should reflect the same alongside relevant details.
4. Fig 3e: what is the control used here? In their Pearson correlation analysis, there seem to be significant reduction in control sets as well upon treatment. This needs to be clarified.
5. Pg 10, the authors claim that '..., thus we reasoned that it may also be used to study phase separation...' But there have been numerous reports starting from 2018, which have utilized this technique in corelation to phase behaviour (albeit individual proteins). The authors should include proper citations as they are extending an idea from the same field to their specific need.
6. For Fig 5b, there should be a comparative image for 'short' isoform.
7. In the context of Figure 5c, the authors claim ...' Note also the higher LLPS propensity of the human long SATB1 isoform compared to the murine SATB1...' Why suddenly human and mouse comparisons are drawn? This figure should be moved to supplementary.

Significance

The authors have made a few novel observations such as the existence of a 'long' isoform of Satb1 with an additional exon, formation of LLPS by this isoform. This study has the potential to be of relevance to the T cell development and transcription regulation community. However, the authors fall short of building a convincing case to this effect. This is primarily due to the fact that they have focused on diverse assays to collect data but not converged on a unique theme. Further, the authors have not mentioned any of the previously published work on Satb1 CD4 specific knockouts, not even the RNAseq studies the other groups have reported under the same conditions. Satb1 knockout model could have been used more effectively to convincingly demonstrate the role/s of the two Satb1 isoforms in T cell development and function.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

This paper looks at in important nuclear matrix protein SATB1, which is a well known global chromatin organizer and help chromatin loop attach to the nuclear matrix. The paper starts with identification of novel short and long form of SATB1. Both the isoform consist of a prion like low complexity domains, but the long isoform additionally contain an extra EPF domain next the Prion like low complexity domain. The paper reports that in murine cells the long isoform is 3-4 fold more abundant than the short isoform. By using STED microscopy they show SATB1 foci lie next to transcription sites in the nucleus. They conclude by looking at the spherical shape of the SATB1 foci and the susceptibility of SATB1 staining after 1,6 hexanediol treatment that SATB1 forms the small foci in the nucleus due to LLPS. The authors also use RAMAN spectroscopy to conclude a change in nuclear chemical space in absence of SATB1 but without much explanation about which chemical bond or nuclear sub structure change correspond to the change in principal component analysis from Raman spectroscopy. The authors use the light inducible aggregation cyr2 tag with the PrD domain of SATB1 and compare it with the Cry2-FUS-LC domain to conclude that the SATB1 LC domain can undergo LLPS. The authors hint at involvement of RNA and also DNA in the LLPS of the SATB1 but without going into any detail.

The key conclusions of the paper are- A) SATB1 undergoes LLPS. But this conclusion is drawn after correlative experiments as detailed below-

1. observation of spherical punctae by STED-which could also seem spherical due to their small size. The resolution limit achieved by the STED microscopy used in this paper is not determined or mentioned clearly.
2. No live cell FRAP experiment with fluorescent SATB1 long or short isoform to show that these foci are liquid like
3. Lack of better staining with antibody against the long and short SATB1 isoforms after treatment with 1,6 Hexanediol. 1, 6 Hexanediol treatment can change many other chromatin associated proteins to which SATB1 can be bound to indirectly. This experiment can
4. Lack of in vitro reconstitution experiments with purified long and short SATB1
5. LLPS is strongly coupled to the cellular concentration of the proteins. Authors should quantify the cellular concentration of the long and short isoform in the cells.

Major conclusion B)- SATB1 regulates transcription and splicing.

This was also shown previously and in this paper they show the close proximity of the transcription site and SATB1 foci by microscopy. Hexanediol tretamnt which lead to loss of colocalization between FU foci and SATB1 is also taken as an evidence in regulation of transcription is not right as the transcription foci itself can be dissolved using 1,6 Hexanediol. Although the rate of transcription is not measured quantitatively.

Major conclusion C)-Post transcriptional modification is important for SATB1 function.

This point is just barely touched upon in the last figure of the paper

Overall I find that the major conclusion-point A and B , is based on very indirect experiments and needs much more convincing data and the role of SATB1 LLPS in cells should be demonstrated more rigorously. And conclusion C is barely described and needs a lot more cell biological and genetic evidence.

I do not recommend publishing the paper in current state. The story needs much more experiment to convincingly prove the major conclusions. Further, the MS needs more careful thinking and presentation to make it streamlined.

Minor comments:

One of the major flaw of the paper is the use too many techniques without proper explanation. E.g. use of STED and RAMAN microscopy need controls and explanation on what is being quantified. The use of Raman microscopy to quantify the nuclear environment of nucleus is not related to the chromatin organization or LLPS of SATB1 at all. And no information is provided at all which aspect of nuclear organization is being measured in Raman and what it means for the LLPS of SATB1.

Similarly for Hexanediol treatment, duration of treatment is missing. Hexanediol can also dissolve the liquid like transcription foci. And hence a decrease in correlation between SATB1 foci and FU foci cannot be taken as a measure of SATB1 foci connection to transcription alone

It is not very clear how many times the STED or Raman microscopy is done on how many samples and biological replicates. Similarly for RNA sequencing number of samples and description of controls are missing. Also if the sequencing data is made publicly available is not clear.

Can they use the all and long isoform antibodies together, then subtract the signal from long isoform to conclude about the localization of the shorth isoform ?

Additional control is needed to report the resolution limit of Superresolution techniques-STED and 3D-SIM systems used by them.

Would be very helpful if the zonation was plotted for the FluoroUridine(FU) also to show that Zone1 (heterochromatin) is completely depleted of FU, and is present in other regions.

Scale bar needed figure 3d

Perfectly rounded SATB1 foci- this does not mean LLPS. For LLPs measurement, protein condensate dynamics measurement by FRAP or fusion experiments is required. What is the size of condensates? and cellular concentration of SATB1 ? Will SATB1 undergo LLPS in vitro at similar concentrations? does SATB1 interact with DNA or RNA to undergo LLPS ?

After careful reading of the MS I conclude that the main conclusions of the paper are very preliminary and need much more detailed experiments. So does not qualify to get published at all at this stage.

Significance

The present manuscript tries to connect the phase separation of SATB1 to understanding the mechanism of SATB1 function in cells. One of the major hallmarks of phase separation is dynamic, liquid-like behaviour and in absence of these measurements, it is very difficult to say that the current manuscript has made any contribution to showing that SATB1 can phase separate.

The presence of 2 isoforms of SATB1 is a novel finding and the paper could have focussed more on this. E.g. elucidate expression of the isoform during thymocyte development and maturation.

As a reviewer my expertise are cell biology experiments, microscopy, in vitro reconstitution assays, RNA binding proteins, RNA and RBP condensate formation. And I feel that the reconstitution experiments are an important tool for understanding phase behaviour of proteins and also to gauge if this behaviour can occur or not in cellular concentration and conditions. I do not have sufficient expertise in Raman microscopy and hence the information provided in the MS on this part was not enough to understand the experiment and conclusions drawn from it.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

The manuscript describes the formation of supernumerary centriole protein assemblies ("cenpas") upon silencing of the E3 ubiquitin ligase TRIM37. These "cenpas" resemble centrioles, centriole precursors, or electron-dense striped structures, termed "tigers". Similar observations are made in cells from patients lacking functional alleles of TRIM37. The "cenpas" usually lack the full complement of centriolar proteins, but contain increased amounts of the pro-centriole marker centrobin. It is further shown that the formation of "cenpas" depends on centrobin, or on a parallel pathway involving Plk1 and SAS-6. Overall, the experiments in this study are of high technical quality and most of them are carefully controlled. The discovery of centrobin-containing striped protein assemblies ("tigers") is very interesting and provokes the question of their molecular composition and their mechanistic role in centriole assembly. Since striated fibres containing the protein rootletin have a similar periodicity of stripes (75nm) as the "tigers" in this study (Vlijm et al., PNAS 2018, 115:E2246-53), I was wondering whether the authors couldn't simply test for colocalization of their "tiger"-stripes with rootletin. A potential identity of "tigers" with striated fibres would help understanding the mechanisms of "cenpas" and centriole assembly upon depletion of TRIM37: striated fibres or "tigers" might be controlling the balance of centriole cohesion vs. disengagement and thereby centriole duplication, or they might play a role in the recruitment of additional proteins involved in pro-centriole assembly.

We are grateful to the reviewer for this interesting suggestion. Accordingly, we will test the distribution of Rootletin and potentially CEP68 by immunofluorescence analysis of cells depleted of TRIM37.

In the same context, did the authors correct for the experimentally induced sample expansion in Figure 5B, when comparing inter-stripe distances between U-ExM and EM samples?

Yes, we did. We will clarify the text of the revised manuscript to make this more explicit.

Other major points: The amount of TRIM37-depletion upon siRNA-treatment should be indicated prominently. I see in the "Materials and Methods" and in Fig. S4 that quantitative RT-PCR has been performed. Could Western blotting be performed to have direct information on the protein levels? Fig. 2C demonstrates that this is possible in cells from human patients, so why are there no data on the majority of other experiments in this manuscript?

We previously reported Western blot analysis to estimate the extent of TRIM37 depletion upon siRNA treatment (Balestra et aI., 2013). However, following the suggestion of the reviewer, we will repeat this analysis for select experiments of this study.

Moreover, what is the transfection efficiency in the siRNA experiments? Is there variability between cells that might explain variability in the "cenpas" phenotypes?

The reviewer brings up an interesting point. However, in the absence of an antibody to detect endogenous TRIM37 by immunofluorescence analysis, we cannot provide an accurate figure in this case. We will mention this limitation explicitly in the text of the revised manuscript.

Minor point: In line 353 (page 12), it is stated that centrobin in si-TRIM37 cells migrates slower (Fig. 4D), suggesting that TRIM37 regulates the post-translational state of centrobin. It looks to me as if the corresponding gel in Fig. 4D was "smiling" (see curvature of centrobin in the neighboring lane). I think that the authors should tone down their statement, or replace Fig. 4D with a more convincing image.

We thank the reviewer for having noticed this. We will provide another gel that is not “smiling” -the difference in migration has been observed in a reproducible manner.

Reviewer #1 (Significance):

The findings of this manuscript are highly significant for our understanding of centriole biogenesis. They should be of interest to a large community of cell biologists working on mitosis and on the centrosome, and they are of further importance for biomedical research related to developmental growth abnormalities (Mulibrey nanism). The manuscript shows for the first time a mechanistic link between TRIM37-dependent control of centrobin protein levels, and their impact on the formation of centriole precursors during the cell cycle. The manuscript is well presented, and the relevant scientific literature is cited correctly. However, I would prefer that a potential relationship between "cenpas", "tigers", and the welldescribed rootletin-containing striated fibres be discussed, if not controlled by additional experiments.

We thank the reviewer for her/his appreciation of our work and support for publication.

Field of expertise of this reviewer: centrosome, microtubules, mitosis, cell culture, light and electron microscopy, biochemistry.

Reviewer #2 (Evidence, reproducibility and clarity):

In this work, the authors investigated roles of TRIM37 in regulation of centriole numbers. It was previously observed that depletion of TRIM37 results in supernumerary centrioles and centriole-like structures (Balestra et al., Dev. Cell, 2013; Meitinger et. al., 2016). Here, the authors characterized these centriolar protein assemblies (Cenpas). Cenpas were formed, following an atypical de novo pathway and eventually trigger centriole assembly. They observed that Centrobin is frequently present in Cenpas from the early stage and other centriolar components are sequentially recruited. Furthermore, they established that Cenpas formation upon TRIM37 depletion requires PLK4 activity. TRIM37 depletion also activates PLK1-dependent centriole multiplication. 1.They propose that the tiger structure acts as platform for PLK4-dependent Cenpas assembly. Cenpas may evolve into centriole-like structures after a stepwise incorporation of other centriolar proteins. Fig. 6E suggests that a series of events seem to occur within G2 phase. Therefore, this reviewer suggests to perform a detailed time-course experiments at G2 phase. According to the model, the Centrobin-positive tiger structures may appear first, and then a Centrobin- and centrin-2-double positive structure starts to appear.

We fully agree with the reviewer that this is an important experiment, which we will perform by analyzing TRIM37 depleted cells at successive time points after release from a double thymidine block, using antibodies against Centrobin and Centrin.

2.They claim that Mulibrey patient cells exhibited evidence of chromosome mis-segregation, as would be expected from multipolar spindle assembly, and conclude that Cenpas are present and active also in Mulibrey patient cells. Chromosome mis-segregation may be observed in the normal cells, too. Therefore, they have to perform statistical analysis on Fig. 2D.

In response to this suggestion and to the related comment of reviewer 3 (see below), we will conduct additional immunofluorescence analysis and quantification of patient and normal cells, assessing the distribution of Centrin, Centrobin, microtubules and γ-tubulin, as well as scoring the extent of chromosome mis-segregation.

3.In Fig. 2A, They claimed that mitotic microtubules were disrupted with the cold treatment for 30 min. In our experience, cold treatment for 30 min is not sufficient to disrupt mitotic microtubules. They may show control panel before microtubule regrowth.

We will show the control panel as requested.

Reviewer #2 (Significance):

Significance of this work resides in identification and description of Cenpas as a novel centriole assembly pathway. The authors used cutting-edge microscopy techniques to visualize Cenpas. The manuscript raised more questions than answers. Nonetheless, it is worth to publish the manuscript after revision.

We thank the reviewer for supporting publication after revision.

Reviewer #3 (Evidence, reproducibility and clarity):

Balestra and colleagues investigate the function of Trim 37 in centrosome biogenesis. Trim 37 is a ubiquitin ligase that has previously been identified by the authors as a regulator of centriole duplication. Mutations in Trim37 cause a rare syndrome named Mulibrey that is responsible for a severe form of dwarphism Here they show that depletion of Trim37 in human cells results in the assembly of structures that they name Cenpas. They follow the possibility that Trim37 localises to the centrosome, which might inhibit the assembly of these structures. Further they show that Trim37 depleted cells (or in patient fibroblasts ) assemble multipolar mitosis. Further analysis shows that what the authors defined as abnormal centriole structures are formed in Trim37 depleted cells. These structures recruit centrobin, a daughter centriole component and this process requires the activity of PLK4 and PLK1. Major comments: This study characterizes Trim37 and its possible role in centriole biogenesis. Most conclusions are convincing, although some of the claims taken by the authors might require more data to be corroborated.

1)The major point to be taken into consideration in my opinion relates with the Cenpas structure. According to the beautiful cryo-EM data shown on Fig 3, I wonder why the authors describe these structures as centriole like- or centriole related. I think these appear very different from centrioles and this might be even quite interesting if these structures nucleate microtubules and can participate in mitotic spindle assembly.

We have a different opinion on this point. Most of the “centriole-like” or “centriole-related” structures do resemble the organelle, in that they contain microtubule bundles and are of a related size (in addition to bearing centriolar markers). However, recognizing that the distinction between these two categories of structures is somewhat arbitrary, we will combine them into the most prudent term “centriole-related”, and further explain in the revised manuscript that they comprise a range of structures.

The authors correlate these non-canonical centriole structures as possible microtubule nucleators that might be responsible for multipolar configurations like in Fig 2D. This correlation has to be established. In Figure 2D, the authors analyze configurations of mitotic cells in terms of centrosome number and characterized frequency of extra foci. To me the foci they show are quite different in nature. Poles 1 and 3 have both centrin and g-tubulin (presumably centrioles), pole 2 has only a tiny amount of centrin and no g-tubulin, while pole 4 appears to contain both but less of each protein. So the question is are they all nucleating microtubules and participating in spindle assembly? This is particularly important in light of what the authors then mention, which is the occurrence of chromosome mis-segreation in patient cells (this is not shown). Also they describe these extra poles, and then say that Cenpas are active in patient cells. But, active in which manner? By nucleating microtubules? First, in either siRNA cells or in patient cells the authors should analyze microtubules and show that all the extra poles (made of non-canonical centriole) nucleate microtubules and participate in spindle assembly.

In response to this suggestion and to the related comment of reviewer 2 (see above), we will conduct additional immunofluorescence analysis and quantification of patient and normal cells, assessing the distribution of Centrin, Centrobin, microtubules and γ-tubulin, as well as scoring the extent of chromosome mis-segregation.

If they want to propose that this might be the cause of genome integrity loss in patients (as stated in the abstract and suggested a few times throughout the paper) they have to show that cells divide abnormally and generate aneuploidy progeny.

See response just above.

2) Another important point that is only partially addresses is the function of Trim37 in stabilizing centrobin. Does Trim37 ubiquitinates centrobin? While the western blot on Figure 4 shows an increase at 8hrs in Trim37 RNAi, this is also the case for tubulin (Fig 4E). But the overall levels appear only slightly increased when compared to its levels at time point zero (Fig. 4F). I can see that in siRNA Ctrl Trim 37 levels go down, but it is still present so how do they explain the lack of Cenpas in this case? Is there a threshold that supports centriole duplication without any major defect but accumulation of a certain level of centrobin then generates Cenpas? Can the authors generate Cenpas just by over-expressing centrobin directly?

It appears from the comment of the reviewer that we were not sufficiently clear here. The experiment reported in Figure 4E and 4F is done in the presence of cycloheximide to analyze the half-life of Centrobin in control conditions and upon TRIM37 depletion. We will clarify the text in the revised manuscript to facilitate understanding.

In Figure 2, they analyze configurations of mitotic cells in terms of centrosome number and characterized frequency of extra foci. To me the foci they show are quite different in nature. Poles 1 and 3 have both centrin and g-tubulin (presumably centrioles), pole 2 has only a tiny mount of centrin and no g-tubulin, while pole 4 appears to contain both but less of each protein. So the question is are they all nucleating microtubules and participating in spindle assembly? This is particularly important in light of what the authors then mention, which is the occurrence of chromosome mis-segreation in patient cells without showing it. Also they describe these extra poles, and then say that Cenpas are active in patient cells. But, active in which manner? By nucleating microtubules? This has to be shown. Also analysis of mitosis should be included to back up a defect in chromosome segregation and also to identify which type of defect.

The above section is a copy/paste mistake (as indicated also in a correspondence between Review Commons and the reviewer).

So in conclusion, the link between Cenpas and multipolarity has to be better investigated in my opinion. This should not be time consuming and also not extremely costly. Authors should label spindle MTs in patient fibroblasts to show that indeed Cenpas are nucleating microtubules. Ideally Cenpas would be distinguished by centrobin labeling. In siRNA depleted cells maybe time lapse microscopy can be used to image mitosis and show a correlation between Cenpas and multipolarity?

As mentioned above, we will conduct additional immunofluorescence analysis and quantification of patient and normal cells, assessing the distribution of Centrin, Centrobin, microtubules and γ-tubulin, as well as scoring the extent of chromosome mis-segregation.

The data is presented without statistical analysis on the figures only on Fig legends, This is really difficult for the reader. The number of experiments and cells analyzed maybe should be also included in each Figure.

We had kept this information to the legends merely to have lean figures, but will consider moving it to the figure panels in the revised manuscript.

Minor comments: Some picture lack scale bars

Apologies. This will be fixed.

the localization of GFP-Trim37. On Figure 1 the authors describe a different localization when fused to a NES localization. It is true that a dotty signal is seen on the panel of NES (Figure 1D), but a nuclear signal is not seen on Trim-GFP in any of the images provided. Shouldn't this be the case?

There is some GFP-TRIM37 nuclear signal in the left panel of Figure 1D, although it is very weak. We will explore the possibility of providing an inset with adjusted brightness/contrast to emphasize this point.

Fig 1C is missing a siCtrl.

The control quantification will be included (no extra centrioles are present in this case).

Why Trim37GFP does not rescue completely the assembly of the extra foci?

In general, there can be many reasons why rescue in such an experimental setting is not complete, including slightly different protein levels, distribution, or interaction with partner proteins. Such possibilities will be discussed explicitly in the revised manuscript.

In Fig 6E, are the authors sure that in the condition of siTRim3 plus si Centrobin and Plk1 inhibition, cells are not stuck in S-phase? This might explain the lack of being in a permissive G2 phase to generate Cenpas?

Although Plk1 inhibition is not expected to block cells in S phase, we cannot rule out this possibility from the data currently available. Therefore, we plan to conduct FACS analysis in a repeat of this experiment to assess cell cycle status.

The data is presented without statistical analysis on the figures. This can be found on figure legends, but it is better to include on the figures to facilitate the reader's job. The number of experiments and cells analyzed maybe should be also included in each Figure?

As mentioned above also, we had kept this information to the legends merely to have lean figures, but will consider moving it to the figure panels in the revised manuscript.

Reviewer #3 (Significance):

Interesting findings and quite novel since a role for Trim 37 in centriole biogenesis has never been reported. Also quite interesting the possible link between multipolarity (needs better characterization) and Mulibrey syndrome.

We thank the reviewer for recognizing the interest and novelty of our work

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Balestra and colleagues investigate the function of Trim 37 in centrosome biogenesis. Trim 37 is a ubiquitin ligase that has previously been identified by the authors as a regulator of centriole duplication. Mutations in Trim37 cause a rare syndrome named Mulibrey that is responsible for a severe form of dwarphism Here they show that depletion of Trim37 in human cells results in the assembly of structures that they name Cenpas. They follow the possibility that Trim37 localises to the centrosome, which might inhibit the assembly of these structures. Further they show that Trim37 depleted cells (or in patient fibroblasts ) assemble multipolar mitosis. Further analysis shows that what the authors defined as abnormal centriole structures are formed in Trim37 depleted cells. These structures recruit centrobin, a daughter centriole component and this process requires the activity of PLK4 and PLK1.

Major comments:

This study characterizes Trim37 and its possible role in centriole biogenesis. Most conclusions are convincing, although some of the claims taken by the authors might require more data to be corroborated.

1. The major point to be taken into consideration in my opinion relates with the Cenpas structure. According to the beautiful cryo-EM data shown on Fig 3, I wonder why the authors describe these structures as centriole like- or centriole related. I think these appear very different from centrioles and this might be even quite interesting if these structures nucleate microtubules and can participate in mitotic spindle assembly. The authors correlate these non-canonical centriole structures as possible microtubule nucleators that might be responsible for multipolar configurations like in Fig 2D. This correlation has to be established. In Figure 2D, the authors analyze configurations of mitotic cells in terms of centrosome number and characterized frequency of extra foci. To me the foci they show are quite different in nature. Poles 1 and 3 have both centrin and g-tubulin (presumably centrioles), pole 2 has only a tiny amount of centrin and no g-tubulin, while pole 4 appears to contain both but less of each protein. So the question is are they all nucleating microtubules and participating in spindle assembly? This is particularly important in light of what the authors then mention, which is the occurrence of chromosome mis-segreation in patient cells (this is not shown). Also they describe these extra poles, and then say that Cenpas are active in patient cells. But, active in which manner? By nucleating microtubules? First, in either siRNA cells or in patient cells the authors should analyze microtubules and show that all the extra poles (made of non-canonical centriole) nucleate microtubules and participate in spindle assembly. If they want to propose that this might be the cause of genome integrity loss in patients (as stated in the abstract and suggested a few times throughout the paper) they have to show that cells divide abnormally and generate aneuploidy progeny.
2. Another important point that is only partially addresses is the function of Trim37 in stabilizing centrobin. Does Trim37 ubiquitinates centrobin? While the western blot on Figure 4 shows an increase at 8hrs in Trim37 RNAi, this is also the case for tubulin (Fig 4E). But the overall levels appear only slightly increased when compared to its levels at time point zero (Fig. 4F). I can see that in siRNA Ctrl Trim 37 levels go down, but it is still present so how do they explain the lack of Cenpas in this case? Is there a threshold that supports centriole duplication without any major defect but accumulation of a certain level of centrobin then generates Cenpas? Can the authors generate Cenpas just by over-expressing centrobin directly?

So in conclusion, the link between Cenpas and multipolarity has to be better investigated in my opinion. This should not be time consuming and also not extremely costly. Authors should label spindle microtubules in patient fibroblasts to show that indeed Cenpas are nucleating microtubules. Ideally Cenpas would be distinguished by centrobin labeling. In siRNA depleted cells maybe time lapse microscopy can be used to image mitosis and show a correlation between Cenpas and multipolarity?

Minor comments:

Some picture lack scale bars

the localization of GFP-Trim37. On Figure 1 the authors describe a different localization when fused to a NES localization. It is true that a dotty signal is seen on the panel of NES (Figure 1D), but a nuclear signal is not seen on Trim-GFP in any of the images provided. Shouldn't this be the case?

Fig 1C is missing a siCtrl. Why Trim37GFP does not rescue completely the assembly of the extra foci?

In Fig 6E, are the authors sure that in the condition of siTRim3 plus si Centrobin and Plk1 inhibition, cells are not stuck in S-phase? This might explain the lack of being in a permissive G2 phase to generate Cenpas?

The data is presented without statistical analysis on the figures. This can be found on figure legends, but it is better to include on the figures to facilitate the reader's job. The number of experiments and cells analyzed maybe should be also included in each Figure?

Significance

Interesting findings and quite novel since a role for Trim 37 in centriole biogenesis has never been reported. Also quite interesting the possible link between multipolarity (needs better characterization) and Mulibrey syndrome.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In this work, the authors investigated roles of TRIM37 in regulation of centriole numbers. It was previously observed that depletion of TRIM37 results in supernumerary centrioles and centriole-like structures (Balestra et al., Dev. Cell, 2013; Meitinger et. al., 2016). Here, the authors characterized these centriolar protein assemblies (Cenpas). Cenpas were formed, following an atypical de novo pathway and eventually trigger centriole assembly. They observed that Centrobin is frequently present in Cenpas from the early stage and other centriolar components are sequentially recruited. Furthermore, they established that Cenpas formation upon TRIM37 depletion requires PLK4 activity. TRIM37 depletion also activates PLK1-dependent centriole multiplication.

1. They propose that the tiger structure acts as platform for PLK4-dependent Cenpas assembly. Cenpas may evolve into centriole-like structures after a stepwise incorporation of other centriolar proteins. Fig. 6E suggests that a series of events seem to occur within G2 phase. Therefore, this reviewer suggests to perform a detailed time-course experiments at G2 phase. According to the model, the Centrobin-positive tiger structures may appear first, and then a Centrobin- and centrin-2-double positive structure starts to appear.
2. They claim that Mulibrey patient cells exhibited evidence of chromosome mis-segregation, as would be expected from multipolar spindle assembly, and conclude that Cenpas are present and active also in Mulibrey patient cells. Chromosome mis-segregation may be observed in the normal cells, too. Therefore, they have to perform statistical analysis on Fig. 2D.
3. In Fig. 2A, They claimed that mitotic microtubules were disrupted with the cold treatment for 30 min. In our experience, cold treatment for 30 min is not sufficient to disrupt mitotic microtubules. They may show control panel before microtubule regrowth.

Significance

Significance of this work resides in identification and description of Cenpas as a novel centriole assembly pathway. The authors used cutting-edge microscopy techniques to visualize Cenpas. The manuscript raised more questions than answers. Nonetheless, it is worth to publish the manuscript after revision.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The manuscript describes the formation of supernumerary centriole protein assemblies ("cenpas") upon silencing of the E3 ubiquitin ligase TRIM37. These "cenpas" resemble centrioles, centriole precursors, or electron-dense striped structures, termed "tigers". Similar observations are made in cells from patients lacking functional alleles of TRIM37. The "cenpas" usually lack the full complement of centriolar proteins, but contain increased amounts of the pro-centriole marker centrobin. It is further shown that the formation of "cenpas" depends on centrobin, or on a parallel pathway involving Plk1 and SAS-6.

Overall, the experiments in this study are of high technical quality and most of them are carefully controlled. The discovery of centrobin-containing striped protein assemblies ("tigers") is very interesting and provokes the question of their molecular composition and their mechanistic role in centriole assembly. Since striated fibres containing the protein rootletin have a similar periodicity of stripes (75nm) as the "tigers" in this study (Vlijm et al., PNAS 2018, 115:E2246-53), I was wondering whether the authors couldn't simply test for co-localization of their "tiger"-stripes with rootletin. A potential identity of "tigers" with striated fibres would help understanding the mechanisms of "cenpas" and centriole assembly upon depletion of TRIM37: striated fibres or "tigers" might be controlling the balance of centriole cohesion vs. disengagement and thereby centriole duplication, or they might play a role in the recruitment of additional proteins involved in pro-centriole assembly. In the same context, did the authors correct for the experimentally induced sample expansion in Figure 5B, when comparing inter-stripe distances between U-ExM and EM samples?

Other major points:

The amount of TRIM37-depletion upon siRNA-treatment should be indicated prominently. I see in the "Materials and Methods" and in Fig. S4 that quantitative RT-PCR has been performed. Could Western blotting be performed to have direct information on the protein levels? Fig. 2C demonstrates that this is possible in cells from human patients, so why are there no data on the majority of other experiments in this manuscript? Moreover, what is the transfection efficiency in the siRNA experiments? Is there variability between cells that might explain variability in the "cenpas" phenotypes?

Minor point:

In line 353 (page 12), it is stated that centrobin in si-TRIM37 cells migrates slower (Fig. 4D), suggesting that TRIM37 regulates the post-translational state of centrobin. It looks to me as if the corresponding gel in Fig. 4D was "smiling" (see curvature of centrobin in the neighboring lane). I think that the authors should tone down their statement, or replace Fig. 4D with a more convincing image.

Significance

The findings of this manuscript are highly significant for our understanding of centriole biogenesis. They should be of interest to a large community of cell biologists working on mitosis and on the centrosome, and they are of further importance for biomedical research related to developmental growth abnormalities (Mulibrey nanism). The manuscript shows for the first time a mechanistic link between TRIM37-dependent control of centrobin protein levels, and their impact on the formation of centriole precursors during the cell cycle. The manuscript is well presented, and the relevant scientific literature is cited correctly. However, I would prefer that a potential relationship between "cenpas", "tigers", and the well-described rootletin-containing striated fibres be discussed, if not controlled by additional experiments.

Field of expertise of this reviewer: centrosome, microtubules, mitosis, cell culture, light and electron microscopy, biochemistry.

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a response at this time.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary

The manuscript by Pal and Das has explored the regulation of LincRNAs by p53 and by the shorter p53 isoform 40p53. In particular, through a series of knockdown and overexpression studies (primarily in one cell line) they demonstrate that LINC00176 is regulated by 40p53 to a greater extent than full-length p53 and provide evidence that this is occurring at the transcriptional level as well as through direct modulation of the RNA stability. This study has provided novel insights into the role of ∆40p53 in regulating the lncRNA-miRNA axis and perhaps more importantly, demonstrates the functional differences between the full-length p53 and its smaller isoforms.

Major Comments

While the subject matter is extremely interesting and has provided new mechanistic insights into how the smaller forms of p53 modulate the functions of the full-length form, many of the results are overstated, have been performed in a single cell line and are not convincing in their current form.

• It's completely unclear how the HCT 116 cell lines expressing only p53 or Δ40p53 were generated. It is stated that the expression of these isoforms is endogenous, yet there is not mention of siRNA to knock down either of the isoforms while maintaining high expression of the other isoform. I am a little confused by the approach used here to maintain endogenous expression of one or the other isoform specifically. Apologies if I have missed this.
• Line 209: "which is analogous to WT p53 and Δ40p53 levels in cancer". Which studies are you referring to, most published studies seem to indicate that the opposite is true??
• Line 211-213: "LINC00176 was positively correlated with p53 levels (Figure S1C, E, G). However, in tumor tissues, they were negatively correlated (Figure S1D, F, H)." This is completely overstated and untrue, needs to be reworded. The only correlation is in Supp Fig 1C. p53 is not significantly correlated with LINC00176 in any other figure (as demonstrated by your p-values and R values).
• Line 225-26: "However, the fold change was highest in cells with Δ40p53 overexpression, suggesting that Δ40p53 might be a more important regulator than p53." Overstated - there is no statistically significant difference between p53 and Δ40p53.
• Fig 1 doesn't make sense... If you transfect cells with siRNA to p53 (Fig 1E) wouldn't you expect an increase in LINC00176??
• Western Blots are very cropped. Full length western blots should be provided.
• Line 251-253- "In HCT116+/+ cells, LINC00176 was upregulated in the doxorubicin treated and glucose-deprived cells; however, in cells treated with thapsigargin, there was no significant change (Figure S2 A-F)." There is no increase in p53 expression in some of the figs shown in the supp figs- then are the levels really correlated with p53 expression??
• "We observed a slight increase in the proportion of cells in G1 phase and a slight decrease in the proportion of cells in S phase with LINC00176 overexpression (Figure S5F)." This is not obvious at all- delete or reword.
• "We found a decrease in the number of colonies after LINC00176 overexpression (Figure S5G) and an increase in the number of colonies after LINC00176 knockdown (Figure S5H)". Colony formation needs to be quantitated, otherwise, don't show it. The results are not obvious at all.
• Almost all statistics reported in this manuscript need corrections for multiple comparisons. I am fairly certain if this is done, many of the comparisons will lose their significance.
• All results should be validated in an additional cell line.
• There is little insight given with respect to the literature regarding what the known functions of LINC00176 RNA are or with respect to the known functions of Δ40p53
• Although Figure 5 starts to delve into the functional impacts of LINC00176, it doesn't really look at any particular function in enough detail for it to make a significant contribution to the results. For instance, the assessment of EMT genes in Figure 5 D-F doesn't really mean much if you haven't shown altered migration/invasion capacity. This needs to be demonstrated. There are no error bars on the proliferation rates (Fig 5G and H, Supp 5B-E). Cell cycle analysis- no stats and the changes look fairly minimal. Target genes such as p21 involved in p53 cell cycle function should be analysed. Colony formation assays need to be quantitated.
• Figure 5 should be complemented by the examination of genes known to be involved in the p53 pathway or known to be regulated by Δ40p53. Additionally, Figure 4 should show if the expression of target genes regulated by the miRNAs is altered in these experiments.
• In all figures (and in the methods section), it needs to be stated how many experiments and how many replicates the result is representing. Given the lack of error bars in 5G,H, I can only assume the experiment has been done once.

Minor Comments

• Cell cycle analysis can use much greater detail, both in the experimental and analysis details (page 7, 178-182). How were the results analysed? Gating examples should be shown in the supplementary data.
• Line 104: siRNA directed to Δ40p53, in Figs 1/2. There are no details of the Δ40p53 siRNA used in these studies.
• Line 124: "non-specific siRNA (Dharmacon) was used in the partial silencing of p53/Δ40p53 in the experiments as control. si" This doesn't make sense, the non-specific siRNA should not affect gene expression??
• Line 219: "Given the distinctive functions of LINC00176 reported in the literature.......". Please qualify and provide appropriate references and examples.
• I can't see the 14A construct in the materials and methods.
• Fig 1, p-values need to be stated and keys to the ** need to be stated as well in the figure legend.
• Line 233 "The levels of LINC00176 decreased in both cell lines after siRNA transfection (Figure 1E, G). However, we did not observe a significant decrease in LINC00176 in either cell line.....". Yet there is a star indicating significance in both figures?? Please correct this.
• Western blots: It makes no sense to choose a housekeeping protein the same size as your protein of interest, as this can skew the results if your blot isn't properly stripped prior to re-probing and there may be some cross reactivity with your protein of interest if the same secondary is used for both that target and housekeeping. What was the rational for choosing B-actin?
• Fig 2K- no mention of Bip or its relevance in the text.
• Fig S3 Why is p53 MW so high (63kDa) compared to other figures throughout the manuscript.
• A better description of the Actinomycin D experiments is needed. Why use this? What are you showing? It is not obvious to the reader and needs to be described.
• The discussion is very poorly referenced overall and greater insight should be given with respect to the current literature and how this has advanced the field.
• Software used to perform statistical analysis is not stated.
• Figure 5 G and H needs error bars.
• The English is poor throughout despite the statement that the manuscript has been checked by English language editors.

Significance

∆40p53 is an important and often underappreciated isoform of p53. It's important regulatory functions are only beginning to be recognised and this study has provided some novel and exciting insights into the role of ∆40p53 in regulating the lncRNA-miRNA axis. However, overall, the experimental details are lacking and the results are overstated in several areas and require validation.

This manuscript would particularly appeal to researchers in the p53 and lncRNA fields.

My expertise is in the p53 field, cancer, cell and molecular biology.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors investigate the interaction between LINC00176 and the translational isoform Δ40p53, exploring how Δ40p53, separately from full-length p53, regulates the expression of LINC00176 and what effects the lncRNA ,ay have on miRNAs and on various cellular processes such as growth and proliferation. Although this is an interesting study, it lacks depth and it feels very preliminary. Even though the main focus of the study lies on the transcriptional regulation of LINC00176 by p53, this process still needs further investigation0 Moreover, the experimental design is messy which is reflected on the figures as well. There is also a lack of depth on the role of the lncRNA in the cells and in miRNA regulation.

Major comments:

1. Despite the title mentioning miRNAs, the results regarding miRNAs (when investigating LINC00176's mechanism of action) seem almost like they belong in another study and there isn't much expansion on these results beyond the fact that the miRNAs identified are potential targets of LINC00176. Additionally, there is no substantial background on miRNAs and the ceRNA theory in the introduction.
2. The authors should show in a figure how the screen was done and what other lncRNAs were discovered
3. The TCGA data in Figures S1A and S1B are contradictory regarding the lncRNA expression.
4. Figure S1C-H do not show clear correlation and in some cases there is no statistical significance.
5. On figure 1, the authors mention that the HCT116-/- express the Δ40p53 isoform. Is this based on the way that the cells were generated (e.g., only the first nucleotides deleted)? Or, is the Δ40p53 stably expressed after ectopic expression in the HCT116-/- cells? It should be clarified.
6. An HCT116-/- cell line with no Δ40p53 should be used as a negative control in Figure 1.
7. The results on Figure 1A and 1I are contradictory. Explain
8. For Figures 1E and 1G, the authors state in the results section that the siRNA KD of either p53 isoform does not lead to a significant decrease in LINC00176, but there are significance markers (p < 0.05) on both graphs.
9. The WB in Figure 2J should be repeated
10. There is no description of Figure 2K in the text.
11. Figure 3: A Luciferase assay with the lncRNA promoter should be conducted. The p53 response element should also be mutated to confirm direct regulation of p53 on the promoter. A schematic of the promoter with p53 response elements is required.
12. Figure S3 is based on a prediction from an algorithm and is not validated. Is Δ40p53 directly binding to the lncRNA? EMSA assay with purified protein and in vitro transcribed RNA is required. There can be no claims for direct p53-RNA interactions otherwise. Δ40p53 may regulate stability indirectly, through a different regulator. Is the lncRNA expressed in the cytoplasm or in the nucleus?
13. There is no ChIP assay description in the methods
14. The potential miRNA targets of LINC00176 identified in Figure 4 have functions involved in the processes of apoptosis, senescence, and autophagy in addition to cell proliferation and cell cycle regulation. It would be nice if they had done phenotypic assays for these processes in Figures 5/S5 as well. How does LINC00176 affect those cellular processes if its potential targets are known to be involved in them?
15. Figure 4: Are the miRNAs regulated by the lncRNA also regulated after p53 knockdown? Is lincRNA the mediator? A rescue experiment is required.
16. Figure 4: Multiple siRNAs for the lncRNA are required to make sure that there is no off-target effect.
17. Figure 5: Why is shRNA used instead of siRNA? In both cases, transient transfection is used.
18. Figure 5G-H: show the average of 3 repeats and not each repeat separately.
19. Figure S5A: shLINC00176 leads to lower Δ40p53. Why? The authors should discuss
20. Figure S5F: How many repeats is the graph showing? There are no stats and no apparent change in cell cycle.
21. Figure S5G should be quantified.
22. There should be a greater focus on the role of the lncRNA in the phenotype of the cells. Is the lncRNA playing any role in the migration and invasion of the cells? A xenograft model would greatly strengthen the study.
23. Is the p53 knockdown phenotype rescued after o/e of the lncRNA?

Minor comments:

1. There are few mistakes such as typos and structural mistakes throughout the text.
2. The siRNA for Δ40p53 is not specific for this isoform. It should be mentioned in the main body of the text. 'Ns psi' should be changed to 'si Nsp' or 'Nsp siRNA'.
3. How many replicates were conducted for each experiment?
4. Figure 2F: How are the stats are compared?
5. Figures 2 J and 2K should be flipped.
6. The models in figures 3 and 4 don't really add much. Since there is a graphical abstract at the end to show an overview of the paper's findings, these earlier models don't seem necessary.
7. The labeling of Fig 3D is distracting. The labels on both the x-axis and the legend for the same things are unnecessary. Also, the fold enrichment in 3D in the control samples seems mild, especially compared to the levels that it was in 3B.
8. The nomenclature of the antibodies is very confusing. I would prefer to just call them p53 antibody and just specify in the methods what specific antibodies were used for each assay.

Significance

This is an interesting topic. It is important to decipher the role and regulation of lncRNAs in the p53 pathway so as to understand how it mediates its function. There are numerous similar studies focusing on the role of lncRNAs in cancer but not so many in the role of p53-regulated lncRNAs. The audience of the study is broad, targeting both p53 and cancer biology as well as RNA biology interest. My expertise lies on cancer biology and RNA biology

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

In this manuscript of title "The "LINC" in between 40p53-miRNA axis in the regulation of cellular processes" authors identify long noncoding RNA LINC00176 as a target of delta40p53 and also as an interactor of delta40p53 protein. Modulation of LINC00176 leads to altered levels of a panel of miRNAs and of some epithelial-mesenchymal markers. Moreover, LINC00176 negatively regulates proliferation/viability.

Major comments:

• Are the key conclusions convincing?

Despite the findings presented in this study are novel and relevant with regard to p53 function in cancer cells, the study is very preliminary and opens different lines of investigation that remain incomplete. Some examples: Authors identify a panel of miRNAs that may interact with LINC00176 but do not provide any functional impact of these miRNAs on cancer cell functions. Authors show modulation of epithelial-mesenchymal markers but do not provide evidence for changes in cell behavior (motility for example) Authors show that LINC00176 impacts on D40p53 protein level, but no statistical significance of this result nor description of the mechanism are provided. Importantly, the study is basically carried out using HCT116 p53-/- cells for the majority of the experiments. It would be worth trying to prove the relevance of the identified axis in the context of a cancer type, by analyzing the expression of D40p53 protein by WB and, concomitantly, the level of LINC00176 expression on the same samples. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

I have indicated this below - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

I have indicated this below - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. - Are the data and the methods presented in such a way that they can be reproduced?

Yes - Are the experiments adequately replicated and statistical analysis adequate?

I have indicated below some critical points in this regard

There are several conclusions in the presented data that are not convincing, especially those from which the study stems. These are detailed below:

Authors say that LINC00176 is expressed at lower level in tumor vs normal tissues in LUAD, LUSC and COAD (box plot supply fig 1b); however, plots from GEPIA presented in Suppl Fig 1A show exactly the opposite result. Moreover, box plots do not have asterisk, which is provided by GEPIA when results are significant, indicating that the presented differences in expression are not significant. I suggest to delete these results and revise the analysis which led to inconclusive contrasting results.

Figure 1D: Please explain in the text why HCT116 p53-/- cells show highly expressed D40p53 to allow readers to easily follow the experiments.

Suppl. Fig.1C-E-G: Authors say that in normal tissues, LINC00176 was positively correlated with p53 levels (line 212). Again, here only in LUAD the positive correlation is significant. They also say that "in tumor tissues they were negatively correlated" (line 213). This is discordant with data presented in Suppl. Fig.1D-F-H, where no negative correlation is present (negative corr. is indicated by minus sign preceding the correlation coefficient (R) in Pearson's / Spearman's analysis).

"This observation suggests that LINC00176 may be positively regulated by WT p53 in normal conditions and negatively regulated by mutant p53 in tumor conditions" (line 214-215): this could be easily assessed as TP53 mutational status is publicly available in the TCGA datasets.

Figure 1. It is not indicated whether the significance derives from three independent biological replicates. This should be addressed for all the experiments presented in the study.

Figure 2I: Please indicate on the graph which comparison the asterisks refer to. Moreover, explain better in the text that induction caused by ER stress is not obtained in absence of D40p53.

Figure 2K-J: Quality of the WB is poor. Moreover, as the b-actin seems down regulated by si-D40/Thaps the normalization over b-act is not so informative (numbers at the bottom of the panels).

Figure 3: Enrichments of D40p53 in ChIP experiments are really small. Usually enrichments <2folds are not very reliable.

Figure 4F-G: Please explain better in the text the pull-down results, describing which comparisons have been made to evaluate the results.

Figure 5G-H: Please include significance for the viability assays

Figure 5E: The finding that o/e of LINC00176 induces D40p53 is very interesting and it's worth reinforcing this by analyzing 3 biological replicates followed by quantification of WB results and statistical analysis. I strongly suggest to evaluate D40p53 protein in cells silenced for LINC00176 as well. Interaction D40p53/LINC00176 could be stabilizing on both sides. Evaluation of cells with modulated LINC00176 in presence/absence of cycloheximide would definitely prove this. Inclusion of evaluation of this aspect with regard also to p53 is encouraged.

For all the presented experiments number of biological replicates evaluated should be indicated.

Minor comments:

• Specific experimental issues that are easily addressable.
• Are prior studies referenced appropriately? Yes
• Are the text and figures clear and accurate? Yes, unless indicated in the suggestions above
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? I have already included this above

Significance

The study highlights that D40p53 protein, besides regulating microRNAs (as previously reported) is also involved in the control of lncRNAs. The findings provide an advancement in the understanding of D40p53 function in cancer cells.

The study might be quite relevant for the scientific community (cancer/tumor suppressors) if evaluation of cancer samples will be included.

My expertise falls in the p53/mutant-p53 and non-coding RNA fields so I think it is appropriate to evaluate this study.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2022-01488

Corresponding author(s): Tobias Lange, Csaba Jeney

1. General Statements

First of all, we would like to thank the reviewers for their valuable comments on our manuscript. We appreciate your questions and comments and we tried to answer thoroughly all points raised.

Consistent with the comments, we would like to shift the focus of this paper to the comparison of scRT-ddPCR with scRNA-seq signal distributions taking this scRNA-seq method as an exemplary but experimentally matching control. This is represented in the new title ”Validation of scRNA-seq by scRT-ddPCR using the example of ErbB2 in MCF7 cells”.

A major point was in the comments the use of ERCC spike-ins. We carefully considered ERCC spike-ins during the design of the experiments but finally omitted this concept as the ERCC spike-ins were designed for relative quantification (fold changes) but not for absolute counts. Furthermore, it was shown that these controls have a high variability and high dropouts (Risso et al. 2014, Vallejos et al. 2017). We were also aware that ERCC spike-ins analysis can be biased by the apparent Poisson distribution and could thus complicate the (absolute) quantitative analysis. However, we are reconsidering including these controls, after external validation, in a subsequent publication.

Besides that, to improve the manuscript it was suggested to split it into two publications, which we seriously considered but the validation of scRNA-seq data by scRT-ddPCR is now the major conclusion, and separate publications are necessary regarding the other improvements presented. Please find the answers below.

We hope that we were able to answer all criticism sufficiently well and we are open for further discussion.

2. Description of the planned revisions

Reviewer 1

Major concerns:

The authors did not compare their results with standard SMART-seq2 in detection sensitivity (comparison on UMAP clustering is really trivial, and cannot serve the purpose)

To further validate our workflow, we consider to compare signal distributions of ErbB2 and ACTB in MCF7 cells from Isakova et al. (2021) (GSE151334) with the distributions obtained from our approach (see Fig 4 a and b).

Reviewer 2

Minor concerns:

Figure 1. B and C figure's axes are not easy to read even at highest zoom. At least the 400 bp in the x axis could be represented using a bigger font.

Yes, we will increase the font size of Fig 1b and c.

Figure S4. 'for in in range' needs some attention.

It might become clearer using the expression “cycle 1000x” or “repeat 1000x”.

Reviewer 3

Major concerns:

Single-cell SMART-Seq with SMART-Seq from "bulk" and "cl", which authors include in scRT-dPCR but not in scRNA-Seq

The controls “bulk” and “cl” are designed to validate the lysis of a single cell after processing by F.SIGHT and I.DOT (see 3.2 Validation of scRT-ddPCR using bulk methods). Our results indicate that, independent of the method, we quantify the same absolute amount of ACTB and ErbB2 mRNA in single cells (Fig 3). To avoid confusion, we will thus remove the signal distribution of “bulk” and “cl” in Fig 4 a and b.

Authors analysed scRNA-Seq data using "pseudo-bulk" differential expression analysis using DESeq2. Authors did not include more details about processing of the data, if they used standard DESeq2 protocol, or modified protocol recommended for scRNA-Seq data. It is hard to conclude if the chosen method is optimal, however I'm recommending to use method, which is standard for scRNA-Seq nowadays, like a Seurat with SCTransfrom.

We have followed published settings of DESeq2, which can be specifically applied to single cell data, also described here. Indeed, after we checked our settings, we realized that we did not use the correct parameters and we have implemented the changes. However, this will not substantially affect our results and conclusions. The scripts of data processing are added to the supplementary material.

Reviewer 3

Minor concerns:

Commercial kit SMART-Seq from Takara is not same as Smart-Seq2 protocol (line 198). Please do not use same name for commercial and academical protocols.

We adjust the nomenclature to account for the differences.

Can you include more details for processing of data?

We revise the manuscript accordingly. Briefly, the aligners were wrapped into bash scripts and alignment was performed on each FASTQ file separately. As recommended in the documentation for kallisto and salmon, the mean read length and its standard deviation was calculated for each file. In alignments with STAR a genome index was created (as recommended). After alignment, the read table was created with FeatureCounts. We also share the scripts and settings for data processing as indicated above.

Can you share whole script for data processing?

Yes, we share the scripts for data processing in the supplementary material.

Why you didn't't show any other cell type specific markers, which differ between chosen cell lines (lines 328/329)?

The chosen cell lines are highly related; in breast cancer research, they are frequently used to control each other. This choice has advantages and drawbacks, as they differ principally in their ErbB2 expression. MCF7 and BT-474 serve as good controls in this study. An expansion to other differentially expressed genes is limited. However, we evaluated KRT8 and TFF1 (two marker genes for MCF7 cells (Isakova et al. 2021)) in scRNA-seq and ErbB2 in both scRNA-seq and scRT-ddPCR as key markers. We could highlight more marker genes between MCF7 and BT-474 cells on the basis of scRNA-seq data.

I don't understand "missing normalization of counts" for comparison between different aligners. Especially, because counts are normalized during analysis using DESeq2 (line 396).

We apologize for the misunderstandable terms, the signal distributions are constructed based on the values from Fig 2b (and not based on DESeq2), thus the unit of salmon and kallisto distributions is TPM, while for STAR distributions it is raw counts. This discrepancy in normalization of counts might contribute to the difference in distributions between STAR and kallisto as well as between STAR and salmon.

Authors should change name "integrated workflow" into something else, because there is no integration of scRNA-Seq data with scRT-dPCR. They only compare results from this two methods.

We consider to rename the publication, for instance, Validation of scRNA-seq by scRT-ddPCR using the example of ErbB2* in MCF7 cells. *

There is no demonstration of needs of validation (line 416).

Yes, we agree, the need for validation is only mentioned in the introduction (lines 69 to 75 and lines 82 to 85) but should be taken up here again.

Are the differences in the log2FC real problem for single-cell experiments? Authors used different cells and different number of cells for comparison. Can it be source of different log2FC?

Indeed, the amount of cells between scRNA-seq and scRT-ddPCR were different and we understand that this might introduce subsampling errors. Assessing that question we bootstrap and down-sample the scRNA-seq group to compare the same amount of cells between scRNA-seq and scRT-ddPCR and revise this part accordingly.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Reviewer 1

Minor concerns:

Fig.1a,b, in ROI, there are overlap between "printed cells" and "detected particles"? How to distinguish between the two?

Each dot in the 2D scatter plot is a detected particle during the dispensation process of the F.SIGHT (see representative images in Fig 1a). The particles can be of various origin: cell debris, cell aggregates, corpuscular materials from cell culture medium or cells. The ROI defines the morphological criteria (diameter and roundness) by which we define a particle as a cell. The overlap between detected particles, which can thus also be cells, and the printed cells is because of the fact that some cells are detected but not evaluated as single cells.

Fig2d, what is the difference between DEG and "different genes"? The no. different genes is not specified for STAR?

1. DEGs are significantly different genes, abs(log2FC)>1 and padj1 but padj>0.05. These genes are different but not significantly.
2. For STAR, we did not obtain any genes of the latter category; all different genes are thus DEGs.

   It is not clear how the bulk samples(Fig.3,4) were prepared.

Thank you for pointing this out. We revised the manuscript accordingly, briefly the total RNA was isolated from 1E6 cells, diluted and analyzed in a dPCR (as described in 2.2 Total RNA isolation and bulk cell lysis). The absolute mRNA counts per single cell were calculated by dividing the detected number of transcripts with the number of cells.

Reviewer 2

Minor concerns:

P5, line 148 is not clear to me.

1E6 cells were lysed using 500 µl of Actome’s proprietary lysis buffer (PICO-000010, Actome). This results in 2000 cells/µl of lysate. By addition of 49.5µl DPBS (100X dilution), the cell concentration is 20 cells/µl. Thus, dispensation of 50 nl using the I.DOT results in an equivalent amount of material of a single cell.

Reviewer 3

Major concerns:

The conclusion from whole paper is confusing, because it is bringing several new information and methods, which would be better if they would presented separately. Mainly down-scaled SMART-Seq using i.DOT and F.SIGHT - it is novel and important. Single-cell dPCR combined with F.SIGHT, which can be presented separately without down-scaled SMART-Seq.

We discovered that down-scaling does not significantly enhance the detection of low-abundant transcripts such as ErbB2 in MCF7 cells (Fig 4a) contrary to theoretical considerations (lines 77 to 82). To assess this bias, scRT-ddPCR was used to validate the representability of low-abundant transcripts in scRNAseq, ultimately, revealing a better resolution of the expression in single MCF7 cells (Fig 4a). We see scRT-ddPCR as the potential improvement in validating scRNA-seq data regardless of the scRNA-seq method used. For the sake of this paper, however, we used a unique combination of methods. We understand the value of the components themselves, and the validation of miniaturized scRNA-seq deserves a subsequent paper. The used combination of methods, albeit unique, was designed to reduce the technical and biological variability to minimum; the cells originate from the same population and the same instrumentation was used. This is better suited to support our claims regarding representability.

Also to note, the scRT-ddPCR is a ground truth method that literally counts molecules. The only mathematical concept applied is Poisson statistics (Basu 2017), and no further data processing is necessary, which could influence data evaluation supporting its generality.

It is hard to say, "what is important message of this manuscript".

Low-abundant transcripts are often referred to as highly interesting and difficult to analyze especially regarding reproducibility (Fortunel et al. 2003, Schwender et al. 2014, Petrova et al. 2017, Taylor et al. 2017). Our data supports previous findings that dropouts in scRNA-seq are frequent (Luecken et al. 2019). Down-scaling of SMART-Seq2 does not significantly increase detection efficiency and reliability (Fig 4) despite the considerable assumptions described in lines 77 to 82. This part of the paper supports the previous findings. Additionally, we see the scRT-ddPCR method as a potential improvement in validating scRNAseq data regardless of the scRNA-seq method used.

I don't understand, why authors present comparison of two RNA isolation protocol in RT-dPCR results.

As described above, the “bulk” controls are needed to validate the full lysis of a single cell after processing by F.SIGHT and I.DOT (see 3.2 Validation of scRT-ddPCR using bulk methods). We assume that through total RNA isolation by commercially available and widely accepted kits, all mRNAs are released from the cells and are efficiently amplified. This serves as a reference value for the scRT-ddPCR method (Fig. 3b). To ensure the reliability of our reference value, we used two different commercial methods for total RNA isolation with unequivocal results (Fig S2d). These two methods, however, differ in sample preparation (DNase I digest vs no digest, enzymatic lysate homogenization vs mechanical lysate homogenization), in buffers and handling in general.

More, the whole conclusion and results are made only from one experiment from two separated measurements. Authors should repeat experiment and check if differences in log2FC between scRNA-Seq and scRT-dPCR are same all the time.

Single cell experiments are inherent biological replicates. We consider them to be a high number of parallels per experiment. They are processed parallely but separately, albeit using the same batch of chemicals and the same instrumentation. We purchased cells and chemicals from commercial sources assuming minimal possibility of error. The instruments were validated before use according to standard procedures.

Reviewer 3

Minor concerns:

What is LBTW (line 154)?

LBTW is a proprietary lysis buffer of Actome GmbH (line 146 and 147) (PICO-000010, Actome).

Have you process/sort cells for scRT-dPCR and scRNA-Seq same day?

Care has been taken to reduce the biological variability, so they were processed with minimal delay from the same dispensation cartridge and originate from the same cell culture flask.

How you dilute RNA for ddPCR (line 180)?

Total RNA from MCF7 cells was diluted 1:20, 1:50, 1:100 and 1:1000 with PBS, and ACTB and ErbB2 mRNAs were quantified in triplicates. Total RNA from BT-474 cells was diluted 1:50, 1:100, 1:1000 and 1:10000 with PBS, and ACTB and ErbB2 mRNAs were quantified in triplicates.

And for scRT-dPCR?

Single cells were not diluted. A single cell was dispensed directly into 0.5 µl lysis buffer, master mix was added and the scRT-ddPCR was performed.

How many cells per condition you have sorted for SMART-Seq?

84 cells were isolated for each cell line (Tab S1).

How much time you need for collection of cells?

The F.SIGHT requires a maximum of 8 min for the dispensation of 84 cells.

How much time you need for pipetting of solution? Can it be problem for neutralization of tagmentation?

The transposome activity was quenched by the addition of 0.5 µl of Neutralization buffer using the I.DOT. The I.DOT can dispense 96-wells per minute (Klinger et al. 2020).

Have you use robot or have you manually cleaned cDNA with AMPure beads?

The clean-up procedure was performed manually.

Which magnetic separator you have used for clean-up?

We used conventional neodym magnets for the separation of liquid and beads.

384-well plate design and clean-up of 20 ul volume is not something standard, please specify it in the protocol.

The procedure is described in the methods section lines 212 to 219.

Have you pooled libraries before clean-up (line 238)?

The cDNA libraries of single MCF7 and BT-474 cells were pooled separately.

If yes, what was final volume?

The final volume for each pooled library was ~420 µl (84 x ~5µl).

How much AMPure beads you have used for clean-up?

After cDNA amplification, we used 9 µl of AMPure bead suspension for clean-up. After library amplification, we used 0.6 to 1-fold volumes of the pooled library volume.

Is it pooling reason of loosing of 30% cells from dataset?

We isolated 84 single cells using the F.SIGHT. During quality control, we excluded ~30% of the cells from down-stream analyses (Tab S1). We applied the quality criteria as mentioned in lines 254 to 260. We think these are common criteria for filtering.

Why you choose different cell types as you used for sequencing?

In scRNA-seq and scRT-ddPCR (and in the corresponding controls), we used MCF7 and BT-474 cell lines. We chose these cell lines because of their well-described difference in ErbB2 expression (Durst et al. 2019) (lines 106 to 108 and lines 349 to 353).

Why it is important that tagmented cDNA was 459/432bp long (Line 310)? Is it specific for down-scaled, or classical SMART-Seq? How to use this information?

Jaeger et al. (2020) show examples of good quality tagmented cDNA libraries for down-scaled SMART-Seq2. Additionally, they mention that the peak should be within the range of 300 bp to 800 bp. Our tagmented cDNA library distribution (Fig 1c) exhibits remarkable similarity to the one shown by Jaeger et al. (2020) and the peak falls within the mentioned range. Thus, the tagmented cDNA obtained by our approach matches criteria for good quality tagemented cDNA library.

Comparison in lines 354-355 is confusing.

Using scRT-ddPCR, we could not detect a statistical difference in ACTB expression between the cell lines (Mann-Whitney test). MCF7 cells express 66±29 ACTB mRNAs per single cell and BT-474 cells express 114±80 ACTB mRNAs per single cell (Fig 3b).

I don't know, what you wanted to say by showing number of copies od different genes in different cell lines.

Absolute numbers of transcripts are very reliable, especially when they are generated by a method of ground truth relying on molecular counting (dPCR). Still some transcripts might not be transcribed into cDNA but partitioning increases their effective concentration (Basu 2017). Based on this, relative quantities can still be calculated. Additionally, absolute quantification eases data comparison as no standard is needed and dPCR has further advantages over qPCR (lines 97 to 103).

I'm not sure that scRNA-Seq and scRT-ddPCR are truly orthogonal methods. Both methods are PCR based. (lines 381-382).

While PCR is applied in both methods, we see the orthogonality of the methods in the independence of the detection events. dPCR provides a single molecular compartmentalization principle instead of scRNA-seq, where all mRNAs are transcribed competitively and simultaneously into cDNA. This results in multiple competing reactions and thus increases the propensity for dropouts. dPCR avoids that and directly provides molecular counts.

At the end, it is not important if the gene has two times or three times higher expression. Important is preservation of the trend.

In our view, trends are less informative measures than absolute counts, absolute counts are direct derivatives of chemical concentrations driving the chemical reactions in cells. Trends, however, can be reconstructed from absolute counts.

Authors are analyzing relative expression of Actb and ErbB2 between two lines. Could be used scRT-qPCR instead of scRT-ddPCR? It could solve problem in the number of genes, which could be analyzed (line 438).

Indeed, qPCR instruments usually offer a higher degree of multiplexing but we think that qPCR cannot deliver the sensitivity needed for the detection of low-abundant transcripts (see lines 97 to 103 and above). dPCR ensures the detection of single molecules, while qPCR has a variable sensitivity and would not be an orthogonal method according to our statement above. Furthermore, qPCR needs external standards for absolute quantification, while dPCR can absolutely quantify by molecular counting.

Are the differences in the log2FC real problem for single-cell experiments? Authors used different cells and different number of cells for comparison. Can it be source of different log2FC?

1. Difference in log2FCs might not be an exclusive problem for single-cell experiments (Rajkumar et al. 2015, von der Heyde et al. 2015, Everaert et al. 2017). However, we believe that in scRNA-seq differences are much more pronounced, especially regarding low-abundant transcripts, because of elevated amounts of technical noise and thus increased propensities for dropouts (Luecken et al. 2019).
2. For the comparison of fold changes, we used two different cell lines, MCF7 and BT-474, but compared fold changes from expression of gene x in MCF7 cells versus expression of gene x in BT-474 cells. Fold changes from scRNA-seq and scRT-ddPCR were calculated this way and eventually compared.

   Why we need absolute numbers of copies of transcripts (lines 458-459)? I'm OK with relative quantity using RT-qPCR.

Absolute numbers of transcripts are very reliable, especially when they are generated by a method of ground truth relying on molecular counting (dPCR). Based on this, relative quantities such as fold changes can still be calculated. As described above, dPCR has several advantages over qPCR. Furthermore, absolute amounts of mRNA per cell determine their chemical activity in a cell (Tang et al. 2011).

Authors presented two novel application, which both separately can be important for single-cell transcriptomic analysis. One is down-scaled SMART-Seq, which save a money and brings full-length scRNA-Seq to more researchers. Second is scRT-ddPCR, which can ultimately increase sensitivity of single-cell methods. However, combination of both methods in one paper, without comparison of other technologies decrease impact and importance both of them. I.e. Pokhilko et. al (2021) presented targeted single-cell RNA-Seq, which increase sensitivity of Smart-Seq2 too.

Pokhilko et al. (2021) also present a down-scaled version of SMART-Seq2 just as many other publications (Mora-Castilla et al. 2016, Jaeger et al. 2020, Isakova et al. 2021, Hahaut et al. 2022, Hagemann-Jensen et al. 2022). Pokhilko et al. (2021) use scRNA-seq data from Volpato et al. (2018), who use a manual, non-high-throughput method for single cell isolation. The F.SIGHT can gently isolate hundreds of single cells in a short period of time (see above) and records in parallel morphological characteristics, which can later be used to judge the cell’s integrity by neuronal networks (Riba et al. 2020) (see above: regarding the main conclusion of the paper and the planned follow-up paper, we highlight here that the focus was intended to be on the scRT-ddPCR method and its validation, and the miniaturized scRNA-seq was used to reduce the technical divergence of the methods).

In my opinion, separated publication of both methods will be better. While down-scaled Smart-Seq2 is often discussed in Core Facilities to bring scRNA-Seq to more biologist and clinician, scRT-dPCR is very interesting but specific method.

Although scRNA-seq is widely used, we could support recent findings (Luecken et al. 2019) that the detection of low-abundant transcripts is still challenging. Furthermore, we provide a proof-of-principle on how to validate the lack of representability of low-abundant transcripts in scRNA-seq: scRT-ddPCR.

I'm focused in the RNA-Sequencing from sample preparation to data analysis. I'm helping people with optimization of the design to get as much information as possible. I wasn't able to say, if used statistical methods are correct.

We carefully chose our statistical methods according to the suggestions in literature. We are open for specific scrutiny however.

How you used DESeq2, BBKNN?

1. The counts and transcript abundances were imported using the tximeta and tximport packages for data aligned with salmon and kallisto, respectively. Differential testing was carried out on the resulting count matrices with DESeq2 using LRT testing and other parameters set according to the recommendations of the DESeq2 vignette for testing single-cell data.
2. For BBKNN clustering, a custom data set was constructed combining our data (salmon aligner) with a published data set containing MCF7 cells, fibroblasts and HEK293T cells (Isakova et al. 2021). For the analysis, the data set was imported in SCANPY. Cells with fewer than 200 genes expressed and genes expressed in less than three cells were excluded from the analysis. Counts per cell were normalized with SCANPY’s built-in normalization method. The data was log-transformed, scaled and a PCA was carried out, according to the standard workflow recommended in the SCANPY documentation. BBKNN was similarly carried out with the respective SCANPY method, the final plot was created after dimensionality reduction with UMAP.

   How you have processed published data?

External data was concatenated with our data into a single AnnData object and analyzed according to the recommendations of the SCNAPY documentation.

4. Description of analyses that authors prefer not to carry out

Reviewer 1

Major concerns:

The authors did not compare their results with standard SMART-seq2 in detection sensitivity (comparison on UMAP clustering is really trivial, and cannot serve the purpose)

Miniaturization of SMART-seq2 and related protocols is frequently applied (Mora-Castilla et al. 2016, Jaeger et al. 2020, Isakova et al. 2021, Hahaut et al. 2022, Hagemann-Jensen et al. 2022) ensuring high quality data and reducing costs per cell. Therefore, we think that there is sufficient evidence that miniaturized/down-scaled protocols deliver the same results compared with standard protocols.

Fig3b, there are a total of four groups of comparison, two genes X two cell lines. In one of the four, i.e. ACTB in MCF7, the quantification among the three methods differ significantly. Given no ground truth here, it is hardly to judge the quality of their method. The author should add ERCC spike-in to control their experiments as stated in their Discussion.

1. Yes, we are aware of this difference as described in lines 371 to 375 and relate this difference to a different passage number (Tab S4) as it was already shown that housekeeping genes underlie fluctuations, too (Kozera et al. 2013). However, the difference in absolute counts does not have a significant impact on the fold changes (Fig 4c).
2. Risso et al. (2014) showed that ERCC control signals have a high variability, and Vallejos et al. (2017) found that only half of the spiked-in molecules are detected. Literature is not conclusive about the ErbB2 expression in MCF7 cells (Subik et al. 2010, Cui et al. 2012, Durst et al. 2019), so we applied scRT-ddPCR (a method of ground truth) on single MCF7 cells to reveal ErbB2 expression at highest available resolution. Upon these considerations ERCC control might have no impact on dPCR results.
3. However, we understand that the ERCC controls, comprising a set of polyadenylated transcripts that are added to the scRNAseq analysis experiment during single-cell isolation, can replicate the effect of low abundance transcripts. Single cells have very low transcript counts; it is questionable to quantitatively recapitulate this effect. The apparent Poisson distribution of the ERCC counts, at that low level, can complicate the quantitative analysis of the results, while the single-cell analysis also has its inherent heterogeneity. In the case of the lack of conclusive quantitative nature of ERCC spike-in, see also above, internal transcripts also can serve this aim of the study. However, in a subsequent paper, we plan to compare the two methods. To our knowledge, such a comparison between scRNA-seq and scRT-ddPCR was never performed before, so we could not follow previous realizations here. Our findings support the hypothesis that scRNA-seq suffers from detection deficits at the lower detection end (Luecken et al. 2019).

   Fig4b, ACTB in BT-474, it seems that the scDDPCR resulted in more cells in the first bin than scRNA-seq. This is in contrast to their claim of higher detection sensitivity of the former.

There are more cells in the first bins of the scRT-ddPCR histogram but on a statistical basis, the distributions do not significantly differ (Tab S6).

To assess the performance of their methods in a more systematic manner, the authors should perform the single cell measurements with ERCC spike-in, and check at least 5-10 endogenous genes at different expression level, in addition to the spike-in RNAs. They should choose cell lines for which the absolute no. of RNA for some house-keep genes has been measured using imaging based methods.

We thought we addressed these issues thoroughly in our discussion (ERCC spike-ins: lines 459 to 461 and more endogenous genes: lines 438 to 443 and see also above). In our view image-based methods suffer more technical ambiguities; however, they could serve as possible validation as they are orthogonal. Additionally, spatial resolution would be preserved but absolute quantification is not possible. Our scRT-ddPCR method was validated against bulk RNA isolation methods, which serve as established references regarding the RNA isolation. We accepted the RT-PCR as a reference as it has been thoroughly validated as a method providing precise nucleic acid counts.

The two methods described in the manuscript represent little technical advance. In addition, the conclusion stated in the manuscript is also not sufficiently convincing. As such, it would be of little interest to limited group of audience.

The two most frequently used methods for scRNA-seq are Chromium from 10X Genomics and Smart-Seq2-based protocols. In a direct comparison, Wang et al. (2021) showed that Smart-Seq2 is better suited for the detection of low abundant transcripts. We wanted to further enhance the sensitivity of SMART-seq2 by down-scaling; it was hypothesized that this increases the detection efficiency (Mora-Castilla et al. 2016). However, we were still not able to detect low-abundant transcripts such as ErbB2 in MCF7 cells (Fig 4a). Low-abundant transcripts are often referred to as highly interesting and difficult to analyze especially regarding reproducibility (Fortunel et al. 2003, Schwender et al. 2014, Petrova et al. 2017, Taylor et al. 2017). Our proposed scRT-ddPCR can reliably and absolutely quantify low-abundant transcripts offering a solution for the detection of such targets. The majority of similar workflows use scRT-qPCR (lines 82 to 86), although dPCR is much more sensitive and can detect fold changes down to 1.16-fold (Basu 2017).

Reviewer 3

Major concerns:

Down-scaled SMART-Seq with standard SMART-Seq

We compared our down-scaled SMART-Seq2 workflow to a validated, down-scaled SMART-Seq2 workflow (Isakova et al. 2021) using UMAP clustering. Furthermore, miniaturization of SMART-Seq2 and related protocols is common practice (Mora-Castilla et al. 2016, Jaeger et al. 2020, Isakova et al. 2021, Hahaut et al. 2022, Hagemann-Jensen et al. 2022). Therefore, we think that a UMAP comparison is sufficiently proving that our down-scaled protocols deliver reliable results. However, we see some possible improvement by comparing distributions of gene expressions (see above).

Single-cell SMART-Seq with SMART-Seq from "bulk" and "cl", which authors include in scRT-dPCR but not in scRNA-Seq

Smart-seq2 was designed to profile the transcriptome of single cells (Picelli et al. 2013, Picelli et al. 2014). Other methods are purely for comparison and validation and were not intended to be technological advancements.

scRT-dPCR with scRT-qPCR

qPCR is often used to validate fold changes from RNA-seq (Zucha et al. 2021). The differences between qPCR and dPCR are extensively described, for instance, in Basu (2017). In several comparisons between qPCR and dPCR or even RT-qPCR and RT-dPCR, the latter showed increased precision, reproducibility, higher sensitivity and high tolerance towards inhibitors (Alikian et al. 2017, Taylor et al. 2017). Thus, we assume that qPCR is not the method of choice for the detection of low-abundant transcripts such as ErbB2 in MCF7 cells (lines 97 to 103).

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

Authors compared differential expression of Actb and ErbB2 between cells from two cell lines MCF7 and BT-474. They used two new/optimized methods: down-scaled SMART-Seq and single-cell RT-dPCR. They demonstrated, that scRNA-Seq method is not sensitive enough method to properly quantify low abundant transcripts and we need additional method for it.

Major comments:

Authors are comparing results from two novel methods - down-scaled SMART-Seq and scRT-dPCR, without including standard protocol. I'm missing some additional experiments/comparison. The conclusion about one correct and one incorrect method are too strong, with many variables. Only one clear conclusion is about dropout in scRNA-Seq in comparison with scRT-dPCR. - Down-scaled SMART-Seq with standard SMART-Seq - Single-cell SMART-Seq with SMART-Seq from "bulk" and "cl", which authors include in scRT-dPCR but not in scRNA-Seq - scRT-dPCR with scRT-qPCR Authors analysed scRNA-Seq data using "pseudo-bulk" differential expression analysis using DESeq2. Authors did not include more details about processing of the data, if they used standard DESeq2 protocol, or modified protocol recommended for scRNA-Seq data. It is hard to conclude if the chosen method is optimal, however I'm recommending to use method, which is standard for scRNA-Seq nowadays, like a Seurat with SCTransfrom. The conclusion from whole paper is confusing, because it is bringing several new information and methods, which would be better if they would presented separately. Mainly down-scaled SMART-Seq using i.DOT and F.SIGHT - it is novel and important. Single-cell dPCR combined with F.SIGHT, which can be presented separately without down-scaled SMART-Seq. And comparison of different aligner for scRNA-Seq data analysis. It is hard to say, "what is important message of this manuscript". I don't understand, why authors present comparison of two RNA isolation protocol in RT-dPCR results. More, the whole conclusion and results are made only from one experiment from two separated measurements. Authors should repeat experiment and check if differences in log2FC between scRNA-Seq and scRT-dPCR are same all the time.

Minor comments:

Authors are commenting sensitivity The method part needs additional information.

What is LBTW (line 154)?

Have you process/sort cells for scRT-dPCR and scRNA-Seq same day?

How you dilute RNA for ddPCR (line 180)? And for scRT-dPCR?

Commercial kit SMART-Seq from Takara is not same as Smart-Seq2 protocol (line 198). Please do not use same name for commercial and academical protocols.

How many cells per condition you have sorted for SMART-Seq?

How much time you need for collection of cells?

How much time you need for pipetting of solution? Can it be problem for neutralization of tagmentation? Have you use robot or have you manually cleaned cDNA with AMPure beads?

Which magnetic separator you have used for clean-up? 384-well plate design and clean-up of 20 ul volume is not something standard, please specify it in the protocol.

Have you pooled libraries before clean-up (line 238)? If yes, what was final volume? How much AMPure beads you have used for clean-up? Is it pooling reason of loosing of 30% cells from dataset?

Can you include more details for processing of data? How you used DESeq2, BBKNN? How you have processed published data? Why you choose different cell types as you used for sequencing? Can you share whole script for data processing?

Why it is important that tagmented cDNA was 459/432bp long (Line 310)? Is it specific for down-scaled, or classical SMART-Seq? How to use this information?

Why you didn't't show any other cell type specific markers, which differ between chosen cell lines (lines 328/329)?

Comparison in lines 354-355 is confusing. I don't know, what you wanted to say by showing number of copies od different genes in different cell lines.

I'm not sure that scRNA-Seq and scRT-ddPCR are truly orthogonal methods. Both methods are PCR based. (lines 381-382).

I don't understand "missing normalization of counts" for comparison between different aligners. Especially, because counts are normalized during analysis using DESeq2 (line 396).

Authors should change name "integrated workflow" into something else, because there is no integration of scRNA-Seq data with scRT-dPCR. They only compare results from this two methods.

There is no demonstration of needs of validation (line 416). At the end, it is not important if the gene has two times or three times higher expression. Important is preservation of the trend.

Authors are analyzing relative expression of Actb and ErbB2 between two lines. Could be used scRT-qPCR instead of scRT-ddPCR? It could solve problem in the number of genes, which could be analyzed (line 438).

Are the differences in the log2FC real problem for single-cell experiments? Authors used different cells and different number of cells for comparison. Can it be source of different log2FC?

Why we need absolute numbers of copies of transcripts (lines 458-459)? I'm OK with relative quantity using RT-qPCR.

Significance

Authors presented two novel application, which both separately can be important for single-cell transcriptomic analysis. One is down-scaled SMART-Seq, which save a money and brings full-length scRNA-Seq to more researchers. Second is scRT-ddPCR, which can ultimately increase sensitivity of single-cell methods. However, combination of both methods in one paper, without comparison of other technologies decrease impact and importance both of them. I.e. Pokhilko et. al (2021) presented targeted single-cell RNA-Seq, which increase sensitivity of Smart-Seq2 too.

In my opinion, separated publication of both methods will be better. While down-scaled Smart-Seq2 is often discussed in Core Facilities to bring scRNA-Seq to more biologist and clinician, scRT-dPCR is very interesting but specific method.

I'm focused in the RNA-Sequencing from sample preparation to data analysis. I'm helping people with optimization of the design to get as much information as possible. I wasn't able to say, if used statistical methods are correct.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

This study aimed to validate the lack of representability of lowly expressed genes by using an integrated workflow of downscaled Smar-seq2 and absolute quantitative, single-cell digital PCR. They addressed the issue of biased/mismatch of data of lowly expressed genes when comparing sc-RNA-seq and RTqPCR which arises due to dropouts of lowly expressed genes in scRNA-seq. They leveraged the sensitivity of scRT-ddPCR in addressing this issue.

The team made a great effort to address the issues related to coverage and quantity of transcriptome analysis. by combining down-scaled sc RNA-seq and scST-ddPCR. They harnessed the inherent portioning of the dPCR which effectively increases the sensitivity that is lacking in sc RNA-seq when it comes to low-abundant mRNAs. They developed a novel, integrated workflow combining down-scaled, single-cell Smart-seq2 and absolute quantitative, single-cell digital PCR. They further validated the workflow by comparative clustering from published data sets and their scRT-ddPCR datasets by contrasting absolute mRNA counts to bulk methods.

The key conclusions of the study are satisfying and supported by the experimental design and robust experiments. Data and methods are well-presented and are reproducible. The manuscript is articulate, and well-written, the data provided are of high standards and help the reader easier understand, especially the graphical abstract.

I have no major comments, but a few minor changes are encouraged.

1. Figure 1. B and C figure's axes are not easy to read even at highest zoom. At least the 400 bp in the x axis could be represented using a bigger font.
2. Figure S4. 'for in in range' needs some attention.
3. P5, line 148 is not clear to me.

Significance

scRNA-seq is a great tool for characterizing cells. However, the issue of losing the lowly expressed genes due to dropouts and also the variation in the fold change found between the bulk methods and ddPCR is one of the challenges. The authors took a nice strategy to address these issues through their effective workflow. The authors performed a thorough comparison between the data from scRNA-seq and ddPCR and their workflow showed to be very effective in addressing the issue of biased conclusions which substantiate their findings. Furthermore, by investigating the workflow in two different cell lines convincingly corroborates their results.

This manuscript is well-written, experiments are thoroughly performed, the findings are convincing and it clearly is an important contribution to the scientific community. Great piece of work and I wish the authors all the best.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The manuscript by Lange et.al described two methods, down-scaled sc-SMART-seq 2 and sc-droplet-based digital PCR for quantification of gene expression at single-cell level. By plate-based analysis of two cell lines, MCF-7 and BT-474, the authors claimed that their methods could achieve high sensitivity and accuracy in single cell gene expression quantification, in particular for the digital PCR strategy. In my opinion, this major conclusion is not sufficiently convincing, given that

1. The authors did not compare their results with standard SMART-seq2 in detection sensitivity (comparison on UMAP clustering is really trivial, and cannot serve the purpose)
2. Fig3b, there are a total of four groups of comparison, two genes X two cell lines. In one of the four, i.e. ACTB in MCF7, the quantification among the three methods differ significantly. Given no ground truth here, it is hardly to judge the quality of their method. The author should add ERCC spike-in to control their experiments as stated in their Discussion.
3. Fig4b, ACTB in BT-474, it seems that the scDDPCR resulted in more cells in the first bin than scRNA-seq. This is in contrast to their claim of higher detection sensitivity of the former.

To assess the performance of their methods in a more systematic manner, the authors should perform the single cell measurements with ERCC spike-in, and check at least 5-10 endogenous genes at different expression level, in addition to the spike-in RNAs. They should choose cell lines for which the absolute no. of RNA for some house-keep genes has been measured using imaging based methods.

Minor concern

1. Fig.1a,b, in ROI, there are overlap between "printed cells" and "detected particles"? How to distinguish between the two?
2. Fig2d, what is the difference between DEG and "different genes"? The no. different genes is not specified for STAR?
3. It is not clear how the bulk samples(Fig.3,4) were prepared.

Significance

The two methods described in the manuscript represent little technical advance. In addition, the conclusion stated in the manuscript is also not sufficiently convincing. As such, it would be of little interest to limited group of audience.

I have been working in the field of genomics, in particularly transcrptomics for the last 20 years. In the last few years, my lab has been developing single-cell omics related methods.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

---

Reply to the Reviewers


We appreciate the time and effort that the reviewers dedicated to providing feedback on our manuscript and are grateful for the insightful comments on and valuable improvements to our paper.

Here is a point-by-point response to the reviewers’ comments and concerns.

Reviewer #1 (Evidence, reproducibility and clarity (Required)): *

Summary:

In this manuscript, Kashiwagi and colleagues examine the role of the BAF complex subunit Smarce1 in mouse ESC. They utilize a gene trap methodology to generate a Smarce1-null cell line (m/m) as well as a Smarce1-rescue cell line (r/r) in which the gene trap is excised. The Smarce1-null cell line exhibited abnormal colony morphology and elevated Nanog expression.

The authors use several approaches to examine the effects of Smarce1 loss on the chromatin characteristics of mouse ESC. Using salt extraction, they show that depletion of Smarce1 causes nucleosome instability, as marked by enhanced solubility of Histone H3. Using immunoprecipitation and sucrose gradient experiments, they suggest that decreased nucleosome stability is due to loss of Arid1a from the BAF complex and improper targeting of the complex to heterochromatin. This improper targeting of the BAF complex to heterochromatin causes a decompaction of heterochromatin foci, potentially due to disruption or displacement of the PRC2 complex. The changes alter the differentiation potential of the m/m mESC, which exhibit abnormal mesoderm differentiation and enhanced neural differentiation. Taken together, these data suggest that Smarce1 is a critical component of the BAF complex that is required for proper targeting of the complex within the chromatin environment.

Major Comments: *

• Throughout the manuscript, the authors make conclusive statements about differences in the intensity or pattern of bands in western blots or DNA gels. However, these statements are purely qualitative, and the authors fail to provide any information about the number of replicates performed. As such, there is no way to judge the statistical significance of the observed changes and it is difficult to have confidence in any of the conclusions drawn from these experiments. *

Responses

We thank the reviewer for the insightful comments. Many of the results presented in this paper were validated multiple times prior to the initial submission. We plan to compile these data, conduct further experiments, and perform quantitative analyses to demonstrate the reproducibility of our findings.

*1. Figure 2b: requires validation through multiple replicates. Ideally, the bands would be quantified and data from multiple replicates can be used for statistical analysis. *

Responses

As suggested by the reviewer, we plan to present quantified data from multiple replicates.

*2. Figure 2d: as depicted, it is impossible to draw any conclusions. To assess the stability or "looseness" of nucleosomes, the authors should perform lane densitometry to compare the relative intensity of the bands within the lanes as well as the spacing of the bands. *

Responses

We appreciate the reviewer’s critical comments. Because the nucleosome repeat length changes due to chromatin structure alteration, it is extremely important to compare the spacing of the bands between the wt, r/r, and m/m cells. As suggested by the reviewer, we plan to perform a quantitative analysis of the band intensity and band spacing.

*3. Figure 3: the authors claim that Arid1a pulldown is decreased in the m/m cells whereas there is no change in BRD9 pulldown between the cell lines. However, there is a decrease in BRD9 pulldown in the r/r cell line that appears equal to the decrease of Arid1a in the m/m cells. Multiple replicates and quantification should be provided to validate the findings, otherwise the reported differences seem to just be judgement calls. *

Responses

As suggested by the reviewer, we plan to present quantitative data from multiple replicates to confirm the observations of the Arid1a and Brd9 pulldown assays.

*4. Figure 3: the immunoprecipitations appear to be poorly normalized. For instance, there seems to be more Smarca4 in the m/m input but less Smarca4 in the pulldown. This could suggest that the immunoprecipitation in the m/m cells was less efficient than in the other two cell lines. Again, additional replicates of the experiment seem necessary. *

Responses

As suggested by the reviewer, we plan to present quantitative data from multiple replicates to normalize the efficiency of immunoprecipitation.

5. Figure 4: Validation of the differences observed between the WT and m/m cell line requires multiple replicates of the experiment. Ideally, the bands can be quantified and the data could be presented as line plots or histograms.

Responses

As suggested by the reviewer, we plan to perform a quantitative analysis of the band intensity and present the results in a graph.

6. Figure 6: same issues as Figure 2b. Additionally, the results for Ezh2, HDAC1, and Kap1 are quite different from those depicted in Figure 2b despite the experiment appearing to be identical. This further emphasizes the need for replication of these experiments.

Responses

We thank the reviewer for highlighting this important point. Regarding the data presented in Figure 2b, we analyzed undifferentiated ES cells, and Figure 6e depicts the results of an analysis of differentiated ES cells. It is known that heterochromatin formation is promoted during the differentiation of ES cells. Therefore, we believe that the heterochromatin components such as Ezh2, HDAC1, and Kap1 are more unstable in Figure 6e compared to Figure 2b. In the full revision, we plan to present the difference in heterochromatin formation between the undifferentiated ES cells and differentiated cells using DAPI-staining or an MNase sensitivity assay. Additionally, we observed by immunostaining that the co-localization of Kap1 to heterochromatin is inhibited in the differentiated m/m cells, which is consistent with the observation that Kap1 is more unstable in Figure 6e compared to Figure 2. We plan to present the Kap1 localization data in the full revision. As suggested by the reviewer, we plan to quantify the immunoblot data from multiple replicates and present the reproducibility of the findings illustrated in Figure 6e.

*Additionally, the interpretation of the differentiation experiments in figure 5 is somewhat confusing and raises several questions:

1. In C-E, the m/m embryoid bodies appear to have much denser outgrowths than the WT and r/r embryoid bodies. While panels A and B demonstrate that the m/m embryoid bodies are smaller, the images in C-E seem to suggest that there is much more proliferation in the m/m outgrowths. This could be due to the maintenance of stem cell characteristics suggested by the presence of more Nanog-positive cells. The authors should comment on this phenomenon. *

Responses

We thank the reviewer for this insightful comment. As highlighted by the reviewer, the maintenance of stem cell characteristics in the m/m cells, which is suggested by more Nanog-positive cells, may influence the proliferation of EB outgrowth. Conversely, we believe that the images in C-E alone are insufficient to assess the proliferation of EB outgrowth, and more observation fields must be analyzed. We plan to address this point by evaluating all areas of the EB outgrowth.

*2. The authors should consider additional experiments to test the persistence of pluripotent cells in these assays. For instance, these outgrowths could be dissociated and replated in ESC growth conditions to examine the ability of the cells to form ESC-like colonies (which would indicate retention of pluripotency). *

Responses

We thank the reviewer for this valuable suggestion. We will examine the retention of pluripotency by investigating the proliferation of dissociated EB-outgrowth in the ESC growth condition. We also plan to evaluate the persistence of several pluripotency markers by qRT-PCR or immunostaining.

3. The authors describe the m/m cells as having impaired mesodermal differentiation based on SMA staining and the morphology of SMA-positive cells. While the morphology of SMA-positive cells does look altered in the m/m cells, there is extensive SMA staining. Rather than "impaired" (which suggests that mesodermal differentiation is blocked), the authors should consider describing mesodermal differentiation as "abnormal" or "altered." Examination of alternative mesodermal markers would also be informative.

Responses

We thank the reviewer for the careful evaluation of the staining data. As suggested, we believe that the SMA staining in the m/m cells is “altered” rather than “impaired”. We will revise the manuscript accordingly during the full revision. We also plan to analyze the expression levels of other mesodermal markers by qRT-PCR to further assess the mesodermal differentiation of the m/m cells.

*4. Are there m/m cells in this assay that are double-positive for SMA and BIII tubulin? This would be compelling evidence demonstrating that loss of Smarce1 disrupts normal differentiation pathways. *

Responses

We thank the reviewer for proposing an attractive model for a novel role of Smarce1 in the regulation of cell differentiation. We have carefully reevaluated our staining data. Although we did not conduct double staining of the m/m cells with anti-SMA and BIII tubulin antibodies, the morphologies of the SMA-positive cells and BIII tubulin-positive cells in a single staining are quite different. This suggests that double staining of the m/m cells with anti-SMA and BIII antibodies is unlikely. However, we believe that the present analysis is insufficient to evaluate the effect of the loss of Smarce1 on normal differentiation pathways. scRNA-seq will provide an overall picture of the effect of Smarce1 loss, which we plan to discuss in the full revision.

Minor Comments:

1. Sox2 expression levels should be added to figure 1d.

Responses

As suggested by the reviewers, we plan to add Sox2 expression levels to Figure 1d.

*2. Please define the regions being targeted in the Oct4, Nanog, and Sox2 chip-pcrs. Are these the promoters, enhancers, gene bodies, etc…? *

Responses

We appreciate the reviewer’s comment. The promoter regions were analyzed in all the ChIP-PCRs. We will elaborate on this in the full revision.

*3. The ChIP data in figure1e-k are difficult to read as presented. It would be helpful to group the data by target rather than cell line so that adjacent data points are directly comparable. *

Responses

We appreciate the reviewer’s comment. As suggested, we will group the ChIP data by the target regions in the full revision.

4. On lines 378-379, the authors state there is minimal to no histone acetylation at IAP and LINE1. This clearly contradicts the data shown in Figure 1.

Responses

We appreciate the reviewer’s comment. Our description was misleading. We intended to say that the difference in histone acetylation at IAP and LINE1 was minimal (if detected at all) between the m/m and wt or r/r cells. We will clarify this point in the full revision.

*5. Are other BAF subunits disrupted in the m/m cells? It would be useful to look at Smarcc1/2, BAF180, Smarcd1/2, in figure 3. *

Responses

We appreciate the reviewer’s comment. We believe that the investigation of other BAF subunits is important to substantiate our conclusion of the role of Smarce1 in BAF complex assembly. We plan to add the data for other BAF subunits to Figure 3 in the full revision.

*6. Similarly, the authors mention in the discussion that impaired REST interaction may explain the enhanced neuronal differentiation observed in the m/m cells. In this case, the authors should consider including REST or Sin3a in figures 3 and 4. *

Responses

We thank the reviewer for the insightful comment. We plan to analyze the interaction between Rest and the BAF complex and Rest and chromatin and will present the results in the full revision. We believe that these experiments would be better performed on differentiated cells, as the Rest function would be more pronounced during neural differentiation.

*7. Additional assays/markers for heterochromatin would strengthen the authors' conclusions about impaired heterochromatin formation. For instance, are overall H3K9me3 or H4K20me3 levels different in the m/m cells? What about HP1? *

Responses

As suggested by the reviewer, we plan to analyze the overall levels of heterochromatin markers and present the results in the full revision.

Reviewer #1 (Significance (Required)): *

This work could provide intriguing conceptual advances in the understanding of BAF complex function in mouse ESC. The authors provide sufficient context for this work in their introduction and discussion sections. As referenced in the manuscript, work from several labs has demonstrated the requirement for canonical BAF complexes in mouse ESC. Recent work has also demonstrated the existence of a non-canonical BAF complex that also functions in the maintenance of mouse ESC. SMARCE1 is specific to the canonical BAF complexes, and this work presented here potentially demonstrates the functional requirement for SMARCE1 in canonical BAF complex function. As such, this work is likely to influence an audience with interest in the molecular biology of the BAF complex and chromatin remodeling.

*

* Reviewer #2 (Evidence, reproducibility and clarity (Required)):

This manuscript is a follow-up on a Nature Methods from 2011 (reference 34) describing an astute method to rapidly generate homozygous mutant mouse ES cells. During this study, the authors noticed that inactivation of Smarce1/BAF57, a subunit of the SWI/SNF complex containing an HMG domain, resulted in abnormal morphology of the ES cells. Here, they have extended the characterization of this mutant, and shown that inactivation of BAF57 leaves essentially unaffected the expression of the pluripotency genes Oct3/4, Nanog, and Sox2, while also apparently preserving the MNase digestion patterns, and H3K9ac and H3K9me accumulation at repeats of the L1 or IAP families. In contrast, the mutation causes increased extractability of the Baf250/Arid1a SWI/SNF subunit, of histone H3, and of the transcriptional co-repressor KAP1. Finally, mutant cells were shown to differentiate into smaller embryoid bodies and failed to differentiate properly into mesodermal lineages. The differentiated cells were also found to contain pericentromeric heterochromatin foci of more elongated shape than in the wild types. Based on these observations, the authors propose that inactivation of Smarce1 decreaseb nucleosome stability and impaired heterochromatin formation during differentiation. Overall, the paper is technically sound. Yet, there is also a clear trend towards overinterpretation of the data, and the arguments in favor of a genome-wide impact on chromatin remain week. On the other hand, the impact of the Baf57 mutation on ES cell differentiation and on the extractability of Baf250 and KAP1 are convincing. *

* Specific comments: *

* Figure 1: There seems to be a contradiction between the conclusion from this figure (Increased H3K9ac levels at the Yamanaka gene promoters but not at repeats, suggesting a local impact on chromatin) and the overall conclusion from the paper, proposing a global decrease in stability of the nucleosomes. An ATAC-seq experiment would probably yield a more definitive conclusion. *

Responses

We thank the reviewer for the important comment. As described below, we believe that our explanation was insufficient. In the full revision, we plan to clarify our explanation as follows and conduct additional experiments to substantiate our findings.

We proposed nucleosome instability of the m/m cells based on biochemical analysis. We should have emphasized here that at a salt concentration of 75 mM, at which chromatin is considered intact (Thoma F et al, J Cell Biol 1979, 83 : 403-427, Allan J et al, J Cell Biol 1981, 90 : 279-288), no difference was observed in the nucleosome stability between the wt and m/m cells either in the salt extraction assay (Figure 2B) or the MNase assay (Figure 2D). The difference in nucleosome instability was observed when the nucleosomes were artificially destabilized by increasing the salt concentration. From this observation, we can speculate that it may be difficult to detect the difference in the genomic status between the wt and m/m cells by ATAC-seq because ATAC-seq is performed under the condition where nucleosomes are intact.

However, as the reviewer highlighted, we believe that further experiments are required to assess the extent of the genome-wide effect of the Smarce1 mutation. It is unclear from the current data whether nucleosome instability occurs globally or only in restricted regions of the genome. Additionally, it has not been proven whether nucleosome instability occurs in live cells. Therefore, we plan to investigate nucleosome instability by fluorescence recovery after photobleaching (FRAP) analysis using H2B-mCherry. If we observe increased incorporation of H2B-mCherry into chromatin in FRAP, we can say that nucleosome instability occurs globally in m/m cells. This would also prove that nucleosomes are indeed unstable in live cells. We have already established stable cell lines that express H2B-mCherry in the wt, m/m, and r/r cells and are ready to begin FRAP analysis.

Figure 2: The increased extractability of Kap1 is difficult to see on panel 2B, while it is clear in the sucrose gradient experiments and in the differentiated cells. These sets of experiments (including ARID1a and histone H3) would therefore be much more ro*bust if the different species were quantified on biological replicates (to allow calculation of a p value). Also, the increased extractability of histone H3 is intriguing, pointing toward a global effect on chromatin, while the MNase experiment showing no impact on the nucleosome ladder argues against such an effect (same issue as for Figure 1). It may be worth exploring whether the extracted H3 is nucleosomal (or alternatively not yet incorporated into chromatin). This could eventually be done by a simple Coomassie staining of the different fractions, that would allow tracking of all the 4 histones simultaneously. *

Responses

We thank the reviewer for the important comment. As suggested, we plan to present quantitative data from multiple replicates. We also plan to conduct Coomassie staining to track all four histones in different fractions to examine whether extracted histones are incorporated or not yet incorporated into chromatin.

Figure *3: It is not clear why the authors connect the sedimentation to a link with heterochromatin, as there is no correlation between distribution of the SWI/SNF subunits and that of histone H3 (while, in contrast, this experiment clearly documents some dissociation of Smarcc1 and the Arid proteins from the rest of the SWI/SNF complex). This should be discussed. Also, the lack of an effect of the BAF57 mutation on histone H3 sedimentation would be in favor of nucleosome remaining intact. *

Responses

(Note: Figure 3 in the reviewer's comment is most likely Figure 4.) Regarding the connection of the sedimentation to a link with heterochromatin, we believe our explanation was insufficient. At a salt concentration of 75 mM as shown, in Figure 4A, a higher-order chromatin structure is maintained (Thoma F et al, J Cell Biol 1979, 83 : 403-427, Allan J et al, J Cell Biol 1981, 90 : 279-288). Thus, the heterochromatin components would tend to distribute in the bottom fractions, while the euchromatin components and free proteins unbound to chromatin would tend to distribute in the top fractions. Since a portion of the esBAF components, such as Smarca4, Arid1a, and Smarcc1, migrated to the bottom fractions in the m/m cells (as evident in fraction 22 in Figure 4A), we interpreted this result as ectopic binding of the BAF complex to heterochromatin. In support on this interpretation, we possess an immunofluorescence data that shows an ectopic co-localization of Smarca4 with heterochromatin markers such as DAPI foci and H3K9me3 in differentiated m/m cells. Smarca4 is normally distributed throughout the nucleoplasm, not at heterochromatin. We plan to present this data in the full revision. A shift in the PRC2 components Ezh2 and Suz12 to the top fractions in the m/m cells is also consistent with the idea that ectopic heterochromatin localization of the BAF complex evicted PRC2 from the heterochromatin. However, we cannot discount the possibility that the migration of BAF components to the bottom fractions was caused by other factors, such as the binding of the Smarce1 (BAF57)-deficient BAF complex with a large protein complex. We will discuss this point in the full revision.

Concerning the lack of effect of the Smarce1 mutation on histone H3 sedimentation, we thank the reviewer for highlighting this. A lack of histone H3 sedimentation at a salt concentration of 75 mM is expected because chromatin is generally considered to be intact under this condition, as mentioned above. Conversely, histone H3 is expected to shift toward the top fractions in the m/m cells at a salt concentration of 300 mM, given that the dissociation of histone H3 increased with increasing salt concentration (as shown in Figure 2B). The band images of histone H3 in Figure. 4B are partially saturated and were not appropriate for quantification. We plan to present adequate images and quantify the density of the histone bands in the results of replicated experiments.

*Figure 6: The modified shape of the pericentromeric foci is remarkable. Their characterization would be greatly improved by 3D reconstruction on their confocal microscope. It will also be important to verify that the effect is not due to an impact of the Baf57 mutation on the cell cycle. A FACS analysis would probably be the best approach, staining with an anti-S10p antibody may also be informative. *

Responses

As suggested by the reviewer, we plan to conduct a 3D reconstruction of the microscopic data and cell cycle analysis.

*Minor point: *

*The information contained in Supplementary Figure 1 is essentially identical to that provided by Wettler et al, Genomics, 1999, one of the original cloning papers of the murine Smarce1. *

Responses

Yeast HNP6A and HNP6B are not presented in Wattler et al. (Genomics, 1999), whereas they were included in the similarity analysis in Supplementary Figure 1. We plan to modify Supplementary Figure 1 to clarify this difference in the full revision.

Reviewer #3 (Evidence, reproducibility and clarity (Required)): *

**This study utilizes mouse embryonic stem cells with homozygous disruption of Smarce1 and those with reversion of Smarce1 to determine the mechanistic function of Smarce1 on cBAF complex assembly, chromatin structure, pluripotency gene expression, and differentiation. The findings indicate that expression of the pluripotency gene, SOX2, increases, and that chromatin structure on Sox2, Nanog, and Oct3/4 becomes more permissible (as evidenced by histone modifications) upon Smarce1 disruption. Other studies suggest that loss of Smarce1 destabilizes nucleosomes and association of chromatin proteins with chromatin. Furthermore, there is disruption of heterochromatin structure and abnormalities in differentiation. *

* Major Concerns: *

* The key conclusion that Smarce1 deficiency impacts upon embryonic stem cell morphology, alters cBAF composition and results in changes in chromatin structure are convincing. However, additional experiments are needed to make many of the specific claims. *

* 1. Fig. 2B indicates that Smarce1 deficiency destabilizes nucleosomes, yet Fig. 2D shows no change in nucleosome positioning. It is suggested that an ATAC-seq experiment be conducted to better determine changes in nucleosome positioning. *

Responses

The nucleosome instability shown in Fig. 2B and no change in nucleosome positioning shown in Fig. 2D seem to be contradictory, but this is due to a lack of an explanation on our part. In the full revision, we plan to include the following explanations and experiments.

It is known that the higher-order structure of chromatin is preserved at a salt concentration of 75 mM (Thoma F et al, J Cell Biol 1979, 83 : 403-427, Allan J et al, J Cell Biol 1981, 90 : 279-288). The nucleosome positioning experiment illustrated in Fig. 2D was performed under this concentration. Conversely, the salt extraction assay depicted in Fig. 2B was performed at concentrations of 75 mM, 150 mM, 300 mM, and 450 mM. It should be emphasized here that under the same 75 mM salt concentration used in the experimental data presented in Fig. 2D, no difference was observed between the wt, m/m, and r/r in Fig. 2B. Therefore, it was assumed that there is little difference in histone-DNA binding between different cell types when looking at static images of chromatin. In contrast, as shown in Fig. 2B, histone dissociation was enhanced by increasing the salt concentration in the m/m cells. This suggests that histones move in and out of chromatin more dynamically in the m/m cells. To examine this dynamic state, we plan to perform FRAP using cells that express H2B-mCherry and quantify the fluidity of histone-DNA binding. We have already established stable cell lines that express H2B-mCherry in the wt, m/m, and r/r cells and are ready to begin FRAP analysis.

As highlighted by the other reviewer, we did not compare the nucleosome repeat length between the wt, r/r, and m/m cells. Because the nucleosome repeat length changes due to chromatin structure alteration, we plan to measure the nucleosome repeat length of these cells.

*2. Fig. 4A shows Arid1a but not Smarca4 migrated at fractions 4 and 6, suggesting that Arid1a is dissociated from the BAF complex. However, there was an increase in BAF components, Smarc1/2 and Smarca4 migrating to the bottom of the sucrose gradient despite the absence of Smarce1 and dissociation of Arid1a. The authors took the lack of size reduction in the complex to mean that in the absence of Smarce1 and dissociation of Arid1a, there is inappropriate interaction of the BAF complex with heterochromatin. Although this is a possibility, there are other possibilities that explain the observation. There could be an increase in PBAF association or association with other proteins that cause the shift. Co-localization studies, chromatin immunoprecipitations or cut and run could more clearly show that there are changes in the interaction of BAF components with heterochromatin. Also, the data is not convincing that there is an increase in the migration of PRC2 components to the top of the gradient. *

Responses

We thank the reviewer for their insightful comments. Regarding the interaction of the BAF components with heterochromatin in the m/m cells, we have the following supportive data which were not shown in our initial manuscript. Using immunostaining, we found an ectopic co-localization of Smarca4 with heterochromatin markers such as DAPI foci and H3K9me3 in differentiated m/m cells. Smarca4 is normally distributed throughout the nucleoplasm. Therefore, this observation supports an ectopic distribution of the BAF complex to heterochromatic regions in m/m cells. We plan to present this result in the full revision. As suggested by the reviewer, we believe that the possibility of the association of the BAF complex with other proteins remains, regardless of the results of the co-localization study. We plan to discuss this point in the full revision.

Regarding the migration of the PRC2 components to the top of the gradient, we plan to present quantitative data from multiple replicates. We speculate that the PRC2 components that migrated to the top fractions are evicted from heterochromatic regions and exist in the nucleoplasm as chromatin-unbound proteins. To investigate this possibility, we plan to conduct FRAP analysis using EGFP-Ezh2. The quicker recovery of the fluorescent signal of EGFP-Ezh2 in m/m cells than wt and r/r cells would indicate an unstable association of Ezh2 with chromatin in m/m cells. The result would also support the notion of the ectopic migration of PRC2 to the top fractions.

*3. Fig. 5 nicely shows changes that Smarce1 disruption causes changes in the ability of the ES cells to differentiate. However, to more convincingly show that Smarce1 compromises endodermal differentiation and enhances ectodermal differentiation, it will be important to look at expression of some lineage specific markers. *

Responses

As suggested by the reviewer, we will analyze the expression of several lineage-specific markers by qRT-PCR.

*4. What is different about Fig. 6A compared to Fig. 2B? In combination, Figs 2B and Fig. 6A indicate that both BAF and PRC2 components and other repressor proteins have looser association with chromatin. How does this result in a shift in BAF components to heterochromatin compartments while PRC2 is lost from these compartments? Additional experiments are needed to support this claim especially since the changes in migration of PRC2 components is very small as shown in Fig. 4A. *

Responses

(Note: Fig. 6A in the reviewer's comment is most likely Fig. 6E.)

We thank the reviewer for the important comment. Regarding the difference between Figure. 6 and Figure. 2B, we believe that our explanation was insufficient. Regarding the data presented in Figure 2B, we analyzed undifferentiated ES cells, and in Figure 6E, we analyzed differentiated ES cells. It is known that heterochromatin formation is promoted during the differentiation of ES cells. For this reason, we believe that heterochromatin components such as Ezh2, HDAC1, and Kap1 are more unstable in Figure 6 compared to Figure 2B. We plan to present the difference in heterochromatin formation between the undifferentiated ES cells and differentiated cells using DAPI-staining or an MNase sensitivity assay in the full revision. Additionally, we observed by immunostaining that co-localization of Kap1 to heterochromatin is inhibited in the differentiated m/m cells, which is consistent with the observation that Kap1 is more unstable in Figure 6E compared to Figure 2. We plan to show the Kap1 localization data in the full revision.

Regarding the shift in the BAF components to heterochromatin compartments and the loss of PRC2 from these compartments, we believe that additional experiments are required to support this theory. As the reviewer observed, the migration of PRC2 to the top fractions is small in Figure 4A. We plan to conduct FRAP analysis using EGFP-Ezh2 to demonstrate an unstable association of Ezh2 with chromatin in m/m cells as mentioned above. Alternatively, we will perform a salt extraction assay of PRC2 in the differentiated cells to evaluate the strength of the interaction of PRC2 with chromatin in the m/m cells.

Minor concerns:

* 1. The Smarca4 co-IP in Fig. 3 should account for the apparent decrease in Smarca4 immunoprecipitation from the mutant ES cells as well as the variable inputs. It would be better to repeat this experiment to get more consistent inputs between the cell lines and more consistent Smarca4 IPs. Alternatively, quantitation of the IPs relative to inputs would help convince readers that there is a decreased association between Smarca4 and Arid1a but not Brd9. *

Responses

As suggested by the reviewer, we plan to present quantitative data from multiple replicates.

2. In Fig. 4A , it looks like Arid1b also migrates at fractions 4 and 6 in mutant ES cells. There should be discussion on this.

Responses

We thank the reviewer for the important remark. As highlighted by the reviewer, Arid1b migrates toward the top fractions in mutant ES cells. We confirmed the reproducibility of this finding. As we mentioned in the Introduction section, Arid1b is not included in the esBAF complex and is thought to be incorporated into the BAF complex during differentiation. ES cells cultured in a serum-containing medium, which was used in this study, are known to fluctuate between undifferentiated and partially differentiated states. We believe that the effect of the loss of Smarce1 on the migration of Arid1b indicates the presence of an Arid1b-containing BAF complex in partially differentiated ES cells. We plan to discuss this point in the full revision.

3. Throughout the text, it is claimed that GBAF is not affected, yet only BRD9 is interrogated. Without experiments on other GBAF subunits, it is better to conclude that one subunit is not affected rather than the whole GBAF complex.

Responses

We agree with the reviewer’s comment that the analysis of Brd9 alone is insufficient to make a conclusion regarding the GBAF complex. We plan to perform an immunoprecipitation assay for other GBAF subunits to clarify the effect of the loss of Smarce1 on the GBAF complex.

*4. The figure legends should indicate how many independent experiments each dataset represents. *

Responses

As suggested by the reviewer, we will indicate the number of independent experiments in the figure legends in the full revision.

*5. There should be discussion on the findings of this study in context with the recently published manuscript on the relationship between SMARCE1 and BRD9 (PMID: 35681054). *

Responses

We thank the reviewer for highlighting this important paper. As mentioned above, we plan to analyze other GBAF subunits to clarify the relationship between Smarce1 and Brd9. Based on those results, we will discuss our findings in light of the above-mentioned paper.

Reviewer #3 (Significance (Required)): *

Significance: This manuscript provides both technical and conceptual advances. The construction of embryonic stem cells with homozygous disruption and reversion of Smarce1 is a technical advance. Although a recent publication ( PMID: 35681054) just showed that Smarce1 disruption destabilizes cBAF complexes, there are other novel conceptual insights provided by this study that are significant. The mechanistic insights into Smarce1 function in embryonic stem cells should be of interest to the chromatin community. Furthermore, since Smarce1 is disrupted in meningiomas and in Coffin-Siros syndrome, it should be of interest to the cancer and developmental biology fields. My expertise is in SWI/SNF chromatin remodeling during cellular differentiation and in cancer. *

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

This study utilizes mouse embryonic stem cells with homozygous disruption of Smarce1 and those with reversion of Smarce1 to determine the mechanistic function of Smarce1 on cBAF complex assembly, chromatin structure, pluripotency gene expression, and differentiation. The findings indicate that expression of the pluripotency gene, SOX2, increases, and that chromatin structure on Sox2, Nanog, and Oct3/4 becomes more permissible (as evidenced by histone modifications) upon Smarce1 disruption. Other studies suggest that loss of Smarce1 destabilizes nucleosomes and association of chromatin proteins with chromatin. Furthermore, there is disruption of heterochromatin structure and abnormalities in differentiation.

Major Concerns:

The key conclusion that Smarce1 deficiency impacts upon embryonic stem cell morphology, alters cBAF composition and results in changes in chromatin structure are convincing. However, additional experiments are needed to make many of the specific claims.

1. Fig. 2B indicates that Smarce1 deficiency destabilizes nucleosomes, yet Fig. 2D shows no change in nucleosome positioning. It is suggested that an ATAC-seq experiment be conducted to better determine changes in nucleosome positioning.
2. Fig. 4A shows Arid1a but not Smarca4 migrated at fractions 4 and 6, suggesting that Arid1a is dissociated from the BAF complex. However, there was an increase in BAF components, Smarc1/2 and Smarca4 migrating to the bottom of the sucrose gradient despite the absence of Smarce1 and dissociation of Arid1a. The authors took the lack of size reduction in the complex to mean that in the absence of Smarce1 and dissociation of Arid1a, there is inappropriate interaction of the BAF complex with heterochromatin. Although this is a possibility, there are other possibilities that explain the observation. There could be an increase in PBAF association or association with other proteins that cause the shift. Co-localization studies, chromatin immunoprecipitations or cut and run could more clearly show that there are changes in the interaction of BAF components with heterochromatin. Also, the data is not convincing that there is an increase in the migration of PRC2 components to the top of the gradient.
3. Fig. 5 nicely shows changes that Smarce1 disruption causes changes in the ability of the ES cells to differentiate. However, to more convincingly show that Smarce1 compromises endodermal differentiation and enhances ectodermal differentiation, it will be important to look at expression of some lineage specific markers.
4. What is different about Fig. 6A compared to Fig. 2B? In combination, Figs 2B and Fig. 6A indicate that both BAF and PRC2 components and other repressor proteins have looser association with chromatin. How does this result in a shift in BAF components to heterochromatin compartments while PRC2 is lost from these compartments? Additional experiments are needed to support this claim especially since the changes in migration of PRC2 components is very small as shown in Fig. 4A.

Minor concerns:

1. The Smarca4 co-IP in Fig. 3 should account for the apparent decrease in Smarca4 immunoprecipitation from the mutant ES cells as well as the variable inputs. It would be better to repeat this experiment to get more consistent inputs between the cell lines and more consistent Smarca4 IPs. Alternatively, quantitation of the IPs relative to inputs would help convince readers that there is a decreased association between Smarca4 and Arid1a but not Brd9.
2. In Fig. 4A , it looks like Arid1b also migrates at fractions 4 and 6 in mutant ES cells. There should be discussion on this.
3. Throughout the text, it is claimed that GBAF is not affected, yet only BRD9 is interrogated. Without experiments on other GBAF subunits, it is better to conclude that one subunit is not affected rather than the whole GBAF complex.
4. The figure legends should indicate how many independent experiments each dataset represents.
5. There should be discussion on the findings of this study in context with the recently published manuscript on the relationship between SMARCE1 and BRD9 (PMID: 35681054).

Significance

This manuscript provides both technical and conceptual advances. The construction of embryonic stem cells with homozygous disruption and reversion of Smarce1 is a technical advance. Although a recent publication ( PMID: 35681054) just showed that Smarce1 disruption destabilizes cBAF complexes, there are other novel conceptual insights provided by this study that are significant. The mechanistic insights into Smarce1 function in embryonic stem cells should be of interest to the chromatin community. Furthermore, since Smarce1 is disrupted in meningiomas and in Coffin-Siros syndrome, it should be of interest to the cancer and developmental biology fields.

My expertise is in SWI/SNF chromatin remodeling during cellular differentiation and in cancer.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

This manuscript is a follow-up on a Nature Methods from 2011 (reference 34) describing an astute method to rapidly generate homozygous mutant mouse ES cells. During this study, the authors noticed that inactivation of Smarce1/BAF57, a subunit of the SWI/SNF complex containing an HMG domain, resulted in abnormal morphology of the ES cells.

Here, they have extended the characterization of this mutant, and shown that inactivation of BAF57 leaves essentially unaffected the expression of the pluripotency genes Oct3/4, Nanog, and Sox2, while also apparently preserving the MNase digestion patterns, and H3K9ac and H3K9me accumulation at repeats of the L1 or IAP families.

In contrast, the mutation causes increased extractability of the Baf250/Arid1a SWI/SNF subunit, of histone H3, and of the transcriptional co-repressor KAP1. Finally, mutant cells were shown to differentiate into smaller embryoid bodies and failed to differentiate properly into mesodermal lineages. The differentiated cells were also found to contain pericentromeric heterochromatin foci of more elongated shape than in the wild types.

Based on these observations, the authors propose that inactivation of Smarce1 decreaseb nucleosome stability and impaired heterochromatin formation during differentiation. Overall, the paper is technically sound. Yet, there is also a clear trend towards overinterpretation of the data, and the arguments in favor of a genome-wide impact on chromatin remain week. On the other hand, the impact of the Baf57 mutation on ES cell differentiation and on the extractability of Baf250 and KAP1 are convincing.

Specific comments:

Figure 1: There seems to be a contradiction between the conclusion from this figure (Increased H3K9ac levels at the Yamanaka gene promoters but not at repeats, suggesting a local impact on chromatin) and the overall conclusion from the paper, proposing a global decrease in stability of the nucleosomes. An ATAC-seq experiment would probably yield a more definitive conclusion.

Figure 2: The increased extractability of Kap1 is difficult to see on panel 2B, while it is clear in the sucrose gradient experiments and in the differentiated cells. These sets of experiments (including ARID1a and histone H3) would therefore be much more robust if the different species were quantified on biological replicates (to allow calculation of a p value). Also, the increased extractability of histone H3 is intriguing, pointing toward a global effect on chromatin, while the MNase experiment showing no impact on the nucleosome ladder argues against such an effect (same issue as for Figure 1). It may be worth exploring whether the extracted H3 is nucleosomal (or alternatively not yet incorporated into chromatin). This could eventually be done by a simple Coomassie staining of the different fractions, that would allow tracking of all the 4 histones simultaneously.

Figure 3: It is not clear why the authors connect the sedimentation to a link with heterochromatin, as there is no correlation between distribution of the SWI/SNF subunits and that of histone H3 (while, in contrast, this experiment clearly documents some dissociation of Smarcc1 and the Arid proteins from the rest of the SWI/SNF complex). This should be discussed. Also, the lack of an effect of the BAF57 mutation on histone H3 sedimentation would be in favor of nucleosome remaining intact.

Figure 6: The modified shape of the pericentromeric foci is remarkable. Their characterization would be greatly improved by 3D reconstruction on their confocal microscope. It will also be important to verify that the effect is not due to an impact of the Baf57 mutation on the cell cycle. A FACS analysis would probably be the best approach, staining with an anti-S10p antibody may also be informative.

Minor point:

The information contained in Supplementary Figure 1 is essentially identical to that provided by Wettler et al, Genomics, 1999, one of the original cloning papers of the murine Smarce1.

Significance

Some interesting observations, but overall, a modest contribution to the field.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript, Kashiwagi and colleagues examine the role of the BAF complex subunit Smarce1 in mouse ESC. They utilize a gene trap methodology to generate a Smarce1-null cell line (m/m) as well as a Smarce1-rescue cell line (r/r) in which the gene trap is excised. The Smarce1-null cell line exhibited abnormal colony morphology and elevated Nanog expression.

The authors use several approaches to examine the effects of Smarce1 loss on the chromatin characteristics of mouse ESC. Using salt extraction, they show that depletion of Smarce1 causes nucleosome instability, as marked by enhanced solubility of Histone H3. Using immunoprecipitation and sucrose gradient experiments, they suggest that decreased nucleosome stability is due to loss of Arid1a from the BAF complex and improper targeting of the complex to heterochromatin. This improper targeting of the BAF complex to heterochromatin causes a decompaction of heterochromatin foci, potentially due to disruption or displacement of the PRC2 complex. The changes alter the differentiation potential of the m/m mESC, which exhibit abnormal mesoderm differentiation and enhanced neural differentiation. Taken together, these data suggest that Smarce1 is a critical component of the BAF complex that is required for proper targeting of the complex within the chromatin environment.

Major Comments:

Throughout the manuscript, the authors make conclusive statements about differences in the intensity or pattern of bands in western blots or DNA gels. However, these statements are purely qualitative, and the authors fail to provide any information about the number of replicates performed. As such, there is no way to judge the statistical significance of the observed changes and it is difficult to have confidence in any of the conclusions drawn from these experiments.

1. Figure 2b: requires validation through multiple replicates. Ideally, the bands would be quantified and data from multiple replicates can be used for statistical analysis.
2. Figure 2d: as depicted, it is impossible to draw any conclusions. To assess the stability or "looseness" of nucleosomes, the authors should perform lane densitometry to compare the relative intensity of the bands within the lanes as well as the spacing of the bands.
3. Figure 3: the authors claim that Arid1a pulldown is decreased in the m/m cells whereas there is no change in BRD9 pulldown between the cell lines. However, there is a decrease in BRD9 pulldown in the r/r cell line that appears equal to the decrease of Arid1a in the m/m cells. Multiple replicates and quantification should be provided to validate the findings, otherwise the reported differences seem to just be judgement calls.
4. Figure 3: the immunoprecipitations appear to be poorly normalized. For instance, there seems to be more Smarca4 in the m/m input but less Smarca4 in the pulldown. This could suggest that the immunoprecipitation in the m/m cells was less efficient than in the other two cell lines. Again, additional replicates of the experiment seem necessary.
5. Figure 4: Validation of the differences observed between the WT and m/m cell line requires multiple replicates of the experiment. Ideally, the bands can be quantified and the data could be presented as line plots or histograms.
6. Figure 6: same issues as Figure 2b. Additionally, the results for Ezh2, HDAC1, and Kap1 are quite different from those depicted in Figure 2b despite the experiment appearing to be identical. This further emphasizes the need for replication of these experiments

Additionally, the interpretation of the differentiation experiments in figure 5 is somewhat confusing and raises several questions:

1. In C-E, the m/m embryoid bodies appear to have much denser outgrowths than the WT and r/r embryoid bodies. While panels A and B demonstrate that the m/m embryoid bodies are smaller, the images in C-E seem to suggest that there is much more proliferation in the m/m outgrowths. This could be due to the maintenance of stem cell characteristics suggested by the presence of more Nanog-positive cells. The authors should comment on this phenomenon.
2. The authors should consider additional experiments to test the persistence of pluripotent cells in these assays. For instance, these outgrowths could be dissociated and replated in ESC growth conditions to examine the ability of the cells to form ESC-like colonies (which would indicate retention of pluripotency).
3. The authors describe the m/m cells as having impaired mesodermal differentiation based on SMA staining and the morphology of SMA-positive cells. While the morphology of SMA-positive cells does look altered in the m/m cells, there is extensive SMA staining. Rather than "impaired" (which suggests that mesodermal differentiation is blocked), the authors should consider describing mesodermal differentiation as "abnormal" or "altered." Examination of alternative mesodermal markers would also be informative.
4. Are there m/m cells in this assay that are double-positive for SMA and BIII tubulin? This would be compelling evidence demonstrating that loss of Smarce1 disrupts normal differentiation pathways.

Minor Comments:

1. Sox2 expression levels should be added to figure 1d
2. Please define the regions being targeted in the Oct4, Nanog, and Sox2 chip-pcrs. Are these the promoters, enhancers, gene bodies, etc...?
3. The ChIP data in figure1e-k are difficult to read as presented. It would be helpful to group the data by target rather than cell line so that adjacent data points are directly comparable.
4. On lines 378-379, the authors state there is minimal to no histone acetylation at IAP and LINE1. This clearly contradicts the data shown in Figure 1.
5. Are other BAF subunits disrupted in the m/m cells? It would be useful to look at Smarcc1/2, BAF180, Smarcd1/2, in figure 3.
6. Similarly, the authors mention in the discussion that impaired REST interaction may explain the enhanced neuronal differentiation observed in the m/m cells. In this case, the authors should consider including REST or Sin3a in figures 3 and 4.
7. Additional assays/markers for heterochromatin would strengthen the authors' conclusions about impaired heterochromatin formation. For instance, are overall H3K9me3 or H4K20me3 levels different in the m/m cells? What about HP1?

Significance

This work could provide intriguing conceptual advances in the understanding of BAF complex function in mouse ESC. The authors provide sufficient context for this work in their introduction and discussion sections. As referenced in the manuscript, work from several labs has demonstrated the requirement for canonical BAF complexes in mouse ESC. Recent work has also demonstrated the existence of a non-canonical BAF complex that also functions in the maintenance of mouse ESC. SMARCE1 is specific to the canonical BAF complexes, and this work presented here potentially demonstrates the functional requirement for SMARCE1 in canonical BAF complex function. As such, this work is likely to influence an audience with interest in the molecular biology of the BAF complex and chromatin remodeling.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Initial plan – Response to Reviewers’ Comments

We thank the three reviewers for their comments, which on balance were very positive and supportive.

The fundamental relevance and translational impact of our manuscript were reinforced by R1 and R3: The present study ”could provide important insight in the field of malaria vaccinology …” (R1), “…lead to a complete revision in how pre-erythrocytic vaccine candidates are identified and prioritized …” (R3) and “… greatly enhances our understanding of exactly how the dynamics, magnitude and quality of CD8+ T-cell responses are modulated by the timing of antigen expression …” (R3).

R1 acknowledged our use of “using cutting edge molecular biology (techniques)” and our efforts to “… provide proof of the concept of vaccine design by evaluating if accessibility/immunogenicity of the antigen is a decisive feature on vaccine design …”. R3 emphasised that the “… manuscript is well written, concise and with a clear narrative…” and that “… conclusions drawn from the study are well supported by the data presented, and the experiments are thoroughly controlled and sufficiently replicated”.

We have now revised the manuscript based on the reviewer’s comments and clarified valid concerns. Together, we consider the review process very helpful to further enhance the impact of our study. At this point, we have also prepared a Graphical Abstract that summarises the key findings of the manuscript.

We address the Reviewer’s Comments below:

Reviewer #1 (Evidence, reproducibility and clarity):

1. General comments: … a little more of deep analysis of immune responses elicited by the transgenic parasites … how about TRM cells, what is the endogenous responses to SIINFKEL without transferring CD8 + T cells from OTI mice?

… the potential of this study demands to be placed in the context of precedent studies that defined pre-erythrocytic stage CD8+ T cell responses. … the importance of CD8+ liver-resident memory CD8+ T cells from Health’s laboratory

<![endif]-->

We agree with the reviewer that the field of malaria pre-erythrocytic immunology is fast-moving. This is exemplified by the more recent identification of resident memory CD8+ T cells (TRM) that patrol hepatocytes against pathogens, including malaria pre-erythrocytic stages by the Heath laboratory. Whilst the focus of our current work is on assessing the timing of expression and immunogenicity of pre-erythrocytic antigens as crucial features for vaccine design, we concur with the reviewer that the analysis of TRM is of remarkable interest to the malaria field, which we believe is currently out of the scope of the current study. Nonetheless, we have now included this in the discussion to link the findings of our study with the evolving field of TRM (lines 409-420).

Nevertheless, we characterised CD8+ T cells using techniques that are commonplace in studying immunological response in the malaria field, while also adapting our approach to probe responses using more physiological proxies.

<![endif]-->

Whilst we did not specifically phenotype for TRM, we measured CD8+ T cell responses in the livers of immunised mice, utilising isolation methods for intrahepatic or liver-infiltrating lymphocytes (Goossens et al., 1990, PMID: 2202764). CD8+ T cells from the livers of mice immunised by irradiated sporozoites delivered intravenously were analysed following adoptive transfer of naïve CD8+ T cells (Figure 3), as well as quantifying endogenous CD8+ T cells (Figure 4B-D). We also assessed CD8+ T cells from the livers of mice immunised with irradiated sporozoites delivered intradermally (as a proxy for the natural route of infection and parenteral vaccine administration; Figure 4E-G).

As mentioned above, the response from endogenous CD8+ T cell, that is without adoptive transfer of naïve CD8+ T cells, are shown in Figure 4A-C (intravenous immunisation) and Figure 4D-F (intradermal immunisation).

We apologise to the reviewer if these results were not obvious. Accordingly, we have reconfigured the figures to i) colour-coordinate intravenous from intradermal administration of sporozoites in Figure 4, and ii) to allow differentiation of pentamer staining from IFN-g production in Figure 3.

1. … the strategy of gating on Fig2a, it is not clear if they want to track the responses from adoptively transferred CD8+ T cells to vaccine or the endogenous CD8+ T cell responses. In any case, the results is potentially interesting but need clarification.

The purpose of adoptively transferring naïve CD8+ T cells was to augment the frequencies of naïve precursors. We used Kb-SIINFEKL pentamers to visualise the developing CD8+ T cell response, which is a combination of both OT-I and endogenous responses. As mentioned above, we have compared the kinetics of the CD8+ T response in mice administered with OT-I cells (Figure 3) or endogenous responses in the absence of OT-I cells (Figure 4).

1. Fig 2: only the responses on the spleen are studied. In order to support the statement about the two different kinds of immunization, they should assess the responses on the liver.

As pointed out by the reviewer, responses in the liver were not performed for Figure 2, but were assessed in Figures 3 to 5.

1. … lack of methodology in flow cytometry analysis, a viability stain is not used, the gating is not determined by FMO … controls … For activation markers in order to assess the impact of the vaccination authors have to use gating that is already established by some of the papers they mentioned (i.e: Harty lab's studies), … the CD11a label should be CD11ahi and is not stated anywhere.

In our gating strategies we relied on the population of cells with a larger FSC value (healthy cells). In previous experiments we established this population to represent the desired population by staining cells with and without Live/Dead dye. Accordingly, we have found this first gating strategy to be satisfactory and consistently excluded dead cells and cell debris.

We apologise for not showing FMOs and have now included exemplary flow cytometry strategies in Supplementary Figure 2 and 5 to illustrate how we gated for CD8+ T cells from blood, spleen and liver. In addition to FMOs we gated for markers in our pentamer and surface stain panel and restimulation cytokine panel.

We have focused on the enumeration of antigen-specific responses using KbSIINFEKL pentamer staining, and the measurement of the effector molecule IFN-g for the evaluation of responses to SIINFEKL. In both methodologies, responses were co-stained with CD8 and CD11a. The utilisation of the CD11a marker and identifying CD11ahi populations in models of infections were established by the Harty and Badovinac laboratories (Rai et al., 2009, PMID: 19933864). CD11ahi populations discriminate antigen-experienced but not inflammation-driven responses, particularly when analysing polyclonal populations of CD8+ T cells. We have referenced the original publication in the manuscript. Moreover, we have corrected mentions and labels of CD11a+ to CD11ahi throughout the manuscript. Thus, in addition to KbSIINFEKL pentamer and IFN-g stainings, the CD11a marker was used as a confirmatory marker for antigen-driven activation. Furthermore, we also stained the cells for canonical activation markers: CD49d, CD62L and CD44. It is notable that the numbers of CD11ahi, CD49dhi, CD62Llo, CD44hi co-stain with Kb-SIINFEKL pentamer (Figure 2 and Supplementary Figure 3), indicating that the identified cells are of effector/ effector memory phenotypes.

1. Line 165: the statement "massive proliferative activity" is not supported by the figure, moreover there are numbers to support the statement.

We have toned down the term from “massive” to “greater”. We have also altered the sentence to read “… immunisation with CSPSIINFEKL sporozoites led to greater expansion of Kb-SIINFEKL+ CD8+ T cells, 6x larger than that observed with UIS4SIINFEKL sporozoites…” (line 195-196), which is in agreement with that shown in Figure 2D, E.

1. -->IFNg and other cytokines production seems too low and the stimulation assay is poorly performed because CD8 were restimulated ex-vivo only with SIINFEKL peptide in the absence of APC (antigen-presenting cells) with Brefeldin A. Also Authors omitted negative controls ( without SIINFEKL Brefeldin A) to be certain that IFNg production is du to SIINFEKL. Again we don't if they are OTI or endogenous cells.

We have utilised stimulation and flow cytometry protocols that are widely used in the malaria pre-erythrocytic stage field (Hafalla et al., 2013, PMID: 23675294; Jagannathan et al., 2015, PMID: 25520427), as well as other fields (Hosking et al., 2014, PMID: 25015828, Nakiboneka et al., 2019, PMID: 30459072). Notably, CD8+ T cell responses to this eukaryotic pathogen have been widely published to be much lower, in contrast to those evoked by viral and bacterial pathogens (Schmidt et al., 2008, PMID: 18780790).

As suggested, we have now included the corresponding negative controls (restimulation without peptide) in a new Supplementary Figure 6.

1. Fig5. Are the cells from Fig5a,b SIINFEKL positive cells or only CD11a and IFNg? Are they OTI? Controls are missing to show a real IFNg production du to the ex vivo stimulation.

The responses shown in Figure 5 were stimulated with SIINFEKL and stained for CD8+ (gated), CD11ahi, IFN-+. The mice did not receive OT-I cells, thus the data reflects the endogenous response.

1. Fig 6. no percentages are shown in the cytometry plots, figure 6d and c seem to be inverted.

We have now included the percentage in the flow cytometry plots. We apologise for the inversion of Figures 6C and D; this has now been corrected to match the figure legend.

1. For the two strains, authors should show the patency in comparison whit WT parasites (currently presented as data not shown)

We have now included the patencies of WT, CSPSIINFEKL and UIS4SIINFEKL parasites in Supplementary Figure 1f. The transgenic parasites exhibit similar patencies to WT parasites.

1. Fig 6: how did the authors measure Sterile protection and Relative parasite load?

We have detailed the measurements of sterile protection and relative parasite load (level) in the Methodology section. Both methodologies are standard procedures in the malaria pre-erythrocytic stage field.

Reviewer #1 (Significance):

The present study could provide important insight in the field of malaria vaccinology. By using cutting edge molecular biology to express the MCHI restricted epitope SIINFEKL a at different stages of the pre-erythrocytic stage of Plasmodium and used it as a surrogate marker to evaluate the CD8+T cell response to infection. The authors attempt to provide proof of the concept of vaccine design by evaluating if accessibility/immunogenicity of the antigen is a decisive feature on vaccine design. Nevertheless, the potential of this study demands to be placed in the context of precedent studies that defined pre-erythrocytic stage CD8+ T cell responses. the authors failed to fully exploit the tools that they developed (transgenic parasite) by overlooking the last studies describing the importance of CD8+ liver-resident memory CD8+ T cells from Health's laboratory or well characterized CD8 T cells responses defined by Harty's laboratory.

If well place in the context (after revisions) this study will not only be fundamental to the malaria field but to other infectious diseases as well.

Field of expertise: malaria immunology, vaccinology, immunomodulation, CD8+ T cell responses

Reviewer #2 (Evidence, reproducibility and clarity):

The manuscript b Mueller and Gibbins et al titled "Low immunogenicity of malaria pre-erythrocytic stages can be overcome by vaccination" compares how transgenic P. berghei parasites expressing SIINFEKL epitope from ovalbumin, as part of CSP or UIS4 present the respective epitope and how immune responses occur to each of the mutants, mostly in mice pre-treated with 2 x 10 OT-I cells expressing a SIINFEKL-specific TCR.

their data show that when in their normal location CSP is much better than UIS4 to elicit an immune response., and that increasing UIS4 (by raising irradiated parasite numbers) does not greatly improve to reduce the difference.

finally the authors show that mice immunized with ovalbumin can reduce liver infection of either CSPSIINFEKL or UIS4SIINFEKL sporozoite challenge infection

the experiments presented by the authors are in my view well done and controlled, but i feel that sometimes conclusions are a bit beyond what the experimental readouts allow for.

Reviewer #2 (Significance):

1. In fig1 the authors show how mutants were made and that proteins with associated SIINFEKL to CSP or UIS4 localise to correct place. (could all be supplementary or Supplementary Figure 1c, d could be included in Fig1). In Fig2a is shown the gating of SIINFEKL-specific CD8+ T cells (could be supplementary).

We deem the depiction of CSP and UIS4 in Figure 1B and C to be important for the concept and impact of the study. We would like to adhere to common practice in immunology studies and keep one representative flow cytometry gating strategy in the main paper (in Figure 2B), to illustrate an example of our analysis methods going forward.

1. In Fig 2b the authors show that the highest CD8T cell specific for SIINFEKL is on the first day analysed (d4) and I would like to see how day 2 and 3 would look like.<br /> specially because proliferative differences don't seem massive to me, CFSE should decrease with each cell division and reach different fluorescence values if replication numbers differ. however here the CFSE fluorescence signal is similar on d5 fig 2c, indicating a similar number of replicative rounds, but probably a different starting numbers of cells that would replicate. Or that CFS labelling was too low to allow distinguishing the number of replicative rounds occuring in that time. so when the authors conclude that proliferative activity was 6x larger than that observed with UIS4SIINFEKL sporozoites, i think they would have to show before that numbers of cells prior to replication was the same

This is a good suggestion, but unfortunately, we did not perform CFSE experiments on days 2 and 3. We agree that the resulting CD8+ T cell responses to both parasites seem to have similar replication rounds (number of cell division), yet the frequencies of those recruited to the immune response are much more elevated in the CSPSIINFEKL as compared UIS4SIINFEKL parasites (5.05 vs 0.84, respectively – as shown in Figure 2D). A better representation is shown in Figure 2E, which is gated on KbSIINFEKL+, CD11ahi, CD8+ T cells.

For our study, we have used published and standard CFSE labelling protocols (Lundie et al., 2008, PMID: 18799734).

In light of Reviewer 1 and 2 both commenting on our use of terminology regarding proliferation, we altered and corrected the text in the manuscript to address that there is a 6x increase (5.05 vs.0.84) in recruitment of SIINFEKL-specific CD8+ T cells rather than proliferation (line 195-196). The same number of cell divisions were undergone, however the level of expansion was greatly increased when mice were immunised with CSPSIINFEKL.

1. I think it would be nice to show when is infection stopped in these two groups os mice, but looking at EEF in the liver if the two groups of mice.

We believe that the reviewer is referring to the outcomes of the protection experiments. We utilised a widely used quantitative PCR method to quantify the EEF in the liver after challenge of vaccinated mice. We agree with the reviewer that it will be interesting to determine whether the kinetics of killing by vaccine-induced CD8+ T cells of CSPSIINFEKL and UIS4SIINFEKL parasites are different. While presently out of the scope, we would have to establish ex vivo quantitative imaging and hope to advance on this in the future.

14 … could show that an adenovirus carrying UIS4 (and CSP) would result in the same as observed here with the ovalbumin one).**

The vaccine efficacy of an Adenovirus vaccine expressing CSP has been established (Rodrigues et al., 1997, PMID: 9013969; Bruña-Romero et al., 2001, PMID: 11553779; Gilbert et al., 2002, PMID: 11803063. Since there are no known ‘immunodominant’ CD8+ T cell epitopes in UIS4 such a vaccine construct is likely to only serve as negative control.. We and others have previously systematically screened for CD8+ T cell epitopes in the pre-erythrocytic stages, including from UIS4, of Pb, but experimental testing yielded only few peptides, with none from UIS4.

15 … discuss the advantages and problems of the two SPZ and PVM locations, assuming that indeed an adenovirus carrying UIS4/CSP would also result in similar protection upon challenge, regarding potential boost from natural Infection, and how variable/conserved each of the proteins are and what could be expected in field trials ion the falciparum counterpart.

We have now included these points in the discussion. Thus far, the consensus in the field is that T cell responses to pre-erythrocytic stage antigens are low in endemic areas (Heide et al., 2019, PMID: 30949162), and there is a striking paucity of data on the impact of boosting (primary infection vs. multiple infections) in the field (Doolan et al., 1993, PMID: 7680226); Khusmith et al., 1999, PMID: 10774643). Previous work in rodent models has demonstrated that boosting of T cell responses to liver stage antigens is poor (Murphy et al., 2013, PMID: 23530242), and this was also documented for CSP (Hafalla et al., 2003, PMID: 12847268). With the very low responses to UIS4SIINFEKL, we reasoned whether they could be enhanced by increased dose of immunisation. However, Figure 5 rejected this hypothesis.

It is noteworthy that we selected CSP and UIS4 as the best characterized representatives of sporozoite and EEF vacuolar antigens, respectively. Following up on the reviewer’s comments, it would be interesting to contrast the allelic diversity of sporozoite and EEF antigens, since this information will be important for vaccine design.

Reviewer #3 (Evidence, reproducibility and clarity):

1. The authors assume a reader familiarity with the use of ovalbumin, the SIINFEKL epitope, the transgenic T-cell receptor OT-1 mice and adoptive transfer experiments to assay immunogenicity. These concepts are not comprehensively introduced in the introduction, and the relationship between these tools are not delineated sufficiently to allow the non-expert reader to follow the logic and methodology of the experiments right from the start. Background information given in Results (Line 139-144, 204-208) and Discussion section, (Line 288-293) could with advantage be synthesized into one paragraph and presented in the introduction to bring all readers onboard from the start.

We thank the reviewer for this important point and have now addressed this in the introduction which reads as follows:

“To control for epitope specificity, we generated Pb transgenic parasites that incorporate the MHC class I H-2-Kb epitope SIINFEKL, from ovalbumin, in either the CSP or UIS4 protein. The resulting transgenic parasites develop normally as wild-type (WT) Pb in the mosquito vector and mammalian host. However, SIINFEKL would be expressed at the same time and space as its respective Plasmodium protein, enabling the CD8+ T cell response against these proteins to be tracked in an epitope-specific physiological manner. In line with previous studies (8,15), to augment low numbers of CD8+ T cell in the naïve response, cells from OT-I mice, which express SIINFEKL-specific TCRs on their CD8+ T cells, were initially adoptively transferred to mice prior to them receiving sporozoite immunisations” (lines 117-127).

1. Results Page 11 Line 255-260, Figure legend Fig. 6 page 27 Line 258-665 The punchline of the paper is that the despite differences in immunogenicity between γ-irradiated CSP SIINFEKL or UIS4 SIINFEKL sporozoites, both CSP SIINFEKL or UIS4 SIINFEKL are targets of protective CD8+ T-cell responses resulting in sterile immunity in a challenge following vaccination with full-length ovalbumin in OT-I cell recipient mice. This section is a cornerstone for the conclusions of the paper and would benefit from being better supported by its explanatory text and presentation of data.

Firstly, there is a mix up, between panel 6c and 6d, where 6c shows "% Sterile protection" and 6d shows "Parasite load in the liver", while it says the opposite in main text and figure legend.

We apologise for this error, which has now been corrected. We also added more explanatory text in the results section to avoid reader’s missing the punchline and impact of our study, which reads as follows: “Strikingly, contrary to the differential CD8+ T cell responses induced by CSP and UIS4, there was no statistical difference in the protection observed when vaccinated mice were challenged with either CSPSIINFEKL or UIS4SIINFEKL sporozoites. Consistent with these findings, both groups of vaccinated mice challenged with either CSPSIINFEKL or UIS4SIINFEKL sporozoites exhibited sterile protection of comparable levels…” (lines 305-310).

1. Secondly, while it is clear that qPCR is used to measure liver parasite load at 24 hours after challenge. It is not immediately clear from neither main text nor figure legend that sterile immunity is measured by microscopy on blood films. The use of the term "sterile immunity" naturally implies this to the initiated reader, but it should be spelled-out that this was the case and that it was monitored from day 3-14 following challenge, which is outlined only in the methods section. Rewriting and restructuring this section to make this clearer would greatly help guide the reader through the results. Currently it reads at first pass as if qPCR on liver samples harvested at 42 hours was used to generate the data in both 6C and 6D.

We agree that this important point should be consistently described and have now added the necessary clarification in the results (line 310-311) and figure legend (line 799-800) to indicate that we used microscopy to assess blood smears for parasitaemia.

19: Thirdly, protective efficacy here is given as a percentage of those mice that become protected, presumably remaining negative by day 14. Authors should provide the actual blood stage parasitaemia in graph or table format in Figure 6 or as a supplemental figure to show that sterile immunity is obtained and maintained until day 14, and that in the control groups patency develops as normal. This will also give clearer insight into how many mice developed patency in the control groups and at what point break-through was observed.

We have now included prepatency in our manuscript to illustrate if and when non-vaccinated and vaccinated animals became parasitaemic. Mice were monitored up to day 14, after which they were deemed sterilely protected. This is found in the new Supplementary Table 2.

1. In a similar vein, qualitative and / or quantitative presentation of microscopy data of EEFs (as presented in Figure 1C) would strengthen conclusions drawn from the qPCR parasite liver load data.

We have included a graph detailing quantitative data of EEF counts as Supplementary Figure 1E.

1. Fourthly, the authors should also comment on why there is such a great variation in the number of mice used in the different studied groups, it says maximum of n=11 mice per group but one group only has as n=3 mice and another n=4, and make a convincing argument this does not affect the conclusions drawn and statistical analysis undertaken.

In this experiment (Figure 6D), we placed particular emphasis on the quantification of the liver load in AdOVA-immunized mice challenged with UIS4SIINFEKL sporozoites. We included cumulative data from multiple challenge experiments. The other groups of mice serve as controls and consistently displayed high parasite loads in non-immunized or WT sporozoite-challenged controls and very low parasite loads in CSPSIINFEKL sporozoite-challenged mice, respectively.

1. Finally, the authors characterise CD8+ T-cell responses in absence of preceding OT-I adoptive transfer but do not report on whether the ovalbumin-immunization was tried on mice without preceding OT-I cell transplant. Was this tried? If not authors should discuss whether this is likely to be successful or not for readers to understand if both sporozoite and EEF presented antigens are likely to induce sterile immunity in a natural setting without artificial enrichment for epitope specific T-cells.

We thank the reviewer for highlighting this point. We did not vaccinate mice in the absence of OT-I cells. Previous work with Py and Pb_CSP-based adenovirus vaccines yielded only up to 40% sterile immunity, despite up to 97% reduction in parasite load in the liver after challenge with viable sporozoites (Rodrigues et al, 1997, PMID: 9013969; Rodrigues et al., 1998, PMID: 9795385). Thus, we augmented the numbers of naïve antigen-specific CD8+ T cell precursors by adoptively transferring OT-I prior to vaccinating with recombinant adenovirus. This methodology was chosen in order to attain optimal levels of vaccine-induced _effector CD8+ T cells producing IFN-g in a single vaccination, and to obtain reliable frequencies comparable to those achieved by prime-boost vaccinations with recombinant adeno- followed vaccinia viruses, or with peptide-loaded dendritic cells followed by recombinant Listeria. Previous work by colleagues and ourselves have shown that in order to achieve sterile protection in both the Py- and Pb-Balb/c model, vaccine-induced CSP-specific CD8+ T cells must exceed a threshold of >1% of all CD8+ T cells in peripheral blood (Bruña-Romero et al., 2001, PMID: 11553779; González-Aseguinolaza et al., 2003, PMID: 14557672; Schmidt et al, 2011, 21460205). Moreover, B10 backgrounds (including C57BL/6) further increases the threshold necessary for sterile protection through a CD8+ T cell-extrinsic mechanism. In our current study, the mean frequencies of antigen-specific CD8+ T cells induced following adenovirus vaccination was 7.5% (Figure 6C), which translated to 80% sterile protection (combined data from CSSIINFEKL and UIS4SIINFEKL groups).

In the current manuscript, we believe that we have successfully provided proof-of-concept evidence to assess the timing of expression and immunogenicity of pre-erythrocytic antigens as crucial parameters for vaccine design. Nonetheless, we have added a comment in the discussion on our chosen approach to test for vaccine efficacy, and on the importance of achieving relatively high levels of CD8+ T cells to enable high vaccine efficacy:

“Regardless of their differing immunogenicities in the context of parasitic infection, we further demonstrated that both sporozoite and EEF antigens are effectively targeted by antigen-specific effector CD8+ T cells, which were generated by vaccination using priming and boosting with recombinant viruses expressing the epitope. This method of prime-boost using recombinant viruses has been consistently shown to induce high numbers of antigen-specific CD8+ T cells (39-43) necessary for protection(20). Importantly, mice harbouring similarly high levels of vaccine-induced, antigen-specific CD8+ T cells were comparably protected when challenged with either CSPSIINFEKL or UIS4SIINFEKL” (lines 371-379).

1. Line 723, 725 clarify if data is from independent biological repeats, i.e. different infected mice fed to different pots of mosquitoes, in which case the data is sufficiently replicated.

The mosquito infectivity is from 14 different mosquito feedings and the sporozoite numbers per mosquito were calculated from 18 (UIS4SIINFEKL and WT) and 21 (CSPSIINFEKL n=21) independent infections.

1. Page 6 Line 132 Please show blood-stage infection data / growth rates for CSP SINFEKL and UIS4 SINFEKL compared to WT as supplemental figure, if available.

We have now included prepatency data for the two transgenic parasites (Supplementary Figure 1f).

1. Figure 1. If quantitative data is available for EEF, as indicated by the mean numbers with SD given within the microscopy pictures it would be nice to see these plotted. Does the reduced EEF numbers for CSP SINFEKL compared to UIS 4SINFEKL and WT mean anything? If not perhaps worth stating this in figure legend, or consider different presentation. Distracting when looking at the figure.

We have generated a graph depicting the numbers of EEFs developing in vitro from sporozoite of Huh7 cells from two independent experiments. This is now found in Supplementary Figure 1E.

1. Figure 2. Would benefit from a panel with a simple schematic that shows the overall experimental design with irradiation of sporozoites, OT-1 transfer, administration of parasites and sampling with the timings for each event clearly marked out.

We thank Reviewer 3 for this suggestion and have now included timelines of our experimental design for Figure 2, as well Figures 3-6.

1. Figure Panel 2b would benefit from the in-figure legend stating CSP SINFEKL + OT-1, UIS4 SINFEKL + OT-1, WT + OT-1 and OT-1 only. Similar to as in Figure 3.**

We thank the reviewer for this suggestion. Since OT-1 transfer was done in all groups of mice, and, hence, is not a distinctive feature, we have instead included a timeline on top of the graph with clear colour coding showing administration of OT-I cells prior to sporozoite immunisation (Figure 2A). We believe this is sufficient to guide the reader through the figure. Similarly, we reduced the labelling in Figure 3, and instead added a timeline as a reference for the experimental design **(Figure 3A)

1. Figure 3 and Figure 4. Label within figure more clearly what is being measured, i.e. what is the difference between panels a,b,c vs. d,e,f (e.g. intravenously v.s. intradermal administrations), gets confusing since Figure 3 and Figure 4 are very similar within the figures (a,b,c vs. d,e,f) and between the figures.

We thank the reviewer for this suggestion and have now added colour coding to Figures 3 and 4 and an experimental schematic to guide the reader through the data. We have included segregation lines above the flow cytometry plots to further guide the reader, i.e. Figure 3B-D denotes Kb-SIINFEKL pentamer data, while Figure 3E-G denotes IFN-g production following restimulation. Further, in Figure 4 segregation lines have been added and labelled to allow easy discernibility of panels 4B-D (intravenous immunisation of sporozoites) vis-a-vis panels 4E-G (intradermal immunisation of sporozoites).

1. Figure 3, 4, The Panel indicating letters (a, b, c, d...) become smaller as figures get bigger and become hard to read for Figure 3 and Figure 4.

This has now been adjusted, as suggested.

1. Line 158 - Throughout manuscript, when it says administration of WT, CSP SINFEKL and / or UIS4 SINFEKL sporozoites it would be good to always have it preceded by irradiated when referring to irradiated sporozoites, e.g. Line 158 and only use sporozoites on its own when referring to live sporozoites (or even better spell out also when using live sporozoites e.g. Line 255).

We have followed the advice of the reviewer including "g-radiation attenuated” or “live” as appropriate (lines 188, 202-203, 216, 236, 248-249, 260-261, 280 and 299).

1. The authors could measure the total amounts of IFN-ɣ being secreted in the tissues after immunization to both antigens and investigate if the level of other IFN-ɣ secreting cells might compensate for the weak response of CD8+ T cells, particularly against UIS4. If completed it has the potential to help the authors to in more detail understand the mechanism and contributing factors to the successful CD8+ T-cell targeting of UIS4. As antigen protection is dependent not only cellular response but also on antibody responses induced against the antigens, authors should analyze by ELISA IgG and IgM responses induced against the two antigens.

We thank the reviewer for raising interest on possible future directions for our study. We have specifically engineered SIINFEKL to be a part of either CSP or UIS4 and utilised an OVA-expressing adenovirus to focus on CD8+ T cell responses. However, we agree with the great idea from the reviewer that justifies further work in dissecting the multifaceted mechanisms underlying CD8+ T cell-mediated protection to malaria pre-erythrocytic stages, as well as future combinations to assess contributions of antibody responses.

1. Page 6 Line 121-123 he authors reason that addition of the SIINFEKL epitope to the immediate C-terminus of the UIS4 protein might confer enhanced antigen presentation through increase MHC-I antigen presentation. Supplementary experiments particularly a MHC I stabilization assay might help confirm this. Complementary experiments looking at MHC-II antigen presentation to APC would also be very relevant.

We have appended the SIINFEKL to the C-terminus of the UIS4, based on earlier studies in Toxoplasma gondii that the potency of an immunodominant epitope was associated with its C-terminal location, allowing for enhanced presentation by infected cells. Whilst this information is not defined for UIS4, studies on the basic biology of pre-erythrocytic stages have demonstrated for several ETRAMPs (UIS4 is a member of the ETRAMP protein family) that the C-terminus faces the host-cell cytoplasm, which might enhance exposure to the MHC I machinery. Our findings showing that vaccine-induced effector CD8+ T cell responses eliminate both transgenic parasites, argues against potential defects in antigen processing and presentation of SIINFEKL in both systems.

Again, we agree that future studies aiming at dissecting the molecular mechanisms of MHC-I antigen presentation in infected host cells and cross-presentation via MHC-II are warranted. Another long-standing goal of the community is to elude Plasmodium peptides from MHC molecules, similar to the pioneer work by Rammensee and co-workers. One potential, albeit challenging, research direction could be to focus on rare EEF-derived peptides, since they might proof to be excellent and hitherto neglected subunit vaccine candidates, as exemplified in the present proof-of-concept study.

1. The authors have described the effect of both antigens in the response of CD8+ T cells and the generation of memory. A more detailed characterization of the differential phenotypes of memory in CD4 and CD8 T cells in the spleen and liver following immunostimulatory therapy would increase the relevance of the data presented.

We entirely agree that a more detailed characterisation of the different phenotypes of not only memory CD8+, including TRM, but also CD4+ T cell responses, is warranted. Whilst these suggestions clearly inspire further work using the transgenic parasites of this study by colleagues and ourselves, we believe that these are out of the scope of the current study.

Reviewer #3 (Significance):

This paper would be of interest to malaria parasite biologists, immunologists and vaccinologists alike. The significance of this paper is three-fold. Firstly, the authors demonstrate contrasting immunogenic profiles between a sporozoite and EEF presented antigen. They comprehensively characterize respective CD8+ T-cells responses, with the sporozoite expressed antigen displaying enhanced immunogenicity compared to the the EEF expressed antigen. Secondly, the authors demonstrate that despite these stark differences in immunogenicity, both the sporozoite and EEF expressed antigens are effective targets of epitope specific CD8+ T-cell responses capable of eliciting sterile immunity. This has the important implication that low immunogenicity as defined by conventional immunological assay fails to capture all antigens that are capable of inducing sterile immunity, and thus could be prioritized as vaccine targets, but instead risks leading investigators down a path where so to speak "the baby is thrown out with the bath water". Thirdly, this work shows for the first time that EEF expressed antigens are potential vaccine targets, and thus effectively expands the pool of available pre-erythrocytic vaccine targets for the research community to explore.

The data presented here should thereby lead to a complete revision in how pre-eryhtrocytic vaccine candidates are identified and prioritized. In terms of basic biology, the fact that CD8+ T-cells are critical in mediating immunity is been well established, however this paper greatly enhances our understanding of exactly how the dynamics, magnitude and quality of CD8+ T-cell responses are modulated by the timing of antigen expression.

Keywords for main reviewer expertise: Malaria, Plasmodium berghei, genetic manipulation, host-parasite interactions

Keywords for ECR co-reviewer expertise: Immunity, host-pathogen interactions.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary

The study by Müller et al. uses the rodent malaria parasite Plasmodium berghei, which gives access to the mouse in vivo infection model. The authors investigate the initiation and development of CD8+ T cell responses during parasite liver-stage infection when the peptide antigen SIINFEK is presented either early or late during liver-stage infection by fusing SIINFEK to the Circumsporozoite Protein (CSP SIINFEK) or the Up-regulated in Infective Sporozoites 4 protein (UIS4 SIINFEK). CSP is expressed already in the motile sporozoite that invades the liver while UIS4, is expressed only in the later exoerthrocytic forms developing in the infected hepatocytes.

Using the SIINFEK peptide the authors can control for epitope differences between CSP and UIS4 and it allows them to use the OT-I transgenic mouse line that produces high numbers of CD8+ T-cells that specifically recognizes MHC class I presented ovalbumin (OT-I cells), which can be used in adoptive transfer experiments. Using this approach the authors provide detailed kinetic and phenotypic analysis of CD8+ T-cell responses to CSP SIINFEK and UIS4 SIINFEK antigen-specific response in vivo and ex vivo, chiefly using FACS. The authors found that despite having different timing of expression and immunogenicity both CSP SIINFEK and UIS4 SIINFEK induce similar levels of CD8+ mediated targeting, resulting in a high degree of sterile immunity in a vaccination challenge experiment.

Major comments

Overall the manuscript is well written, concise and with a clear narrative. The conclusions drawn from the study are well supported by the data presented, and the experiments are thoroughly controlled and sufficiently replicated. The manuscript is suited for publication but presentation of key concepts and data could be made clearer and impact enhanced if the authors address some of the following commentary.

1. Introduction -The authors assume a reader familiarity with the use of ovalbumin, the SIINFEKL epitope, the transgenic T-cell receptor OT-1 mice and adoptive transfer experiments to assay immunogenicity. These concepts are not comprehensively introduced in the introduction, and the relationship between these tools are not delineated sufficiently to allow the non-expert reader to follow the logic and methodology of the experiments right from the start. Background information given in Results (Line 139-144, 204-208) and Discussion section, (Line 288-293) could with advantage be synthesized into one paragraph and presented in the introduction to bring all readers onboard from the start.
2. Results Page 11 Line 255-260, Figure legend Fig. 6 page 27 Line 258-665 The punchline of the paper is that the despite differences in immunogenicity between γ-irradiated CSP SIINFEKL or UIS4 SIINFEKL sporozoites, both CSP SIINFEKL or UIS4 SIINFEKL are targets of protective CD8+ T-cell responses resulting in sterile immunity in a challenge following vaccination with full-length ovalbumin in OT-I cell recipient mice. This section is a cornerstone for the conclusions of the paper and would benefit from being better supported by its explanatory text and presentation of data.

Firstly, there is a mix up, between panel 6C and 6D, where 6C shows "% Sterile protection" and 6D shows "Parasite load in the liver", while it says the opposite in main text and figure legend.

Secondly, while it is clear that qPCR is used to measure liver parasite load at 24 hours after challenge. It is not immediately clear from neither main text nor figure legend that sterile immunity is measured by microscopy on blood films. The use of the term "sterile immunity" naturally implies this to the initiated reader, but it should be spelled-out that this was the case and that it was monitored from day 3-14 following challenge, which is outlined only in the methods section. Rewriting and restructuring this section to make this clearer would greatly help guide the reader through the results. Currently it reads at first pass as if qPCR on liver samples harvested at 42 hours was used to generate the data in both 6C and 6D.

Thirdly, protective efficacy here is given as a percentage of those mice that become protected, presumably remaining negative by day 14. Authors should provide the actual blood stage parasitaemia in graph or table format in Figure 6 or as a supplemental figure to show that sterile immunity is obtained and maintained until day 14, and that in the control groups patency develops as normal. This will also give clearer insight into how many mice developed patency in the control groups and at what point break-through was observed.

In a similar vein, qualitative and / or quantitative presentation of microscopy data of EEFs (as presented in Figure 1C) would strengthen conclusions drawn from the qPCR parasite liver load data.

Fourthly, the authors should also comment on why there is such a great variation in the number of mice used in the different studied groups, it says maximum of n=11 mice per group but one group only has as n=3 mice and another n=4, and make a convincing argument this does not affect the conclusions drawn and statistical analysis undertaken.

Finally, the authors characterise CD8+ T-cell responses in absence of preceding OT-I adoptive transfer but do not report on whether the ovalbumin-immunization was tried on mice without preceding OT-I cell transplant. Was this tried? If not authors should discuss whether this is likely to be successful or not for readers to understand if both sporozoite and EEF presented antigens are likely to induce sterile immunity in a natural setting without artificial enrichment for epitope specific T-cells. 3. Line 723, 725 clarify if data is from independent biological repeats, i.e. different infected mice fed to different pots of mosquitoes, in which case the data is sufficiently replicated.

Minor comments:

1. Page 6 Line 132 Please show blood-stage infection data / growth rates for CSP SINFEKL and UIS4 SINFEKL compared to WT as supplemental figure, if available.
2. Figure 1. If quantitative data is available for EEF, as indicated by the mean numbers with SD given within the microscopy pictures it would be nice to see these plotted. Does the reduced EEF numbers for CSP SINFEKL compared to UIS 4SINFEKL and WT mean anything? If not perhaps worth stating this in figure legend, or consider different presentation. Distracting when looking at the figure.
3. Figure 2. Would benefit from a panel with a simple schematic that shows the overall experimental design with irradiation of sporozoites, OT-1 transfer, administration of parasites and sampling with the timings for each event clearly marked out.
4. Figure Panel 2b would benefit from the in-figure legend stating CSP SINFEKL + OT-1, UIS4 SINFEKL + OT-1, WT + OT-1 and OT-1 only. Similar to as in Figure 3.
5. Figure 3 and Figure 4. Label within figure more clearly what is being measured, i.e. what is the difference between panels a,b,c vs. d,e,f (e.g. intravenously v.s. intradermal administrations), gets confusing since Figure 3 and Figure 4 are very similar within the figures (a,b,c vs. d,e,f) and between the figures.
6. Figure 3, 4, The Panel indicating letters (a, b, c, d...) become smaller as figures get bigger and become hard to read for Figure 3 and Figure 4.
7. Line 158 - Throughout manuscript, when it says administration of WT, CSP SINFEKL and / or UIS4 SINFEKL sporozoites it would be good to always have it preceded by irradiated when referring to irradiated sporozoites, e.g. Line 158 and only use sporozoites on its own when referring to live sporozoites (or even better spell out also when using live sporozoites e.g. Line 255).
8. The authors could measure the total amounts of IFN-ɣ being secreted in the tissues after immunization to both antigens and investigate if the level of other IFN-ɣ secreting cells might compensate for the weak response of CD8+ T cells, particularly against UIS4. If completed it has the potential to help the authors to in more detail understand the mechanism and contributing factors to the successful CD8+ T-cell targeting of UIS4.

Suggested extra experiments:

1. As antigen protection is dependent not only cellular response but also on antibody responses induced against the antigens, authors should analyze by ELISA IgG and IgM responses induced against the two antigens
2. Page 6 Line 121-123 he authors reason that addition of the SIINFEKL epitope to the immediate C-terminus of the UIS4 protein might confer enhanced antigen presentation through increase MHC-I antigen presentation. Supplementary experiments particularly a MHC I stabilization assay might help confirm this. Complementary experiments looking at MHC-II antigen presentation to APC would also be very relevant.
3. The authors have described the effect of both antigens in the response of CD8+ T cells and the generation of memory. A more detailed characterization of the differential phenotypes of memory in CD4 and CD8 T cells in the spleen and liver following immunostimulatory therapy would increase the relevance of the data presented.

Significance

This paper would be of interest to malaria parasite biologists, immunologists and vaccinologists alike. The significance of this paper is three-fold. Firstly, the authors demonstrate contrasting immunogenic profiles between a sporozoite and EEF presented antigen. They comprehensively characterize respective CD8+ T-cells responses, with the sporozoite expressed antigen displaying enhanced immunogenicity compared to the the EEF expressed antigen. Secondly, the authors demonstrate that despite these stark differences in immunogenicity, both the sporozoite and EEF expressed antigens are effective targets of epitope specific CD8+ T-cell responses capable of eliciting sterile immunity. This has the important implication that low immunogenicity as defined by conventional immunological assay fails to capture all antigens that are capable of inducing sterile immunity, and thus could be prioritized as vaccine targets, but instead risks leading investigators down a path where so to speak "the baby is thrown out with the bath water". Thirdly, this work shows for the first time that EEF expressed antigens are potential vaccine targets, and thus effectively expands the pool of available pre-erythrocytic vaccine targets for the research community to explore.

The data presented here should thereby lead to a complete revision in how pre-eryhtrocytic vaccine candidates are identified and prioritized. In terms of basic biology, the fact that CD8+ T-cells are critical in mediating immunity is been well established, however this paper greatly enhances our understanding of exactly how the dynamics, magnitude and quality of CD8+ T-cell responses are modulated by the timing of antigen expression.

Keywords for main reviewer expertise: Malaria, Plasmodium berghei, genetic manipulation, host-parasite interactions

Keywords for ECR co-reviewer expertise: Immunity, host-pathogen interactions.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The manuscript b Mueller and Gibbins et al titled "Low immunogenicity of malaria pre-erythrocytic stages can be overcome by vaccination" compares how transgenic P. berghei parasites expressing SIINFEKL epitope from ovalbumin, as part of CSP or UIS4 present the respective epitope and how immune responses occur to each of the mutants, mostly in mice pre-treated with 2 x 10 OT-I cells expressing a SIINFEKL-specific TCR.

their data show that when in their normal location CSP is much better than UIS4 to elicit an immune response., and that increasing UIS4 (by raising irradiated parasite numbers) does not greatly improve to reduce the difference.

finally the authors show that mice immunized with ovalbumin can reduce liver infection of either CSPSIINFEKL or UIS4SIINFEKL sporozoite challenge infection

the experiments presented by the authors are in my view well done and controlled, but i feel that sometimes conclusions are a bit beyond what the experimental readouts allow for.

Significance

In fig1 the authors show how mutants were made and that proteins with associated SIINFEKL to CSP or UIS4 localise to correct place. (could all be supplementary or Supplementary Figure 1c, d could be included in Fig1).

In Fig2a is shown the gating of SIINFEKL-specific CD8+ T cells (could be supplementary). In Fig 2b the authors show that the highest CD8T cell specific for SIINFEKL is on the first day analysed (d4) and I would like o see how day 2 and 3 would look like. specially because proliferative differences don't seem massive to me, CFSE should decrease with each cell division and reach different fluorescence values if replication numbers differ. however here the CFSE fluorescence signal is similar on d5 fig 2c, indicating a similar number of replicative rounds, but probably a different starting numbers of cells that would replicate. Or that CFS labelling was too low to allow distinguishing the number of replicative rounds occuring in that time.

so when the authors conclude that proliferative activity was 6x larger than that observed with UIS4SIINFEKL sporozoites, i think they would have to show before that numbers of cells prior to replication was the same

Figs 3 and 4 show that response to CSP is stronger than response to UIS4, and in the spleen larger than in the liver and that this was true for mice adoptively transferred with OT-I cells prior to intravenously immunisation or without that, and that with the transfer responses were much higher.

Fig 5 show that increasing # of irradiated UIS4SIINFEKL 8x does not bring levels of response to anywhere close than the observed against 1x CSPSIINFEKL.

and fig 6 show that if a response is obtained (in the case with an adenovirus expressing ovalbumin which will generate e a response recognising SIINFEKL) both CSPSIINFEKL or UIS4SIINFEKL infection challenge can be blocked and protective immunity equally achieved.

I think it would be nice to show when is infection stopped in these two groups os mice, but looking at EEF in the liver if the two groups of mice.

Also the authors could show that an adenovirus carrying UIS4 (and CSP) would result in the same as observed here with the ovalbumin one).

I also think the authors should discuss the advantages and problems of the two SPZ and PVM locations, assuming that indeed an adenovirus carrying UIS4/CSP would also result in similar protection upon challenge, regarding potential boost from natural Infection, and how variable/conserved each of the proteins are and what could be expected in field trials ion the falciparum counterpart.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this study by Müller et al, the authors study if immunogenicity is an adequate predictor for vaccine development in malaria and more precisely against malaria pre-erythrocytic stage. For that the used two different strains of the murine parasite Plasmodium berghei They based their study on the use of the MCH I restricted epitope SIINFEKL to follow CD8 T cell responses. For that, they integrated the sequence SIINFEKL sequence into the protein CSP expressed by the infective form sporozoite and at the end of the sequence of the protein UIS4 expressed exclusively by the exo-erythrocytic forms (EEF) of the parasite. They compared then the CD8+ T cell responses elicited by each strain of the parasite and came to the conclusion that whilst antigen origin results in very different immunogenicity responses both sporozoite and EEF expressed antigens elicit antigen-specific effector CD8+ T cell responses with a high level of protection.

Major comments:

Whilst rational of parasite strain design is adequate and well-performed and the concept of low immunogenicity novel potentially interesting, there are several methodological flaws that make the conclusions somewhat speculative and need to be addressed to really support the conclusions. Given the fact that authors are top-level scientists in the malaria vaccinology field, I am confident that they can address the following comments that will help to improve the manuscript and its impact;

• General comment: this reviewer was expecting a little more of deep analysis of immune responses elicited by the transgenic parasites that authors developed and not only a superficial analysis, how about TRM cells, what is the endogenous responses to SIINFKEL without transferring CD8 + T cells from OTI mice? This should be addressed

• Fig 2-3: Authors compared the CD8+ T cell responses elicited by the two different strains of P.berghei. In order to evaluated if the two strains allowed to track anti-SIINFEKL, they immunized mice with both irradiated parasite strains or their control WT. To track these responses mice were adoptively transferred with CD8+ T cells from OT-I mice and immunized with irradiated parasites. They track responses by using a SIINFEKL tetramer expressing CD8+ T cells in the blood and the marker for antigen-experienced T cells CD11a. The problem here is that with the strategy of gating on Fig2a, it is not clear if they want to track the responses from adoptively transferred CD8+ T cells to vaccine or the endogenous CD8+ T cell responses. In any case, the results is potentially interesting but need clarification.

  • Fig 2: only the responses on the spleen are studied. In order to support the statement about the two different kinds of immunization, they should assess the responses on the liver.
  • There is also a lack of methodology in flow cytometry analysis, a viability stain is not used, the gating is not determined by FMO (fluorescence minus one) controls and seems aleatory. For activation markers in order to assess the impact of the vaccination authors have to use gating that is already established by some of the papers they mentioned (i.e: Harty lab's studies), it is difficult to evaluate the responses if we don't know how many of the CD11a/Cd49d cells are Memory effector or effector (CD62L and CD44 markers). Moreover, the CD11a label should be CD11ahi and is not stated anywhere.

Line 165: the statement "massive proliferative activity" is not supported by the figure, moreover there are numbers to support the statement. - IFNg and other cytokines production seems too low and the stimulation assay is poorly performed because CD8 were restimulated ex-vivo only with SIINFEKL peptide in the absence of APC (antigen-presenting cells) with Brefeldin A. Also Authors omitted negative controls ( without SIINFEKL Brefeldin A) to be certain that IFNg production is du to SIINFEKL. Again we don't if they are OTI or endogenous cells. - Fig5. Are the cells from Fig5a,b SIINFEKL positive cells or only CD11a and IFNg? Are they OTI? Controls are missing to show a real IFNg production du to the ex vivo stimulation. - Fig 6. no percentages are shown in the cytometry plots, figure 6d and c seem to be inverted. An interesting observation is that the level of protection against both strains of parasites is the same when vaccinated mice with AdOVA are challenged. The authors make the interpretation that immunogenicity does not predict effector responses. This is one of the central conclusions of the paper. The authors only show level of protection but don't characterize the phenotype of CD8+ T cells in the liver of vaccinated and challenged mice. Can cells from Fig6a be find in the liver? Are they liver TRm (resident memory CD8+ T cells), know to be an important class of cells for protection against malaria.

Minor comments:

• For the two strains, authors should show the patency in comparison whit WT parasites (currently presented as data not shown)
• Gating strategy for markers is missing, FMO as well
• Fig 6: how did the authors measure Sterile protection and Relative parasite load?

Significance

The present study could provide important insight in the field of malaria vaccinology. By using cutting edge molecular biology to express the MCHI restricted epitope SIINFEKL a at different stages of the pre-erythrocytic stage of Plasmodium and used it as a surrogate marker to evaluate the CD8+T cell response to infection. The authors attempt to provide proof of the concept of vaccine design by evaluating if accessibility/immunogenicity of the antigen is a decisive feature on vaccine design. Nevertheless, the potential of this study demands to be placed in the context of precedent studies that defined pre-erythrocytic stage CD8+ T cell responses. the authors failed to fully exploit the tools that they developed (transgenic parasite) by overlooking the last studies describing the importance of CD8+ liver-resident memory CD8+ T cells from Health's laboratory or well characterized CD8 T cells responses defined by Harty's laboratory.

If well place in the context (after revisions) this study will not only be fundamental to the malaria field but to other infectious diseases as well.

Field of expertise: malaria immunology, vaccinology, immunomodulation, CD8+ T cell responses

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2022-01501

Corresponding author(s): Prachee Avasthi

[The “revision plan” should delineate the revisions that authors intend to carry out in response to the points raised by the referees. It also provides the authors with the opportunity to explain their view of the paper and of the referee reports.

• *

The document is important for the editors of affiliate journals when they make a first decision on the transferred manuscript. It will also be useful to readers of the reprint and help them to obtain a balanced view of the paper.

• *

If you wish to submit a full revision, please use our "Full Revision" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

• *

We thank the reviewers for their careful reading and evaluation of our manuscript. The reviewers have emphasized the need for several important changes which we plan to address.

First, they request better evidence and specificity of the BCI target in Chlamydomonas. We have created double mutants between the dusp6 ortholog mutants and found severe defects in ciliogenesis similar to what we see with BCI treatment. We plan to include this data in the paper as well as the subsequent analyses we performed with the single dusp6 ortholog mutants. This data will provide stronger evidence that this pathway regulates ciliary length in Chlamydomonas aside from the other potential off target effects that could be impacting this pathway that we may be seeing through the use of BCI.

Second, the reviewers have requested more consistency and clarity both in statistics and descriptions of the data and to expand upon our findings in the discussion. We will create a clear guideline for our use of statistics and adjust the descriptions of the data to fit this guideline more strictly and prevent overstating/oversimplifying results. We will also add more discussion and information related to off target effects of BCI, the importance of the subtle defects in NPHP4 protein expression in the transition zone, and the relevancy of the membrane trafficking data in light of this study.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

---

Reviewer #1 (Evidence, reproducibility and clarity (Required)):____

---

SUMMARY:____

---

The authors investigated the effects of an allosteric inhibitor of DUSP (BCI) on cilia length regulation in Chlamydomonas. Among seven conclusions summarized in Fig. 7, BCI is found to severely disrupt cilia regeneration and microtubule reorganization. Additionally, changes in kinesin-II dynamic, ciliary protein synthesis, transition zone composition and membrane trafficking are also explored. All these aspects have been shown to affect cilia length regulation. Findings from this body of work may give insights on how MAPK, a major player in cilia length regulation, functions in various avenues. Additionally, the study of BCI and other specific phosphatase inhibitors may provide a unique addition to the toolset available to uncover this important and complicated mechanism.

MAJOR COMMENTS

Major comment 1____

The addition of BCI increases phosphorylated MAPK in Chlamydomonas based on Fig 1B. However, the claim that BCI inhibits Chlamydomonas MKPs is not supported at all. SF1A shows CrMKP2, 3 and 5 are related to each other but distant from HsDUSP6 and DrDUSP6. At the same time, 2 out 3 predicted BCI interacting residues are different from the Hs and Dr DUSP6 in SF1B, contradicting "well conserved" in line 172. Consistently, mutants of these orthologs have little to no ciliary length and regeneration defects compared to BCI treatment (see major comment 6 about statistical significance). I am not convinced that BCI inhibits the identified orthologs or any MKPs in Chlamydomonas. It's possible that BCI inhibits a broad range of phosphatases including the ones listed and/or those for upstream kinases. But such a point is not demonstrated by the presented data.

While BCI is predicted to interact with these residues, it is also predicted to interact with the “general acid loop backbone” by fitting in between the a7 helix and the acid loop backbone (Molina et al., 2009).

MKP2 has ciliary length defects compared to wild type, though it regenerates normally. In addition, we have crossed these mutants together and have found that cells (2x3 12.2 and 3x5 29.4) cannot generate cilia. We will include this data in the supplement and perform follow up analyses on these double mutants. Because these structures are not 100% conserved, and we have changed the text to “partially conserved” to reflect this, it is possible that BCI is hitting all of these DUSPs rather than just one, or the DUSPs may serve compensatory functions that rescue ciliary length.

Major comment 3____

The claims that "BCI inhibits KAP-GFP protein expression" (line 271) and "BCI inhibits ciliary protein synthesis" (line 286) are not convincingly demonstrated. Overlooking that only KAP is investigated instead of kinesin-II, none of the relative intensity from the WB in 30 or 50 µM BCI and the basal body fluorescence intensity indicates a statistically significant difference. The washout made no difference in any of the assay and it's not explained how phosphatase inhibition by BCI might affect overall ciliary protein synthesis. The claims about protein expression may need a fair amount of effort and time investment to demonstrate, therefore I suggest leaving these out for this manuscript.

Though it's very interesting to see that in SF 2C cilia in 20 µM BCI treatment can regeneration slowly. Line 162, the author claimed "In the presence of (30 µM) BCI, cilia could not regenerate at all (Fig 1E)". Since Fig 1E only extends to 2 hours, I think it's important to clarify if in 30 µM BCI cilia indeed can not generate even after 6 or 8 hours.

We have altered the text to be more specific with our wording that KAP-GFP is investigated rather than kinesin-2, and we have added text to indicate that downstream phosphorylation events could impact transcription and translation of proteins necessary for ciliary maintenance. This interpretation of the data mentioned above is correct; KAP-GFP is not significantly altered at the basal bodies or in accordance with the steady state western blots. What we see here and demonstrated in Figure 2F-I is the depleted KAP-GFP protein which is not restored following a 2 hour regeneration in BCI. We likely do not see a difference in steady state conditions because the protein is not degraded, just being moved around in the cell. We can only see the difference when the majority of KAP-GFP, which the data suggests is mostly present in cilia, is physically removed through ciliary shedding. This protein is not replaced during a 2 hour regeneration which allows us to conclude that this protein is inhibited due to BCI.

The washout made a small difference in the double regeneration whereby we begin to see cilia begin to form in washed out conditions, though this was not statistically significant. It is possible that BCI has a potent effect on the cell similar to how other drugs, such as colchicine, cannot be easily washed out. The purpose here is to show that regardless of the statistical significance, cells can begin to regenerate their cilia after BCI washout, though this occurs 4 hours after washout in doubly regenerated cells, and we do not see this potent effect on the singly regenerated cells in SF 2C. Though in SF2C, as mentioned, we do see slowly growing cilia, and this could, once again, be due to the potent inhibition BCI has on ciliary protein synthesis. We will confirm and clarify if 30 µM BCI cannot regenerate even after 6 or 8 hours.

Major comment 5____

It is very interesting that BCI disrupts microtubule reorganization induced by deciliation and colchicine. Data in Fig 6B and C are presented differently than those in SF 4C. For example, in SF 4C, BCI treatment for 60 min has close to 50 % cells with microtubule partially reorganized while in Fig 6C about 20% cells with microtubule fully (or combined?) reorganized. The nature of the difference is unclear to me without an assay comparing the two directly. Hence the implied claim that BCI affects colchicine induced microtubule reorganization differently than deciliation induced one is hard to interpret (line 398, line 388 vs line 403).

---

The fact that taxol doesn't rescue cilia regeneration defect by BCI is very interesting. Here taxol treatment results in fully regenerated cilia while Junmin Pan's group (Wang et. al., 2013) reported much shorter regenerated cilia. It might be worthwhile to compare the experimental variance as this is a key data point in both instances. The relationship between cilia regeneration and microtubule dynamic is not in one direction. On one side, there's a significant upregulation of tubulin after deciliation. While many microtubule depolymerization factors such as katanin, kinesin-13 positively regulate cilia assembly (though not without exceptions). It is hard to determine that the BCI induced cilia regeneration defect can't be rescued by other forms of microtubule stabilization. Microtubule reorganization is one of the most striking defects related to BCI treatment. I suggest changing the oversimplified claim to a more limited one (such as "PTX stabilized microtubule ...") and an expansion on the discussion about microtubule dynamics and cilia length regulation beyond the use of taxol. Meanwhile, I strongly encourage authors to continue to investigate this aspect and its connection to the cilia regeneration.

We will remove data regarding “partially” formed cytoplasmic microtubules and only include fully formed for each of these experiments for clarity.

It is important to note the different taxol concentration used here. While Wang et al., 2013 used 40 µM taxol to study ciliary affects, we use 15 µM where stabilization still occurs. There have been reports of varied cell responses to higher vs. lower doses of taxol (see Ikui et al., 2005, Pushkarev 2009, Yeung 1999) mostly with regards to the cell’s mitotic/apoptotic response. We could be seeing altered responses at this lower concentration because Chlamydomonas cells also behave differently in higher vs. lower taxol concentrations. Thank you for your suggestions. We have adjusted the text to be more specific to PTX treatment as opposed to general stabilization.

Major comment 7:____

There are several places where the technical detail or presentation of the data are missing or clearly erroneous.

Fig 1B: pMAPK and MAPK antibodies used in the WB are not described in the Material and methods. It's not clear if the same #9101, CST antibody used for RPE1 cell in Fig 1J is used.

We have updated the materials and methods to include that this antibody was used for both RPE1 and Chlamydomonas cells.

---

line 260 and Fig 3A state 20 µM BCI was used while Fig 3 legend repeatedly states 30 µM until (J). Also 30 µM in SF 2A.

We have corrected the text to 20 µM BCI in the mentioned places.

Fig 6C, the two lines under p value on top mostly likely start from the second column (B) instead of the first (D). Fig 6G, the line is perhaps intended for the second and fourth columns?

We will make these comparisons more clear. We had performed a chi-square analysis and were comparing the difference between DMSO and BCI before PTX stabilization or MG132 treatment to after. We will add brackets to more clearly show these comparisons.

Fig 6C, legends indicate bars representing each category. But only one bar is shown for each column. Same for 6G?

This is the same as the previous comment for the way we represented the statistics. We will make this clearer with brackets to show the comparisons.

Minor comments:____

1. A number of small errors in text were noted above. Done.

"orthologs" is misused in place of "ortholog mutants": line 176, 352, 421 (first), 879, 882, 898, 902, 938 , 939.

Done.

Capital names is misused as mutant names (e.g. "MKP2"should be "mkp2"): line 178, SF 1C, 1D and 1E, SF 3C, SF 6A

Done.

At several places such statistical analysis lines indicated are chosen confusingly. A simplest example is in Fig 1D, the comparison between 0 to 45 is less important than 0 to 30. Same as in Fig 1H, 1I. The line ends are inconsistent as well. They either end in the middle or the edge of the columns/data points (such as in SF 4B) and some with vertical lines (SF 2B, SF 4A, SF 6B). I suggest adding vertical lines pointing to the middle to indicate the compared datasets clearly.

Thank you for this suggestion. We agree and will update the figures to reflect this and provide clarity for statistical comparisons.

line 101 remove "the"

Done.

line 120 "modulate" to "alter"

Done.

line 198 "N=30" should be "N=3"

Done.

line 212. The legend for p value is likely for (G)

Done.

line 284, "singly" should be "single"

Done.

The dataset for "Pre" and "0m" in Fig 6D and 6E are clearly the same. Consider combining the two as in Fig 6C.

This is correct. We will combine the data sets.

Fig 6E, "BCI" on the X-axis should be "DMSO".

This is correct. We will correct this.

line 685, remove "?".

Done.

line 894: "Fig 3J" instead of "Fig 3H"

Done.

SF 1 legend, (C) and (D) are inverted.

Done.

SF 4A "Recovered" should be "Full"

Done.

SF 5, row 5, under second arrow perhaps missing +PTX

Done. We greatly appreciate this close reading of the text and the list of changes making these errors easy to find. We will make these changes in the manuscript.

Reviewer #1 (Significance (Required)):____

---

Increasing evidence indicates that several MAPKs activated by phosphorylation negatively control cilia length while few studies focus on how MAPK dephosphorylation affects cilia length regulation, largely due to the unknown identity of the phosphatase(s) specifically involved in cilia length regulation. The authors set out to investigate the effect of BCI on cilia length control. BCI specifically inhibits DUSP1 and DUSP6, both of which are known MAPK phosphatase, and therefore may provide a unique opportunity to understand how MAPK pathway is controlled by specific phosphatase(s) activity in cilia length regulation.

---

Overlooking some inconclusive results and oversimplified interpretations, I find the most striking findings are the BCI's effects including ciliogenesis, kinesin-2 ciliary dynamics and microtubule reorganization. I believe these findings have significant relevance to the stated goal (line 131) and conclusions (line 57) and readers may find them a good starting point for further investigation of the role phosphatases play in cilia length regulation.

Cilia length regulation is a complicated mechanism that is affected by many aspects of the cell and functions differently in various systems. My field of expertise may be summarized by cilia biology, cilia length regulation, IFT, kinesin, kinases (MAPKs), microtubules. The membrane trafficking's role in cilia length regulation is somewhat unfamiliar to me. Additionally, the authors used a number of statistical tests and corrections in various assays. The nuance of these choices is not clear to me and neither explained to general readers.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

In their manuscript, "ERK pathway activation inhibits ciliogenesis and causes defects in motor behavior, ciliary gating, and cytoskeletal rearrangement," Dougherty et al investigate how BCI, an activator of MAPK signaling, regulates ciliary length. Despite advances in our understanding of the structure and function of cilia, a fundamental question remains as to what are the mechanisms that control ciliary length. This is a critical question because cilia undergo dynamic changes in structure during the cell cycle where they must disassemble as they enter the cell cycle and must rebuild after cell division. This work contributes to a growing body of work to determine mechanisms that regulate cilia length.

The authors use a well-established model system, Chlamydomonas, to study cilia dynamics. This work expands on previous findings from these authors that inhibition of MAPK signaling using U0126 lengthens cilia as well as other publications that implicate MAPK signaling in controlling ciliary length. However, the authors only observe a few significant phenotypes with other subtle trends, leaving the conclusion regarding the role of MAPK signaling murky. Furthermore, it is unclear through what mechanism BCI impacts ciliary length. Several issues must be addressed:

MAJOR ISSUES

1. The basis for this study is the use of the ERK activator BCI, which the authors show activates MAPK signaling. While the authors do use putative DUSP6 ortholog mutants to corroborate some of the phenotypes, the majority of the data (and conclusions) uses BCI. However, there may be off target effects and the authors do not address this limitation of the study. The authors only use 1 pharmacological tool to manipulate MAPK signaling, so it is unclear whether these ciliary disruptions are specifically due to increased MAPK. It is necessary to clarify the following questions about BCI action to interpret the results:
2. ____a.____ What are off target effects of BCI? Does BCI impact proliferation? Why is the BCI phenotype of cilia shortening transient and dose dependent? Why does the phenotype of cilia length and regeneration capacity in Chlamydomonas differ from both ortholog mutants and hTERT-RPE1 cells? While we do mention following supplemental figure 1 that other MKPs could be the target for BCI, we also cite Molina et al., 2009 who showed specificity for BCI hydrochloride in zebrafish. BCI targets primarily DUSP6, but also exhibited some activity towards DUSP1. In this study, the authors had also used zebrafish embryos to check expression of 2 other FGF inhibitors, spry 4 and XFD, in the presence of BCI but found that their effects were not reversed. In addition, they checked the ability for BCI to suppress activity of other phosphatases including Cdc25B, PTP1B, or DUSP3/VHR and found that BCI could not suppress these phosphatases. BCI inhibition has previously been found to be more specific to MAPK phosphatases. In addition, we have previously confirmed that U0126 has a slight lengthening effect on Chlamydomonas which further implicates this pathway in cilium length tuning (Avasthi et al. 2012).

While cell proliferation assays maybe provide more support for MAPK signaling, it does not clarify lack of off target effects that could also contribute to this same phenotype. We do provide a cell proliferation assay for RPE1 cells where we show that higher concentrations of BCI result in cellular senescence as well (Fig 1I).

The BCI phenotype of cilia shortening is likely transient and dose dependent due to its effect on ciliary protein synthesis demonstrated in Figure 3J. The increase in drug likely increases its substrate binding to exert its effects on the cell faster, even if this includes off target proteins.

In RPE1 cells, we are likely seeing differences in regeneration capacity potentially due to their different mechanisms of ciliogenesis (RPE1 cells partake in intracellular ciliogenesis where axonemal assembly begins in the cytosol whereas Chlamydomonas cells partake in extracellular ciliogenesis where axonemal assembly begins after basal bodies dock to the apical membrane), or it could be that we’re missing a delay in regeneration in RPE1 cells after waiting 48 hours for ciliogenesis. We do not check this process sooner. There may be a defect that cells overcome. Additionally, among ortholog mutants and RPE1 compared to BCI-treated wild-type Chlamydomonas, there indeed could be off target effects or the drug could be targeting all of these MKPs rather than just one. We will add this to the discussion for clarity.

Reviewer #2 (Significance (Required)):

---

see above

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

SUMMARY:

In this study, the authors used a pharmacological approach to explore the function of ERK pathway in ciliogenesis. It has been reported that the alteration of FGF signaling causes abnormal ciliogenesis in several animal models including Xenopus, zebrafish, and mice. However, it remains elusive the molecular detail of how ERK pathway is associated with cilia assembling process. The authors found that the ERK1/2 activator/DUSP6 inhibitor, BCI inhibits ciliogenesis, highlighting the importance of ERK during ciliogenesis. Overall, this paper is well written, data are solid and convincing. This paper will be of great interest to many researchers who are interested in understanding ciliogenesis. The following comment is not mandatory requests but suggestions to improve the paper's significance and impact.

MAJOR COMMENTS:

- Combination of chemical blocker experiments were well controlled and data are solid. The authors are aware of the side effects of BCI, thus they carefully characterized the phenotypes of Mkp2/3/5 in Chlamydomonas. This reviewer wonders if the levels of ERK1/2 phosphorylation are activated in these mutants. Did the authors examine the levels of ERK1/2 phosphorylation in these mutants?

While we do not include the data showing ERK activation in these mutants, we have checked pMAPK activation and found that it is not significantly upregulated in these mutants. This could likely be due to compensatory pathways preventing persistent pMAPK activation. For example, constant ERK activation can lead to negative feedback to regulate this signal for cell cycle progression (Fritsche-Guenther et al., 2011). The ERK pathway has not been fully elucidated in Chlamydomonas, but it is possible that these similar mechanisms are in place for MAPKs. We will include this data in the supplement.

Reviewer #3 (Significance (Required)):

---

Accumulated studies suggest that the FGF signaling pathway plays a pivotal role in ciliogenesis. Disruption of either FGF ligands or its FGF receptor results in defective ciliogenesis in Xenopus and zebrafish. On the other hand, FGF signaling negatively controls the length of cilia in chondrocytes that would cause skeletal dysplasias seen in achondroplasia. Therefore, there is strong evidence suggesting that FGF signaling participates in ciliogenesis in cell-type and tissue-context dependent manners. However, the detailed mechanism of the downstream of FGF signaling in ciliogenesis is still unclear. In this regard, this paper is beneficial for the cilia community to expand the knowledge of how ERK1/2 kinase contributes to the regulation of ciliogenesis.

---

This reviewer therefore suggests that the authors may want to add more discussion to explain how their finding possibly moves the field forward to understand the pathogenesis of multiple ciliopathies.

We will add a description of this to the discussion.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

Reviewer 1:

---

Major comment 4____

A single panel in Fig 4A also can't support the shift in protein density in the TZ in line 317. As line 324 implies protein synthesis defect by BCI, the very minor (in amount and significance) reduction of the NPHP4 fluorescence should not be interpreted as any disruption at all to the transition zone. I suggest checking other TZ proteins such as CEP290 etc or leave this section out.

Also, The additive effect from BFA and BCI treatment in Fig 5A suggests BCI affects cilia length independent of Golgi. The "actin puncta" and arpc4 mutant are not sufficiently introduced. And more importantly, how increase in the actin puncta explains the shorter cilia length caused by BCI while actin puncta are absent in arpc4 mutant with shorter cilia? Also, the Arl6 fluorescence signal "increase" is not significant in either time point. I suggest leaving this section out as well.

We agree that one EM image cannot support a protein shift and have removed our observation in the text. However, we do see a statistically significant decrease in NPHP4 fluorescence in BCI treated cells which we consider a disruption in the sense that the structural composition is altered. We will change the word “disruption” to “alteration” for clarity. Though this is a minor defect, we believe it is still worth noting. We believe this data still adds to the model that though the EM-visible structure is unaltered, finer details within the transition zone are indeed altered and we cannot rule out that these smaller changes are not impacting protein entry into cilia. Awata et al. 2014 shows that NPHP4 is important for controlling trafficking of ciliary proteins at the transition zone, and its loss from the transition zone has been found to have effects in ciliary protein composition. Because we see decreased NPHP4 expression, we believe this is a notable finding as we see effects on the abundance of a protein which is known to affect ciliary protein composition and have therefore chosen to leave the data in the manuscript. We will adjust the language to most accurately describe our findings.

We also agree with the interpretation that the additive effect seen from BFA and BCI treatment could suggest independent pathway collapse separate from the Golgi which we have mentioned in the manuscript.

We have provided more information to introduce actin puncta and ARPC4 with regards to membrane trafficking. Bigge et al. 2020 shows that ARPC4, a subunit of the ARP2/3 complex which is an actin binding protein important for nucleating actin branches, has a role in ciliary assembly. ARPC4 mutants have repressed ability to regenerate their cilia. One feature they noticed in regenerating cells is the immediate formation of actin puncta which are reminiscent of yeast endocytic pits. This observation in addition to altered membrane uptake pathways in Chlamydomonas suggests that ciliogenesis involves reclaiming plasma membrane for use in ciliogenesis (because of the diffusion barrier preventing a contiguous membrane). Here, we incorporate this assay to assess the ability for the cell to reclaim membrane during BCI treatment and find that there is increased actin puncta. This could indicate that there is increased number of endocytic pits or alternatively that the lifetime of these pits is increased (perhaps due to incomplete endocytosis) such that we are able to detect more of them at a fixed point in time. While we cannot say which is happening here, we have previously found that these actin puncta are likely endocytic and needed to reclaim membrane for early ciliogenesis. An increase in these puncta may suggest dysregulated endocytosis in one way or another. ARPC4 cells cannot form the actin puncta in the first place, whereas we are seeing defects following puncta formation. We have taken out the Arl6 data.

Major comment 6____

Throughout this manuscript, the standard the authors used to interpret statistical significance is erratic. In a few instances, the threshold for p value is clearly indicated such as in Fig 1 legend. Though other times, much higher p values are considered differences. Here are some examples:

SF 1C, p=0.1167 is considered "(mkp5) shorter than wildtype ciliary lengths" (also line 177 "SF 1C" instead of "SF 1D")

Fig 3C, p=0.083 interpreted as "slightly less" in line 262 and possibly as "(KAP-GFP) not being able to enter (cilia)" in line 268

Fig 3G, p=0.1087 is considered "not decrease after two hours" line 267

SF 3C, p=0.2929 for mkp2 mutant (misuse of "orthologs" in line 352) is considered "fewer actin puncta compared to wild type cells" (line 352).

SF 6B, p=0.1565for mkp3 mutant (line 421: misuse of "orthologs" and correct use of "ortholog mutants") is considered not be able to "fully reorganize their microtubules" (line 421).

These instances sometimes serve as basis for major conclusions and should be clarified or more carefully characterized.

We agree the interpretations are very erratic in places and greatly appreciate this detailed list making it easy to find and correct these interpretations. We have adjusted the text in the mentioned places to reflect these changes, and we have made a statement in the text and under statistical methods that say we consider p Reviewer 2:

In multiple instances the conclusions are overstated, and the author must clarify the interpretation of the results to reflect the data presented. Here are some examples:

• ____a.____ The conclusion that protein synthesis is disrupted is incorrect in two instances (line 258 and 275) as the experiments in figure 3 do not directly examine changes in synthesis (they look at cilia regeneration as a proxy). We show that KAP-GFP expression is not normal during regeneration at 120 minutes which suggests, in addition to the inability for cilia to grow in BCI, that synthesis is inhibited because this protein is not replaced. In addition, blocking the proteosome did not rescue this decrease in KAP-GFP expression indicating that this is not a matter of KAP-GFP protein being degraded rapidly. We use regeneration and KAP-GFP readout as a proxy for protein synthesis. We have clarified this in the text.

• ____b.____ The conclusion that BCI disrupts membrane trafficking is too broad when the authors only examined trafficking of one membrane protein, Arl6. While we only looked at one membrane protein specifically, we assess other membrane trafficking paths. We looked at BCI vs. BFA to assess Golgi trafficking (Dentler 2010) in addition to formation of actin puncta which is used in Bigge et al. 2020 as an assay for membrane uptake from the plasma membrane for incorporation into cilia.

• ____c.____ The conclusion that the transition zone is disrupted is too broad based on a decrease in the expression of one transition zone protein, NPHP4. We have changed the text to be more specific to NPHP4.

Highlighting the overstatement, the conclusion of the header and figure caption on page 10 contradict one another. The manuscript states that "BCI partially disrupts the transition zone" (line 313) and that "The TZ structure is structurally unaltered with BCI treatment" (line 329).

In the manuscript, we show that the EM-visible structure is indeed unaltered. Because we see a decrease in NPHP4 fluorescence, we concluded that while the EM-visible structure is unaltered, protein composition within the transition zone is altered which suggests that BCI partially disrupts the transition zone.

Why is kinesin-2 the only target studied for ciliogenesis? Ciliogenesis is a complex process that involves many other critical proteins and investigating kinesin-2 alone is not sufficient to conclude why BCI prevents cilia assembly.

We use kinesin-2 because it is the only ciliary anterograde motor in Chlamydomonas which is required for proper ciliogenesis. By assessing kinesin-2, we were able to address whether this protein alone was the cause for inhibited ciliary assembly (and we find that it’s not), whether its ability to enter was impacted (likely owing to defects in other protein entry), and we were able to use this protein to understand how its protein expression was affected. Because KAP-GFP is a cargo adaptor protein and interacts with IFT complexes and other cargoes, defects in this protein can have a wide range of implications. We agree and the data agree that kinesin-2 alone is not sufficient to conclude why BCI prevents cilia assembly. Because of this, we assessed other pathways including membrane trafficking and microtubule stabilization to better understand why we see defects in ciliary assembly. Certainly many other proteins are important in ciliogenesis and we hope that this study sparks further work in this area to identify additional causative explanations for impaired ciliogenesis upon MAPK activation..

Tagged ciliary proteins are sensitive to disruptions in function and expression within cilia. It is important to include proper controls in the study using KAP-GFP Chlamydomonas cells to ensure that KAP-GFP maintains endogenous expression levels and normal function as untagged KAP. Furthermore, if this information is available through the resource where the cells were purchased, then this needs to be discussed.

KAP-GFP expressing Chlamydomonas has previously been validated as described in Mueller et al., 2005. We will provide details in the text about validation of this strain.

The authors need to provide clear explanations to a general audience of why this technique is used and how the authors reached the interpretations. There are several instances where the authors use techniques that are cited as fundamental papers in Chlamydomonas. Here are two examples:

• ____a.____ It is unclear how the authors concluded that decreased frequency and velocity of train size shows that kinesin entry, specifically, is disrupted. We have expanded on this in the text. Please see response to reviewer 1, Major comment 2 above.

• ____b.____ It was impossible to follow how the experiment where cells treated with cycloheximide could not regenerate their cilia following BCI treatment shows that BCI inhibits protein synthesis. We have adapted the text to be more clear regarding this experiment. In this experiment, we deplete the ciliary protein pool by forcing ciliary shedding two times. Following the first shedding, there is enough protein to assemble cilia to half length (Rosenbaum, 1969). We ensure that the protein pool is completely used up by inhibiting further ciliary protein synthesis with cycloheximide. For the second shedding event, completely new ciliary protein must be synthesized for ciliogenesis to occur which is why ciliogenesis takes much longer compared to a single regeneration where half of the ciliary protein pool still remains and can be immediately incorporated into cilia (SF 2C). In the presence of BCI, cilia cannot grow at all as expected; but 4 hours after BCI is washed out, we see ciliogenesis just beginning to occur which indicates that there is protein present for ciliogenesis to begin whereas in cells where BCI is not washed out, we do not see any ciliogenesis.

The impact of BCI treatment on membrane trafficking as presented is confusing. BCI exacerbated the effects of BFA treatment on Golgi, yet the authors do not address that this could be an indirect effect of BCI or an off-target effect of BCI.

This is addressed in the discussion (paragraph 4).

The discussion section includes many interpretations of the results, but leaves the reader confused as to what the authors think might be happening. The manuscript would be far clearer if the authors would provide a working model for why BCI impacts cilia length. It is fine for this to be left for future work but, as the experts, the authors must have relevant thoughts to share with the field.

Figure 7 provides a model with as much as we can conclude given the data; what we show is that BCI inhibits many different processes in the cell, but we do not necessarily show links between these processes to provide a complete working model of how these are all interconnected; we have provided a summary model that depicts the various, still disconnected processes that are inhibited by BCI. MAP kinases such as ERK have dozens of downstream targets both within and outside the nucleus. Ciliogenesis also is a complex process coordinating many cellular mechanisms. The intersection of these two seem to have a multi-fold effect that results in a dramatic ciliary phenotype through a combination of factors, however not one that fully explains the severity upon initial deciliation in BCI/MAPK activation. Further work is needed to identify the precise cause of completely inhibited cilium growth from zero length.

MINOR ISSUES

1. The title of the manuscript is inaccurate and overstates the pathway involvement in cilia. The authors do not directly show that ERK pathway activation causes the ciliary phenotypes due to the use of BCI, a drug that modulates ERK. We have adjusted the title to “The ERK activator, BCI, causes…”

When discussing results of data that are not statistically significant it creates confusion to state that the results "increased/decreased slightly".

We agree that references to statistics are inconsistent or confusing throughout the text and have adjusted these references accordingly.

Reviewer 3:

Major comment:

- If the authors want to emphasize their finding is associated with MAP kinases, it would be also beneficial to examine other major MAP kinase pathways such as P38/JNK. If not, then this reviewer suggests revising the text as ERK through this manuscript to avoid confusions.

Because the ERK pathway has not been fully elucidated in Chlamydomonas, we have refrained from using “ERK” as a descriptor because this particular MAPK shares equal identity with multiple MAPKs in Chlamydomonas. Further, BCI may be targeting more than one MAPK phosphatase resulting in the myriad phenotypes we have discovered. At this time, we lack a level of gene-level resolution to map to known MAPK pathways.

• *

4. Description of analyses that authors prefer not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

---

Reviewer 1:

Major comment 2____

The claim that "BCI treatment decreases kinesin-2 entry into cilia" (line 236) is a misinterpretation of the data presented. The data indicates KAP-GFP have reduced accumulation in cilia, decreased IFT (anterograde) frequency, velocity and injection size associated with BCI treatment. Though as shown in Fig 1D and Fig 2C, cilia length is also shorter due to BCI treatment. Ludington et. al, 2013 showed a negative correlation of cilia length and KAP injection rate in various treatments that affect cilia length. It's essential to rule out that the KAP dynamics reported in the current manuscript is not an outcome of shortened cilia in order to claim as line 236 seems to suggest. One way to demonstrate specific effect by BCI would be to compare KAP dynamic in cilia with equal or similar length, either by only selecting the shorter cilia from wt or use other treatments that are known to decrease cilia length (chemicals, cell cycle, mutants etc.). Given the capability and resource represented in this manuscript, I don't expect a significant cost and time investment for these experiments.

Ludington et al., 2013 shows that injection size decreases with increasing length. Our data show that the shorter length cilia have decreased injection size and rate inconsistent with the cause being due to shortened length alone. In other words, in figure 2C and 2G, we see decreased KAP-GFP fluorescence in shorter cilia as opposed to greater fluorescent signal in shorter cilia seen in Ludington et al., 2013. This data, in combination with the decreasing frequency of KAP-GFP entry overtime in figure 2E and decreased velocity in figure 2F support decreased kinesin-2 entry into cilia. If entry was unaltered, we would expect increased KAP-GFP fluorescence in the cilia over time in BCI-treated cells.

---

Reviewer 2:

The authors state that the decreased length of cilia following BCI treatment could be a result of reduced assembly or increased assembly. Disruptions to cilia assembly and disassembly are not mutually exclusive and both must be evaluated. The authors do not test whether cilia disassembly is disrupted in BCI treatment and therefore, cannot conclude that BCI solely disrupts cilia assembly.

While effects on disassembly remains a possibility, the striking inability to increase from zero length upon deciliation and the effects on anterograde IFT through the TIRFM assays suggest an affect on assembly. There may be effects on disassembly and likely many other cilia related processes not investigated but we feel it remains accurate to conclude that assembly is affected by BCI treatment.

Reviewer 3:

- If time allows, in addition to examining NPHP4, it would be beneficial to examine other TZ/TF markers such as CEP164 to confirm if BCI partially disrupts the TZ.

Given the known outcomes of NPHP4 loss in Chlamydomonas (Awata et al., …) in affecting ciliary protein composition, we suspect the changes in NPHP4 abundance at the transition zone will have a significant impact and agree it would be interesting in a follow up study to see how other transition zone proteins (particularly ones known to interact with NPHP4 or others critical for TZ function) are impacted following BCI treatment.

---

MINOR COMMENTS:

- I suggest moving supplemental figure 1 to the main figure (Fig. 1?) so that the readers appreciate the author's careful examination of BCI through this manuscript.

Thank you for your suggestion and kind critique. We have included this data in the supplement for consistency with mutant data in all of the other supplemental figures.

---

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

In this study, the authors used a pharmacological approach to explore the function of ERK pathway in ciliogenesis. It has been reported that the alteration of FGF signaling causes abnormal ciliogenesis in several animal models including Xenopus, zebrafish, and mice. However, it remains elusive the molecular detail of how ERK pathway is associated with cilia assembling process. The authors found that the ERK1/2 activator/DUSP6 inhibitor, BCI inhibits ciliogenesis, highlighting the importance of ERK during ciliogenesis. Overall, this paper is well written, data are solid and convincing. This paper will be of great interest to many researchers who are interested in understanding ciliogenesis. The following comment is not mandatory requests but suggestions to improve the paper's significance and impact.

Major comments:

• Combination of chemical blocker experiments were well controlled and data are solid. The authors are aware of the side effects of BCI, thus they carefully characterized the phenotypes of Mkp2/3/5 in Chlamydomonas. This reviewer wonders if the levels of ERK1/2 phosphorylation are activated in these mutants. Did the authors examine the levels of ERK1/2 phosphorylation in these mutants?

• If the authors want to emphasize their finding is associated with MAP kinases, it would be also beneficial to examine other major MAP kinase pathways such as P38/JNK. If not, then this reviewer suggests revising the text as ERK through this manuscript to avoid confusions.

• If time allows, in addition to examining NPHP4, it would be beneficial to examine other TZ/TF markers such as CEP164 to confirm if BCI partially disrupts the TZ.

Minor comments:

• I suggest moving supplemental figure 1 to the main figure (Fig. 1?) so that the readers appreciate the author's careful examination of BCI through this manuscript.

Significance

Accumulated studies suggest that the FGF signaling pathway plays a pivotal role in ciliogenesis. Disruption of either FGF ligands or its FGF receptor results in defective ciliogenesis in Xenopus and zebrafish. On the other hand, FGF signaling negatively controls the length of cilia in chondrocytes that would cause skeletal dysplasias seen in achondroplasia. Therefore, there is strong evidence suggesting that FGF signaling participates in ciliogenesis in cell-type and tissue-context dependent manners. However, the detailed mechanism of the downstream of FGF signaling in ciliogenesis is still unclear. In this regard, this paper is beneficial for the cilia community to expand the knowledge of how ERK1/2 kinase contributes to the regulation of ciliongenesis.

This reviewer therefore suggests that the authors may want to add more discussion to explain how their finding possibly moves the field forward to understand the pathogenesis of multiple ciliopathies.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In their manuscript, "ERK pathway activation inhibits ciliogenesis and causes defects in motor behavior, ciliary gating, and cytoskeletal rearrangement," Dougherty et al investigate how BCI, an activator of MAPK signaling, regulates ciliary length. Despite advances in our understanding of the structure and function of cilia, a fundamental question remains as to what are the mechanisms that control ciliary length. This is a critical question because cilia undergo dynamic changes in structure during the cell cycle where they must disassemble as they enter the cell cycle and must rebuild after cell division. This work contributes to a growing body of work to determine mechanisms that regulate cilia length.

The authors use a well-established model system, Chlamydomonas, to study cilia dynamics. This work expands on previous findings from these authors that inhibition of MAPK signaling using U0126 lengthens cilia as well as other publications that implicate MAPK signaling in controlling ciliary length. However, the authors only observe a few significant phenotypes with other subtle trends, leaving the conclusion regarding the role of MAPK signaling murky. Furthermore, it is unclear through what mechanism BCI impacts ciliary length. Several issues must be addressed:

MAJOR ISSUES

1. The basis for this study is the use of the ERK activator BCI, which the authors show activates MAPK signaling. While the authors do use putative DUSP6 ortholog mutants to corroborate some of the phenotypes, the majority of the data (and conclusions) uses BCI. However, there may be off target effects and the authors do not address this limitation of the study. The authors only use 1 pharmacological tool to manipulate MAPK signaling, so it is unclear whether these ciliary disruptions are specifically due to increased MAPK. It is necessary to clarify the following questions about BCI action to interpret the results:

a) What are off target effects of BCI? Does BCI impact proliferation? Why is the BCI phenotype of cilia shortening transient and dose dependent? Why does the phenotype of cilia length and regeneration capacity in Chlamydomonas differ from both ortholog mutants and hTERT-RPE1 cells?

1. In multiple instances the conclusions are overstated, and the author must clarify the interpretation of the results to reflect the data presented. Here are some examples:

a) The conclusion that protein synthesis is disrupted is incorrect in two instances (line 258 and 275) as the experiments in figure 3 do not directly examine changes in synthesis (they look at cilia regeneration as a proxy).

b) The conclusion that BCI disrupts membrane trafficking is too broad when the authors only examined trafficking of one membrane protein, Arl6.

c) The conclusion that the transition zone is disrupted is too broad based on a decrease in the expression of one transition zone protein, NPHP4.

1. Highlighting the overstatement, the conclusion of the header and figure caption on page 10 contradict one another. The manuscript states that "BCI partially disrupts the transition zone" (line 313) and that "The TZ structure is structurally unaltered with BCI treatment" (line 329).

2. The authors state that the decreased length of cilia following BCI treatment could be a result of reduced assembly or increased assembly. Disruptions to cilia assembly and disassembly are not mutually exclusive and both must be evaluated. The authors do not test whether cilia disassembly is disrupted in BCI treatment and therefore, cannot conclude that BCI solely disrupts cilia assembly.

3. Why is kinesin-2 the only target studied for ciliogenesis? Ciliogenesis is a complex process that involves many other critical proteins and investigating kinesin-2 alone is not sufficient to conclude why BCI prevents cilia assembly.

4. Tagged ciliary proteins are sensitive to disruptions in function and expression within cilia. It is important to include proper controls in the study using KAP-GFP Chlamydomonas cells to ensure that KAP-GFP maintains endogenous expression levels and normal function as untagged KAP. Furthermore, if this information is available through the resource where the cells were purchased, then this needs to be discussed.

5. The authors need to provide clear explanations to a general audience of why this technique is used and how the authors reached the interpretations. There are several instances where the authors use techniques that are cited as fundamental papers in Chlamydomonas. Here are two examples:

a) It is unclear how the authors concluded that decreased frequency and velocity of train size shows that kinesin entry, specifically, is disrupted.

b) It was impossible to follow how the experiment where cells treated with cycloheximide could not regenerate their cilia following BCI treatment shows that BCI inhibits protein synthesis.

1. The impact of BCI treatment on membrane trafficking as presented is confusing. BCI exacerbated the effects of BFA treatment on Golgi, yet the authors do not address that this could be an indirect effect of BCI or an off-target effect of BCI.

2. The discussion section includes many interpretations of the results, but leaves the reader confused as to what the authors think might be happening. The manuscript would be far clearer if the authors would provide a working model for why BCI impacts cilia length. It is fine for this to be left for future work but, as the experts, the authors must have relevant thoughts to share with the field.

MINOR ISSUES

1. The title of the manuscript is inaccurate and overstates the pathway involvement in cilia. The authors do not directly show that ERK pathway activation causes the ciliary phenotypes due to the use of BCI, a drug that modulates ERK.

2. When discussing results of data that are not statistically significant it creates confusion to state that the results "increased/decreased slightly".

Significance

see above

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

The authors investigated the effects of an allosteric inhibitor of DUSP (BCI) on cilia length regulation in Chlamydomonas. Among seven conclusions summarized in Fig. 7, BCI is found to severely disrupt cilia regeneration and microtubule reorganization. Additionally, changes in kinesin-II dynamic, ciliary protein synthesis, transition zone composition and membrane trafficking are also explored. All these aspects have been shown to affect cilia length regulation. Findings from this body of work may give insights on how MAPK, a major player in cilia length regulation, functions in various avenues. Additionally, the study of BCI and other specific phosphatase inhibitors may provide a unique addition to the toolset available to uncover this important and complicated mechanism.

Major comments:

Major comment 1

The addition of BCI increases phosphorylated MAPK in Chlamydomonas based on Fig 1B. However, the claim that BCI inhibits Chlamydomonas MKPs is not supported at all. SF1A shows CrMKP2, 3 and 5 are related to each other but distant from HsDUSP6 and DrDUSP6. At the same time, 2 out 3 predicted BCI interacting residues are different from the Hs and Dr DUSP6 in SF1B, contradicting "well conserved" in line 172. Consistently, mutants of these orthologs have little to no ciliary length and regeneration defects compared to BCI treatment (see major comment 6 about statistical significance). I am not convinced that BCI inhibits the identified orthologs or any MKPs in Chlamydomonas. It's possible that BCI inhibits a broad range of phosphatases including the ones listed and/or those for upstream kinases. But such a point is not demonstrated by the presented data.

Major comment 2

The claim that "BCI treatment decreases kinesin-2 entry into cilia" (line 236) is a misinterpretation of the data presented. The data indicates KAP-GFP have reduced accumulation in cilia, decreased IFT (anterograde) frequency, velocity and injection size associated with BCI treatment. Though as shown in Fig 1D and Fig 2C, cilia length is also shorter due to BCI treatment. Ludington et. al, 2013 showed a negative correlation of cilia length and KAP injection rate in various treatments that affect cilia length. It's essential to rule out that the KAP dynamics reported in the current manuscript is not an outcome of shortened cilia in order to claim as line 236 seems to suggest. One way to demonstrate specific effect by BCI would be to compare KAP dynamic in cilia with equal or similar length, either by only selecting the shorter cilia from wt or use other treatments that are known to decrease cilia length (chemicals, cell cycle, mutants etc.). Given the capability and resource represented in this manuscript, I don't expect a significant cost and time investment for these experiments.

Major comment 3

The claims that "BCI inhibits KAP-GFP protein expression" (line 271) and "BCI inhibits ciliary protein synthesis" (line 286) are not convincingly demonstrated. Overlooking that only KAP is investigated instead of kinesin-II, none of the relative intensity from the WB in 30 or 50 µM BCI and the basal body fluorescence intensity indicates a statistically significant difference. The washout made no difference in any of the assay and it's not explained how phosphatase inhibition by BCI might affect overall ciliary protein synthesis. The claims about protein expression may need a fair amount of effort and time investment to demonstrate, therefore I suggest leaving these out for this manuscript. Though it's very interesting to see that in SF 2C cilia in 20 µM BCI treatment can regeneration slowly. Line 162, the author claimed "In the presence of (30 µM) BCI, cilia could not regenerate at all (Fig 1E)". Since Fig 1E only extends to 2 hours, I think it's important to clarify if in 30 µM BCI cilia indeed can not generate even after 6 or 8 hours.

Major comment 4

A single panel in Fig 4A also can't support the shift in protein density in the TZ in line 317. As line 324 implies protein synthesis defect by BCI, the very minor (in amount and significance) reduction of the NPHP4 fluorescence should not be interpreted as any disruption at all to the transition zone. I suggest checking other TZ proteins such as CEP290 etc or leave this section out. Also, The additive effect from BFA and BCI treatment in Fig 5A suggests BCI affects cilia length independent of Golgi. The "actin puncta" and arpc4 mutant are not sufficiently introduced. And more importantly, how increase in the actin puncta explains the shorter cilia length caused by BCI while actin puncta are absent in arpc4 mutant with shorter cilia? Also, the Arl6 fluorescence signal "increase" is not significant in either time point. I suggest leaving this section out as well.

Major comment 5

It is very interesting that BCI disrupts microtubule reorganization induced by deciliation and colchicine. Data in Fig 6B and C are presented differently than those in SF 4C. For example, in SF 4C, BCI treatment for 60 min has close to 50 % cells with microtubule partially reorganized while in Fig 6C about 20% cells with microtubule fully (or combined?) reorganized. The nature of the difference is unclear to me without an assay comparing the two directly. Hence the implied claim that BCI affects colchicine induced microtubule reorganization differently than deciliation induced one is hard to interpret (line 398, line 388 vs line 403). The fact that taxol doesn't rescue cilia regeneration defect by BCI is very interesting. Here taxol treatment results in fully regenerated cilia while Junmin Pan's group (Wang et. al., 2013) reported much shorter regenerated cilia. It might be worthwhile to compare the experimental variance as this is a key data point in both instances. The relationship between cilia regeneration and microtubule dynamic is not in one direction. On one side, there's a significant upregulation of tubulin after deciliation. While many microtubule depolymerization factors such as katanin, kinesin-13 positively regulate cilia assembly (though not without exceptions). It is hard to determine that the BCI induced cilia regeneration defect can't be rescued by other forms of microtubule stabilization. Microtubule reorganization is one of the most striking defects related to BCI treatment. I suggest changing the oversimplified claim to a more limited one (such as "PTX stabilized microtubule ...") and an expansion on the discussion about microtubule dynamics and cilia length regulation beyond the use of taxol. Meanwhile, I strongly encourage authors to continue to investigate this aspect and its connection to the cilia regeneration.

Major comment 6

Throughout this manuscript, the standard the authors used to interpret statistical significance is erratic. In a few instances, the threshold for p value is clearly indicated such as in Fig 1 legend. Though other times, much higher p values are considered differences. Here are some examples: SF 1C, p=0.1167 is considered "(mkp5) shorter than wildtype ciliary lengths" (also line 177 "SF 1C" instead of "SF 1D") Fig 3C, p=0.083 interpreted as "slightly less" in line 262 and possibly as "(KAP-GFP) not being able to enter (cilia)" in line 268 Fig 3G, p=0.1087 is considered "not decrease after two hours" line 267 SF 3C, p=0.2929 for mkp2 mutant (misuse of "orthologs" in line 352) is considered "fewer actin puncta compared to wild type cells" (line 352). SF 6B, p=0.1565for mkp3 mutant (line 421: misuse of "orthologs" and correct use of "ortholog mutants") is considered not be able to "fully reorganize their microtubules" (line 421). These instances sometimes serve as basis for major conclusions and should be clarified or more carefully characterized.

Major comment 7

There are several places where the technical detail or presentation of the data are missing or clearly erroneous.

• Fig 1B: pMAPK and MAPK antibodies used in the WB are not described in the Material and methods. It's not clear if the same #9101, CST antibody used for RPE1 cell in Fig 1J is used.
• line 260 and Fig 3A state 20 µM BCI was used while Fig 3 legend repeatedly states 30 µM until (J). Also 30 µM in SF 2A.
• Fig 6C, the two lines under p value on top mostly likely start from the second column (B) instead of the first (D). Fig 6G, the line is perhaps intended for the second and fourth columns?
• Fig 6C, legends indicate bars representing each category. But only one bar is shown for each column. Same for 6G?

Minor comments:

1. A number of small errors in text were noted above.

2. "orthologs" is misused in place of "ortholog mutants": line 176, 352, 421 (first), 879, 882, 898, 902, 938 , 939.

3. Capital names is misused as mutant names (e.g. "MKP2"should be "mkp2"): line 178, SF 1C, 1D and 1E, SF 3C, SF 6A

4. At several places such statistical analysis lines indicated are chosen confusingly. A simplest example is in Fig 1D, the comparison between 0 to 45 is less important than 0 to 30. Same as in Fig 1H, 1I. The line ends are inconsistent as well. They either end in the middle or the edge of the columns/data points (such as in SF 4B) and some with vertical lines (SF 2B, SF 4A, SF 6B). I suggest adding vertical lines pointing to the middle to indicate the compared datasets clearly.

5. line 101 remove "the"

6. line 120 "modulate" to "alter"

7. line 198 "N=30" should be "N=3"

8. line 212. The legend for p value is likely for (G)

9. line 284, "singly" should be "single"

10. The dataset for "Pre" and "0m" in Fig 6D and 6E are clearly the same. Consider combining the two as in Fig 6C.

11. Fig 6E, "BCI" on the X-axis should be "DMSO".

12. line 685, remove "?".

13. line 894: "Fig 3J" instead of "Fig 3H"

14. SF 1 legend, (C) and (D) are inverted.

15. SF 4A "Recovered" should be "Full"

16. SF 5, row 5, under second arrow perhaps missing +PTX

Significance

Increasing evidence indicates that several MAPKs activated by phosphorylation negatively control cilia length while few studies focus on how MAPK dephosphorylation affects cilia length regulation, largely due to the unknown identity of the phosphatase(s) specifically involved in cilia length regulation. The authors set out to investigate the effect of BCI on cilia length control. BCI specifically inhibits DUSP1 and DUSP6, both of which are known MAPK phosphatase, and therefore may provide a unique opportunity to understand how MAPK pathway is controlled by specific phosphatase(s) activity in cilia length regulation.

Overlooking some inconclusive results and oversimplified interpretations, I find the most striking findings are the BCI's effects including ciliogenesis, kinesin-2 ciliary dynamics and microtubule reorganization. I believe these findings have significant relevance to the stated goal (line 131) and conclusions (line 57) and readers may find them a good starting point for further investigation of the role phosphatases play in cilia length regulation.

Cilia length regulation is a complicated mechanism that is affected by many aspects of the cell and functions differently in various systems. My field of expertise may be summarized by cilia biology, cilia length regulation, IFT, kinesin, kinases (MAPKs), microtubules. The membrane trafficking's role in cilia length regulation is somewhat unfamiliar to me. Additionally, the authors used a number of statistical tests and corrections in various assays. The nuance of these choices is not clear to me and neither explained to general readers.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

We would like to thank the editor for the opportunity to submit our revised manuscript “Neuron- derived Thioredoxin-80: a novel regulator of type-I interferon response in microglia”. We thank the reviewers for their thorough analysis and thoughtful insights, we have considered all thequestions and issues aroused and modified the manuscript where appropriate and all changes in the manuscript are highlighted in yellow. We hope that this new improved version will be suitable for publication in an affiliated journal of Review Commons. Please find below a point-to-point description of the changes and the experiments that we plan to carry out.

Reviewer #1:

Major Comments:

1.This work is potentially interesting, but the results are very preliminary. There is not a clear demonstration of the signaling pathways triggered by oxidative stress and leading to Trx80 production in neurons. The authors claim the role of Nrf2, but did not silence Nrf2, nor demonstrated the cascade downstream Nrf2 that is responsible for Trx80 production.

This is a very valuable point raised by the reviewer. To better characterize the role of Nrf2 and the downstream cascade responsible for Trx80 production, we are currently running the following experiments:

• We are silencing Nrf2 in neuronal primary cultures prior to 27-hydroxycholesterol (27-OHC) or Rotenone treatment. We will then measure Trx1 and Trx80 protein levels. We expect to see significant decrease in the protein levels of both Trx1 and Trx80 in control conditions, and a lack of effect of 27-OHC and rotenone in inducing an increase in their levels.

Additionally, to confirm in our model that, as previously reported, ADAM10/17 α-secretases are responsible for the cleavage of Trx1 into Trx80, neuronal primary cultures will be treated with GW280264X, an inhibitor of ADAM10 and ADAM17 prior to 27-OHC or rotenone treatment. We expect to observe a decrease in the amount of Trx80 produced, whereas Trx1 protein levels should still increase in presence of 27-OHC and rotenone. We believe that these experiments will help to confirm the pathway responsible for the increased production of Trx80 downstream Nrf2 activation by 27-OHC or rotenone.

Additionally, we will be more specific in the description of the oxidative-stress related signaling pathways that we describe from our RNAseq data, and determine whether know downstream targets of Nrf2 are indeed changing their expression levels upon 27OH treatment in neurons.

1. In addition, Cyp27Tg mice show higher Trx80 levels only at a very old age and it is not at all shown that oxidative stress is responsible for Trx80 enhanced production in this mice model.

We would like to point out that most of the studies regarding the oxidative effects caused by 27-OHC have been carried out in vitro, where it promotes the activation of cell survival pathways that appear to be modulated by Reactive Oxygen Species (ROS) (Vurusaner et al., 2018). Moreover, in vitro treatments with this oxysterol induce the expression of Nrf2 through extracellular signal-regulated kinase (ERK) and the phosphoinositide 3-kinase (PI3K)/Akt pathways (Vurusaner et al., 2016). Nrf2 is a transcription factors for many antioxidant proteins including heme oxygenase-1 (HO-1) that has also been found to be elevated upon 27-OHC treatment (Dasari et al., 2010). Despite this evidence in vitro, no study so far has evaluated 27-OHC-mediated oxidative stress in vivo.

• To further clarify the pathways responsible for Trx80 production and its effects in Cyp27Tg in vivo we will perform fluorescence-activated-nuclei sorting (FANS) of neurons (Neun+), microglia (neun-, pu1+) and astrocytes (eaat1+, neun-) from 22 month old Cyp27 tg mouse cortex, followed by RNAseq analysis.

  1. The authors claim a role of Trx80 in promoting IRM phenotype in microglia. However, there is not any data showing its relevance in Alzheimer`s (AD progression).

The role of IRMs in the brain is not yet completely understood. However, it has been reported that DNA damage (Hartlova and colleagues 2015) as well as amyloid plaques containing nucleic acids (Roy et al 2020) induce type-I interferon response in microglia. Dorman and colleagues have recently shown that type-I interferon responses in microglia can rapidly induce phagocytosis of damaged neurons (Dorman et al 2022). An increased phagocytic activity by microglia would also explain the decrease in amyloid-beta (Ab) previously reported in a Drosophila model overexpressing both human Trx80 and Ab42 (Gerenu et al., 2019).

There are studies showing that type-I interferons and IRMs are present in human brain and actively play a role in aging and Alzheimer’s Disease (AD) (Roy et al 2020)(Olah et al., 2020). One potential model to explain the role of IRM and their relevance for AD is that exposure to damage associated molecular patterns (DAMPs) or secreted Trx80 from stressed neurons promote a type I-interferon response in microglia that subsequently triggers an autocrine loop that enhances phagocytic efficiency. Under physiological conditions, this mechanism might play an important role at dealing with bacterial and viral infections in the brain as well as removing debris and damaged and apoptotic neurons to keep a healthy brain homeostasis. However, these responses can become pathological if sustained high IFN-I levels trigger a exacerbated microglial response that leads to widespread cell death and neuroinflammation.

Trx80 has been previously reported to be depleted in AD brains (Gil-Bea et al., 2012) and to decrease in APPNL-G-F mice, a mouse model of amyloid pathology as amyloid accumulation worsens. This pathology is characterized by a generalized loss of neurons, which as we show in our study, are the main producers of Trx80. Moreover, an increasing accumulation of amyloid pathology might as well explain the decrease in Trx80 and its effects on microglia. Evidence supporting this possibility come from studies showing that the presence of amyloid-plaques promote the generation of disease-associated microglia, which are transcriptionally different from IRMs (Sala-Frigerio et al., 2019)(Keren-Shaul et al., 2017). This shift in microglia phenotype might be preceded by a shift in the signaling mechanism that governs microglial functions, from a reduction in the production and secretion of neuronal Trx80 to the generation of a different type of signaling molecules that promote disease-associated microglial functions.

Nevertheless, we agree with the reviewers that the main current limitation of this work is that it ha s been mainly performed in vitro. To better understand the involvement of Trx80 in regulating microglia function in vivo and its relevance in an AD context, we will:

• Induce Trx80 production in neurons in vivo by performing stereotaxic injections in the prefrontal cortex of adeno-associated virus (AAVs) carrying the Trx80 sequence under the neuronal promoter synapsin, that will allow for Trx80 overexpression exclusively in neurons. We will analyze the effects of neuronal Trx80 overexpression on surrounding microglia by determining the expression of IRM signatures both by immunofluorescence and RT-qPCR.

• We will also use this system to analyze the effects of Trx80 in APPNL-G-F mice, where we will determine the effects of Trx80 overproduction in neurons on amyloid pathology in the Trx80-transduced hemisphere compared to the opposite hemisphere of the same mouse that will be transduced with control virus. These mice develop plaques at 3 months, we will therefore perform injections in 2 month-old mice and determine the effects of Trx80 at 1, 2 and 4 weeks post-transduction.

1. They show that Trem2 silencing in vitro prevents Trx80-dependent expression of genes characterizing IRM phenotype in microglia. Notably, they did not show any data about the expression of these genes in 3 and 10 months old APPNL-G-F mice, not in young and 22 months old Cyp27Tg. Enhanced Trx80 levels in 22 months old Cyp27Tg do parallel enhanced expression of IRM markers?

We did not further look at the interferon response genes in the APPNL-G-F mice because their presence in this mouse model was previously reported at a single cell resolution in microglia (Sala-Frigerio et al., 2019). We will change the text in our manuscript to a more detailed explanation about this previously reported data on IRM gene expression at different ages of the APPNL-G-F mouse.

Regarding IRM markers in Cyp27Tg mice, we did look at microglia expressing ISG15, an interferon response protein, in 22 months old Cyp27Tg mice and their age matched controls by immunofluorescence. As we report in Figure 4D, we found that 22 months old Cyp27Tg mice had a higher proportion of microglia ISG15 positive. Looking at other markers was limited due to antibody availability and specificity.

As we mention in point 2, we will further determine the presence of IRMs by performing FANS of neurons, microglia and astrocytes from 22 month old Cyp27Tg mice. We expect that, even in theIRM population is small, by performing RNAseq analysis in a cell-specific manner, we will be able to find an increase in IRM molecular signatures in microglia.

1. Is there brain inflammation in 22 months old 22 months old Cyp27Tg?

We appreciate the point raised by the reviewer. 27-hydroxycholesterol (27-OHC) has been previously described to induce inflammation in the periphery (Umetani et al., 2014) as well as in the brain in the form of S100A8-RAGE signaling pathway (Loera-Valencia et al., 2021). However, to confirm this in our experimental model, we will run an V-PLEX Plus Mouse Cytokine 19-Plex Kit of inflammatory markers by ELISA (MSD). This panel will allow us to accurately measure the levels of IFN-γ, IL-1β, IL-2, IL-4, IL-5, IL-6, IL-9, IL-10, IL-12p70, IL-15, IL-17A/F, IL-27p28/IL-30, IL-33, IP-10, KC/GRO, MCP-1, MIP-1α, MIP-2 and TNF-α in 22 months old Cyp27Tg and age-matched control brain homogenates from the prefrontal cortex.

This point will further be clarified by the FANS-RNAseq experiment described above.

1. Decreased levels of Trx80 in 10 months old APPNL-G-F mice do parallel decreased levels of IRM markers compared to age matched control mice?

According to Sala-Frigerio and colleagues that evaluated the gene expression profile of microglia isolated from APPNL-G-F mice at single-cell resolution, IRM population progressively increases with age (Sala-Frigerio et al., 2019). This suggests that several factors other than exposure to Trx80, including DNA-damage accumulation, that has been previously reported to be associated with an IRM-like response in human brains (Mathys et al., 2017) might as well promote and sustain the IRM phenotype. Further research will be therefore necessary to fully understand the finely-tuned mechanisms that regulate microglia states, both with temporal and spatial resolution.

alterations. The authors need to clarify the functional relevance of their data, so several experiments are necessary.

We thank the reviewer for her/his comment, and we agree that studying the functional relevance of this system will help to greatly improve the quality of this work.

As described in point 4., we will determine the functional relevance of Trx80 in vivo and whether it influences amyloid-beta-induced alterations by performing stereotaxic injections of AAVs carrying Trx80 before the first plaques appear in the mouse and at different time-points post transduction(1,2 and 4 weeks) to determine how Trx80-overexpression induced reactive microglia in vivo alters amyloid pathology-derived alterations.

Reviewer #1:

1. Minor comments: Figure 3f: in the text is written "neurons", while in the figure legends is written microglia.

We apologize for this mistake and we have now changed the text accordingly (p.11, l. 258).

CROSS-CONSULTATION COMMENTS

Microglia are quite resistant to viral transduction so the 50% knockdown by siRNA further raises the question of their identity in culture

We would like to apologize for the misunderstanding regarding the Trem2 silencing transduction since it is missing in the methodology part. We did not use viral transduction, we used siRNA mediated transduction (Horizon SMARTpool siRNA) as it has been previously and successfully used in primary microglia cultures (Ruan et al., 2022). We have now added this information to the methods part of the manuscript (p.6, l.137-142).

The subject of study is potentially very interesting because of investigating the role of Tx80 in microgliaand showing that Trx80 acts through Trem2, which is implicated in AD. Microglia and oxidative stressare considered playing a key role in AD progression. However, data are very preliminary and thismanuscript does not present data showing the functional relevance of Trx80 in AD.

• We agree and thank the reviewer for her/his comments. We believe that the newly planned experiments describe above will help to address the function of Trx80 in vivo and its relevance in an AD context (by determining its effect in the APPNL-G-F mouse model of amyloid pathology) will help to greatly improve this study.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

In this manuscript, Goikolea and colleagues aim to describe how neuronal thioredoxin-80 (Trx80)influences microglial reactivity. Because Trx80 levels track with age and amyloid pathology, understanding this signaling axis provides insight into the pathogenesis of AD. The authors show that pyramidal neuron expression of Trx80, rather than its precursor, is upregulated in aging and the APP mouse model of AD. They show that Trx80 induces interferon response gene induction in microglia cultures and that knockdown of Trem2 prevents this. This work has the potential to be very impactful.

Minor points:

One wonders if the discrepancy between gene, precursors, and Trx80 is due to lack of degradationof Trx80 with age. If anything is known about this, the authors might comment on its regulation inthe discussion.

We apologize for the misunderstanding. We will improve our explanation on Trx80 regulation in thediscussion.

Methods for siRNA knockdown appear to be missing.

We apologize for this mistake. We have now included it in the text p.6, l.137-142).

Reviewer #2 (Significance (Required)):

This work has the potential to advance our understanding of how a known anti-oxidant Trx80 contributes to microglial states. Given the major limitation of being an in vitro study, the extrapolation of these findings into AD pathogenesis are not possible.

We agree and thank the reviewer for her/his comments. We believe that the newly planned experiments describe above will help to address the function of Trx80 in vivo and its relevance in an AD context (by determining its effect in the APPNL-G-F mouse model of amyloid pathology)will help to greatly improve this study in this regard.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In this manuscript, Goikolea and colleagues aim to describe how neuronal thioredoxin-80 (Trx80) influences microglial reactivity. Because Trx80 levels track with age and amyloid pathology, understanding this signaling axis provides insight into the pathogenesis of AD. The authors show that pyramidal neuron expression of Trx80, rather than its precursor, is upregulated in aging and the APP mouse model of AD. They show that Trx80 induces interferon response gene induction in microglia cultures and that knockdown of Trem2 prevents this. This work has the potential to be very impactful.

The major limitation of this work is that it is conducted strictly in vitro or ex vivo - without return to the invivo state with cell-specific knockout of Trx80 and subsequent analyses of microglial phenotypes. This is of particular importance given that microglia are exquisitely sensitive to manipulation and there is increasing evidence that in vitro states (especially not those derived from mixed glial cultures) are not representative of true in vivo production. Microglia are quite resistant to viral transduction so the 50% knockdown by siRNA further raises the question of their identity in culture. If the authors cannot manipulate Trx80 in vivo in a cell specific way, they might consider using more highly purified more invivo like cultures such as those championed by Bohlen et al, Neuron, 2018.

Minor points:

One wonders if the discrepancy between gene, precursors, and Trx80 is due to lack of degradation of Trx80 with age. If anything is known about this, the authors might comment on its regulation in the discussion Methods for siRNA knockdown appear to be missing.

Significance

This work has the potential to advance our understanding of how a known anti-oxidant Trx80 contributes to microglial states.

Given the major limitation of being an in vitro study, the extrapolation of these findings into AD pathogenesis are not possible.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript entitled "Neuron-derived Thioredoxin-80: a novel regulator of type-I interferon response in microglia" demonstrates that neurons are the major source of Trx80, derived from the cleavage of Trx, into the brain. Trx80 production increases during normal aging. On the contrary, APPNL-G-F mice shows an opposite trend compared to wild type mice: Trx80 levels are significantly higher in 3 months old mice compared to age matched littermate, while significantly decreased in 10 months old APPNL-G-F mice compared to controls. The authors revealed that oxidative stress induced Trx80 production in neurons and this effect is Nrf2-dependent. Indeed, rotenone - an oxidative stress inducer- enhanced both Nrf2 expression and Trx80 levels. In agreement, 27-hydroxycholesterol (27-OHC), which promotes oxidative stress, promoted Trx80 production and Trx2 expression in neurons. In addition, 22 months old 27-OHC over-producing (Cyp27Tg) mice showed enhanced levels of Trx80. By gene expression analysis, the authors reported that Trx80 treated microglia showed a IRM gene expression profile, because of an enhanced expression of genes considered as IRN markers. They demonstrated in vitro that Trx80 promotes the IRN phenotype in microglia through Trem2. Knock down of Trem2 in microglia prevented Trx80-mediated enhanced expression of IRM markers.

Major Comments:

This work is potentially interesting, but the results are very preliminary. There is not a clear demonstration of the signaling pathways triggered by oxidative stress and leading to Trx80 production in neurons. The authors claim the role of Nrf2, but did not silence Nrf2, nor demonstrated the cascade downstream Nrf2 that is responsible for Trx80 production. In addition, Cyp27Tg mice show higher Trx80 levels only at a very old age and it is not at all shown that oxidative stress is responsible for Trx80 enhanced production in this mice model.

The authors claim a role of Trx80 in promoting IRM phenotype in microglia. However, there is not any data showing its relevance in Alzheimer`s (AD progression). They show that Trem2 silencing in vitro prevents Trx80-dependent expression of genes characterizing IRM phenotype in microglia. Notably, they did not show any data about the expression of these genes in 3 and 10 months old APPNL-G-F mice, not in young and 22 months old Cyp27Tg. Enhanced Trx80 levels in 22 months old Cyp27Tg do parallel enhanced expression of IRM markers? There is brain inflammation in 22 months old 22 months old Cyp27Tg? Decreased levels of Trx80 in 10 months old APPNL-G-F mice do parallel decreased levels of IRM markers compared to age matched control mice? Which is the significance of this pathway in AD?

It may be interesting to analyze whether microglia pre-treatment with Trx80 alters Abeta-induced alterations. The authors need to clarify the functional relevance of their data, so several experiments are necessary. Methods and data are sufficiently described.

Minor comments:

Figure 3f: in the text is written "neurons", while in the figure legends is written microglia

Referees cross-commenting

Comments to reviewer 2 opinion: "The major limitation of this work is that it is conducted strictly in vitro or ex vivo - without return to the invivo state with cell-specific knockout of Trx80 and subsequent analyses of microglial phenotypes. This is of particular importance given that microglia are exquisitely sensitive to manipulation and there is increasing evidence that in vitro states (especially not those derived from mixed glial cultures) are not representative of true in vivo production. Microglia are quite resistant to viral transduction so the 50% knockdown by siRNA further raises the question of their identity in culture. If the authors cannot manipulate Trx80 in vivo in a cell specific way, they might consider using more highly purified more invivo like cultures such as those championed by Bohlen et al, Neuron, 2018." I agree that in vivo experiments are necessary. Moreover, also the in vitro studies presented are preliminary.

Significance

The subject of study is potentially very interesting because of investigating the role of Tx80 in microglia and showing that Trx80 acts through Trem2, which is implicated in AD. Microglia and oxidative stress are considered playing a key role in AD progression. However, data are very preliminary and this manuscript does not present data showing the functional relevance of Trx80 in AD. The audience that maybe interested in the subject proposed by the authors are scientist working on: AD, aging, oxidative stress, microglia activation.

My fields of expertise: Alzheimer, oxidative stress, TXNIP function, inflammation, neurodegeneration, microglia, gene expression

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a response at this time.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #4

Evidence, reproducibility and clarity

In the manuscript "ATP induced conformational change of axonemal outer dynein arms studied by cryo-electron tomography", Noemi Zimmermann et al. built pseudo atomic models of outer dynein arms (ODA) from the native axonemes with and without ATP treatment using a combination of cryo-electron tomography (cryo-ET), sub-tomogram averaging and atomic model fitting analysis. The authors clearly distinguished several important conformations of ODA using their high-quality cryo-ET maps. The authors showed that in situ ODA conformation in post-power stroke state is different from in vitro ODA structures, either lacking B-tubule binding or A-tubule binding. In my opinion, this is a very important observation by taking the advantage of cryo-ET analysis on intact axonemes. Furthermore, by freezing the activated axoneme immediately after ATP treatment, the authors obtained the active pre-power stroke and an intriguing intermediate conformation of ODA. By generating pseudo atomic models, the authors were able to compare the structural changes in dynein heads and stalks among different states and highlighted geometrical constraints from neighboring MTDs on ODA. Overall, the findings by Noemi et al have provided really exciting insights into ODA conformational changes during the power stoke. I therefore highly recommend publication of the manuscript. However, before the official publication, I do have some comments and believe the authors can further improve their manuscript to make it more exciting to the field.

1. The authors only showed the maps from sub-tomogram averages (Supply Fig 1). I suggest the authors also show a representative reconstruction of the whole tomogram as a supplementary figure so that we have a better overview of the reconstruction.
2. Since this is a typical piece of structural work, I highly suggest the authors summarize their cryo-ET data collection and processing parameters as a supplementary table, such as standard microscopy parameters, image pixel sizes, number of tomograms, number of particles etc.
3. On page 5 and Supplementary Figure 2H, I, the authors fitted Lis1 model to the additional density at the interface between AAA2 and AAA3. This is really intriguing. However, according the currently published Lis1-dynein structures (PMID: 28886386, PMID: 34994688), it seems that Lis1 interacts with dynein on AAA4 and AAA5. Can the authors discuss anything about the evolutionary conservation of Lis1 binding? In addition, the authors did not fit LC5 model into the density map. I am a bit worried that there might be some bias on Lis1. With the fast development of protein prediction tools like Alphafold and Rosetta fold, the authors would be able to have a nice prediction of the LC5 structure to fit the additional density. I therefore suggest the authors try to do so if it is technically feasible, and then discuss a bit more on this point.
4. On Page 6, the authors mentioned that "neither of the two structures (MTBS1, MTBS2) represented our conformation of ODA". This is an interesting finding since in the reconstituted ODA array on MTD by Rao et al., 2021 paper, they observed both MTBS1 (MTBD: 0 nm; MTBD:0nm; MTBD:8nm) and MTBS2 (MTBD: 0 nm; MTBD:8nm; MTBD:8 nm) conformations (Here, 0nm and 8nm represent the relative longitudinal positions along the tubulin lattice among the three MTBDs). According to the post-ODA structure from this manuscript, the authors found all three heavy chains are in the post-2 states, or equivalently with MTBDs at the 8-nm position (MTBD: 8nm; MTBD:8nm; MTBD:8nm, Fig3G). The authors also mentioned that the conformations of minimum energy of ODA are different in vivo and in vitro in the discussion. On the other hand, many structures previously determined by X-ray and EM in vitro show that Post-1 were overwhelmingly preferred before Rao et al reported the Post-2 state. This raises a very interesting question, how many MTBS states can ODA actually adopt in vivo? In theory, the three MTBDs can be arranged in at least a certain subset of the eight states (000,001,010,100,011,101,110,111) if the distance between any two MTBDs is restricted to 8nm, and the movement of each MTBD is restricted along one direction. There might be more states if the movement is more than one step. Therefore, from the results of both this manuscript and Rao et al., 2021 paper, probably not all states could have been observed. I wonder if the authors can perform more 3D classification on their STA particles in the post-PS state to demonstrate and see if there is any chance to see more states in vivo. I was a bit surprised because I felt there might be more states in vivo than in vitro reconstitution. The idea that the two neighboring MTDs can restrict the ODA conformation is great. I suggest the authors discuss more about the possible effects from two neighboring instead of just a general concept of energy minimization (probably it is impossible to estimate the total energy of such a complex system under physiological conditions using any kind of currently available techniques).
5. In Figure 4, the authors observe structural changes of ODA among different states. The figures clearly show the differences among post-PS, intermediate state, and pre-PS state. For the pre-PS and intermediate state, I wonder if the authors can map the two conformations back onto the raw tomograms and show how they look like in a relatively large region with more repeating units.
6. In Figure 4, I really appreciate the authors pointing out the distortion (changes in distances and the rotation angles) between adjacent MTDs. To my knowledge, the distortion of neighboring MTDs during ODA power stroke cycle has not been well analyzed in many previous publications. To gain more insights on this part, I wonder if the authors can perform more quantitative analysis on all adjacent MTDs with and without ATP from their current data sets. There are some nice publications on filament distortion analysis using single particle approaches, including one from the Sindelar lab (PMID: 32636254, Fig 4 and 6). More specifically, since the authors already have the position and Euler angle information of each particle from the subtomogram averaging, it is possible to extract the distortion information from two adjacent MTDs. After extracting distortion information from all MTD pairs and plotting the data points in different ways, the authors may be able to correlate the ODA conformation, MTD bending and see whether they could find some intriguing patterns. The authors do not have to incorporate all their results from this analysis into the current manuscript since there are already many interesting things, but briefly showing some curvature distribution would be highly appreciated, and the authors can still publish other interesting results in their future publications.
7. It seems the authors have not deposited their maps and PDBs (as they are XXXX's in the current manuscript). It would be nice to if they can do so at their earliest convenience.
8. On page 5, the authors found an additional density next to the  dynein which could be Lis1 or LC5 (see also minor comment #1). Again, this is an advantage using cryo-ET. This observation is also missing from ODA SPA papers, and I appreciate the authors for the careful examination. Since there are several 96-nm MTD maps from previously studies from Chlamydomonas and Tetrahymena, I wonder if this additional density is also present from previous cryo-ET maps.
9. On page 5, the sentence "one unit of the dimeric Homo sapiens Lis1 (PDB-5VLJ (Htet et al., 2020, p. 1)) and fitting it into our density allowed us to assess its likeability." The Lis1 model in PDB-5VLJ is from Saccharomyces cerevisiae, not from Home sapiens. In addition, the reference paper doesn't match the PDB-5VLJ. The authors should cite the correct paper.
10. On page 6 Figure 2 legend D, B HC should be  HC.
11. On page 8 Figure 3 legend "A and B) Rigid body fit of the whole MTBS1 map (Walton et al., 2021).". The citation here should be Rao et al., 2021.
12. In Figure 5, the authors generated models for the pre-PS conformation of ODA. From the cryo-ET density map, the authors suggested that -MTBD was in a bent conformation, which was similar to the conformation in shulin-ODA. This is a novel observation. Since the authors have atomic models, I suggest the authors directly use the PDB models for better visualization of structural changes among post-PS ODA, intermediate ODA, and pre-PS ODA. A supplementary figure or movie will be very nice.
13. On page 16 "EM grids" session, I suggest the authors provide slightly more details on their sample preparation, such as the concentration of the axoneme, blotting time, temperature, humidity etc.

Significance

Significance: This is a very nice manuscript for better understanding of the motile cilia system. It is a significant progress in the field with lots of interesting findings.

Audience: People in the field of dynein, motile cilia, cytoskeleton and in cryo-ET technique as well.

My expertise: I am very confident in reviewing this paper, both biologically and technically, and I have recently published in this field as well.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

The study attempts to reconcile cryo-EM SPA structures of ODAs with in situ tomographic reconstructions.

Several key discrepancies between SPA structures and the native in situ structures (here) are highlighted in the study with a particular focus on the positions of various ODA motor head components (linker, tails etc.) during the powerstroke cycle.

The study also highlights largely concordant inter and intra-ODA connections between previous SPA structures and the tomographic reconstructions.

Major comments:

Overall, the key conclusions are convincing. No additional experiments are suggested. The manuscript is acceptable provided minor comments below are addressed.

Minor comments:

The text could be improved throughout for improved clarity. Overall, the figures are good, but some panels are over-annotated which is confusing. Simplification or cartoon illustrations could add clarity to the figures.

CROSS-CONSULTATION COMMENTS

The paper still represents a significant and sufficient advance. Correction of factual errors flagged up by other reviewers (use of correct references and citations, correct species for Lis1 models used etc.) is required and essential prior to acceptance. Addition of more details in the sample preparation methods section would also be useful. Depositing PDBs and maps is recommended.

Agree on the overall point of improving accessibility and readability of the text. Figures can be much improved to highlight the biological insights for the reader.

The point of contention between extra density corresponding to either Lis1 or LC5 is valid. Tempering the assertion and removing bias towards Lis1 in the text would resolve this issue. The authors are putting forth a speculative model which is valid; this model can be tested in future work.

Several minor comments highlighted by other reviewers are fair and should be addressed as best as possible.

Several major comments highlighted by other reviewers (specifically: use of structure prediction and modeling, filament distortion analysis etc.) are well beyond the scope of the present work and do not advance the specific and main conclusions of the current study.

Significance

The study presents structures of ODAs during their powerstroke cycles in situ in their native context and integrates previous structural models of ODAs to provide novel insights.

The identification of a Lis1 or LC5 like density adjacent to the alpha-HC and observation of a curved position of the beta-HC stalk in the native state adds further novelty to the study.

The study will be of interest to researchers like myself working on cilia motility and dynein motors.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

• The authors report cryo-EM tomography of the axoneme of motile cilia in the presence and absence of ATP, providing new insight into the mechanism of action of the motors. They use crystal structures and information from single particle cryo-EM to fit these fragments into their new density obtained in situ, and show that distortions to these smaller structures are required for them to be accommodated in the complex and crowded environment of the axoneme. The movies provided show the relevant fits in 3D, which is important because the complexity of the structures makes 2D visualisations limited. Are the authors sufficiently confident in their atomistic models that they would be useful for other researchers, and if so are they planning to release them (e.g. as pdb files) with the paper, or on request?

• There are potentially a few editorial additions and changes that the authors might consider making to improve the readability of the paper for non-specialists in the axoneme. For example, could they insert a sentence explaining what Shulin is and its biological significance? There are numerous abbreviations and acronyms throughout the manuscript - would it be helpful to maybe write some of those out in full where appropriate? In the very helpful Supplementary table containing the pdb IDs used to fit into the current structure, would it be useful to have a small picture of each system as one of the columns in this table? Would it also potentially be helpful to include a figure summarising the different types of dynein observed in this and other relevant studies - e.g the pre and post-powerstroke states, Shulin bound etc? This would help the reader to understand the magnitudes of the conformational changes between these various states that are under discussion. Could a schematic diagram representing the "winch" and "rotation" models be included potentially? In the Discussion section, I was not able to understand whether the winch or rotation models are most supported by the data in this paper, or whether a mixture of the two might be needed to understand axoneme mechanics, so further clarification of this would be helpful.

• Please note that all of these comments are suggestions to improve accessibility and readability, and are not essential additions for the paper to be publishable.

CROSS-CONSULTATION COMMENTS

I was very interested to read the detailed and informative comments from the other referees. While I agree with referee 1 point 4 that the use of alpha-fold to predict how atomistic structures from different organisms may differ, and subsequent flexible fitting would be desirable, this in my opinion would be an enormous amount of work, and would be best reserved for subsequent publications. Sharing of the pdb files of the fitted structures obtained so far would open this mammoth task up to the rest of the community.

Given the complexity of the axoneme, and the huge amount of expertise needed to obtain and process these tomograms, I did wonder if this community would consider forming a collaborative consortium where researchers worked together to construct a common model.

Significance

• The paper reports more complete and detailed structural information on the axoneme than (to my knowledge) has been obtained before. The fitting of atomistic level structures into the density to create a pseudo-atomic model is highly instructive.

• To me, it was not in the least bit surprising that distortions from the structures obtained in isolation using single particle analysis are required for an optimal fit. In fact, theoretical work reported by Richardson et al, QRB 2020 showed for inner dynein arms that the crowded environment provided solely by the microtubule tracks within the axoneme modified the conformations of the dynein stalk that were accessible compared to a simple isolated dynein motor. While this study considers outer dynein arms, the conceptual physical rationale is equivalent to the findings here. In my opinion, the finding reported in this paper that considering fragments of biological ultrastructures is not necessarily equivalent to the whole functioning entity is both important and profound, and has implications beyond motile cilia, particularly as cryo-electron tomography enables us to visualise ever larger and more complex functional biological assemblies.

• Please note that my area of expertise does not enable me to comment on the experimental procedures used to obtain the tomograms, as I am a computer modeller with an interest in dynein.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary

Zimmermann et al. provide a comparison between recent atomic models of the ODA determined by single particle cryo-EM and their conformation within intact axonemes by cryo-ET subtomogram averaging. They observed slight changes in the position of the motors for the structures of Kubo et al. and Walton et al., but the structure of Rao et al. required more changes, indicating that within the axoneme, the conformation of the ODA is influenced by the MTD on which it is docked, and the neighboring MTD to which its motors bind. They then use the information from their newly fit models to interpret cryo-ET maps of axonemes in the presence of ATP, which activates the ODA and other axonemal dyneins. They observe two states of the ODA, and describe how the position of the motor, linker, MTBD and LC tower change during the powerstroke cycle. A revised model of the ODA and the ability to describe conformational changes at the subunit level provides an advance on previous work and will be of interest to the dynein and cilia fields. However, the comments below must be addressed prior to publication, and additional work is needed to make the paper accessible.

Major comments

1. Greater clarity is needed in the introduction to explain the differences between the recent atomic models of the ODA. This is essential to understanding the paper, including Fig. 3. Arguably, the top half of Fig. S2 provides a stronger case for the study than any of the current main figures.

2. In the manuscript, potential differences between Chlamydomonas and Tetrahymena ODAs are not considered but need to be explored. Comparison of Tetrahymena models within Chlamydomonas maps could result in misinterpretations.

3. Systematic quantification of the fit-to-map should be provided for the models before and after refitting (together with evidence - see the point below - that the model has not been inappropriately distorted to fit the map). This information could be inserted into an expanded Supplementary Table.

4. Because the revised pseudo-atomic model of the ODA is a chimera of PDBs from different organisms, it does not accurately represent the Chlamydomonas ODA. The modeling method also has the potential to introduce clashes between rigid-body fitted chains. Validation of the model is necessary, and alternative approaches to generate a more accurate model (e.g. AlphaFold and molecular dynamics flexible fitting) should be considered.

5. Additional evidence needs to be provided to demonstrate that the intermediate state observed in Figure 4 is robustly detected and does not simply represent the data that doesn't fall into the "good" classes. In Fig. S1, the map looks very noisy and requires denoising. Are there other changes observed in the IDAs that would support the existence of an intermediate state?

6. The speculation that the additional density bound to a-HC is Lis1 is not well-supported. Lis1 binds AAA4/5 (PDB: 5VH9), not AAA2/3. The fit of the Lis1 homolog into the cryo-ET density does not appear consistent with Lis1 binding the motor. The authors should consider other possibilities that could explain the additional density.

Minor comments

1. The results section "Post-PS structure and Fitting of the atomic models" is very dense. It should be split into subsections to help guide the reader through specific models or regions of the ODA.

2. ODA numbering should be made consistent with previous papers (i.e. ODA1-4 as in Bui et al., 2012)

3. The ODA-shulin model (PDB: 6ZYW) is inaccurately described as the state transported during IFT, but experimental confirmation of this hypothesis is lacking.

4. The term TTH for tail-to-head contacts is too similar to T/TH for the tether/tetherhead complex and should be changed. An abbreviation may not be necessary.

5. Please check to make sure that all figures and figure legends clearly specify which map/model/motor is being shown. This will make the figures easier to follow.

6. The structures in Fig. 3 are from Rao et al., not Walton et al.

7. Fig 5M-O is very difficult to interpret. Could the authors consider coloring by region, for one of the maps, or at least put the maps in a similar orientation to the ODA cores as in Fig 2?

8. The final processing step in panel Fig S1B is confusing. Additional information is needed to explain the supervised classification step and how the final particle set was derived.

9. Atomic resolution should not be used to describe structures determined to 4.3 Å resolution (e.g. EMD-11579).

10. Supervised classification is not a method of validation

11. Please check for grammatical and spelling errors throughout the manuscript.

Significance

While previous literature has interpreted ODA conformation in broad regions, this study goes farther by using recent atomic models to identify specific subunits that change conformations and interactions during the powerstroke. From my perspective as a structural biologist in the cilia field, I think this paper provides a conceptual advance to the study and interpretation of axonemes.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reviewer #1

• The authors claim that bin2 has a "confused" phenotype, which they define as high variability in shoot versus root lengths along with a low degree of response to water limitation. bin2-1 is a semi-dominant gain-of-function mutant, which can only be propagated as a heterozygote (homozygous individuals are viable, but don't produce seeds). There is no mention in the manuscript about genotyping or selection of homozygous bin2-1 individuals for the phenotyping assays. Could the high variability observed in fact be caused by the authors looking at a segregating population of bin2-1? * By propagating plants under optimal growth conditions over > 4 months at the TUMmesa ecotron, we were in fact able to obtain over 24 individual homozygous bin2-1 plants. We distinguish homo- and heterozygous seed by (i) adult phenotype (ii) segregation in the next generation (iii) root:shoot ratios from dark-grown seedlings on plate and (iv) sequencing of the TREE domain (as shown in Fig. 2e). Therefore, we are sure to have used only homozygous mutants in our analysis. This is now specified in the supplementary method S5.

*The authors state that bin2 mutants had considerably more severe phenotypes than other BR biosynthesis, perception, or transcription factor mutants. This is like comparing apples to oranges, as the set of mutants they've examined consists of gain-of-function and partial loss-of-function alleles. Null alleles for BR biosynthesis (e.g. cpd, dwf4), perception (bri1brl1brl3 triple mutants) and transcription factors (bzr1bes1beh1-4 sextuple mutants) are described in the literature and would need to be tested before arriving at such a conclusion. *

This is an important point and the nature of all alleles was and still is clearly outlined in Table S1 “Lines used in this study”. We have obtained and propagated bri1brl1brl3 triple mutant seed from Christian Hardtke (Kang et al., 2017), as well as null cpd alleles from NASC and these now complement or replace det2-1 and bri1-6 in our analysis. We compare null alleles, semi-dominant or dominant or higher order null alleles with each other. To make these comparisons clear we have highlighted these different allele types in the manuscript as depicted in the table, with null in regular font, semi-dominant or dominant in bold and higher order mutants underlined. This is described in Table S1 and in the figure legends, where applicable. We have not been able to obtain and propagate enough seed in the period of review to extend the analysis to sextuple transcription factor mutants. Therefore, we have removed the comparison between brassinosteroid mutants and now refer to the importance and role of the brassinosteroid pathway in general and, more specifically, to BR signaling rather than to BIN2.

*For most of the phenotyping experiments a "RQ ratio" is presented. This is the ratio adjustment of the mutant/ratio adjustment of WT. While this derived quantity is useful for interpretation, we're missing plots of the raw data, and particularly those that show the underlying distribution of data points. *

We understand that the RQratio (Fig. 4e) value is a step removed from the raw data. Please note that we also show the RQshoot (Fig. S8a) and the RQroot (Fig. S8b) in the supplement. We now depict violin plots in Fig. 4a-c and Fig. S7 as a best representation of the raw data, as follows

Results page 10: “The violin plots compare organ length distributions in mutants versus the corresponding wild-type ecotype, which depicts dwarfism in some brassinosteroid mutants. It is also apparent that wild-type (Col-0) root length varies under water-deficit in the dark (Fig. S7). Although we have optimized protocols for PEG plates to the best of our ability, there is still a lot-to-lot and plate-to-plate variation. This emphasizes the need for normalizing each mutant line to its corresponding wild-type ecotype on the same (PEG) plate in the same experiment. To this end, the response to water stress in the dark was represented as a normalized response quotient (RQ), which is an indication of how much the mutant deviates from the corresponding wild type (Fig. 4e; see methods).”

The RQhypocotyl, RQroot and RQratio are a necessary consequence of the variance in the data, and we consider them to be the most relevant metrics. Representative experiments were chosen from at least three replicates on the bases of RQ and P values (as specified in the legends of Fig. 3 and Fig. S10).

Root growth involves both cell division in meristematic cells at the tip of the root and subsequent elongation as cells exit the meristem and begin to differentiate. The authors claim a nine-fold difference in CycB1,1:GUS in the root meristem in dark vs darkW, however their images show similar CycB1,1:GUS expression patterns. Furthermore, the meristems of darkW are actually smaller than dark, which would be unexpected if cell division *was increased. *

We have reviewed the raw data again, applying blinding to avoid bias, and chosen a more representative image for the dark; the mitotic indexes are represented in a violin plot (Fig. 6c) to better show the distribution of datapoints. The conclusions are unchanged. We reimaged the wild-type under light, dark and darkW, specifically focusing on meristem properties and on final cell length. The results are presented in Fig. 6, Fig. S14, Fig. S15 and described as follows:

Results page 14:

“It is generally accepted that root growth correlates with the size of the root apical meristem (RAM; Beemster and Baskin 1998). Meristem size was assessed by computing the number of isodiametric and transition cells (González-García et al., 2011; Verbelen et al., 2006; Method S8). In addition, we applied a Gaussian mixed model of cell length to distinguish between short meristematic cells and longer cells in the elongation zone (Fig. S14; Fridman et al., 2021). Meristem size was shortest under water deficit in the dark (Fig. 6a; Fig. S15a,b) and, surprisingly, did not correlate well with final organ length (Fig. 1c; Fig. 6g). “

Discussion page 16:

“it appears counterintuitive that meristem size and organ length do not correlate in our conflict-of-interest scenario. Questions arise as to why the meristem is smaller under water deficit in the dark even though the mitotic index is higher than in the dark, and how growth is promoted under our additive stress scenarios. An important difference between our conditions and those described by others is that we germinated seed under limiting conditions in the dark in the absence of a carbon source… When water stress was applied in the dark, the mitotic index increased, but the newly produced meristematic cells immediately elongated, thereby exiting the meristem. As a consequence, meristem size remained small despite the increased number of mitotic cells. It appears that what our study shows is a novel paradigm for root growth under limiting conditions, which depends not only on shoot-versus-root trade-offs in the allocation of limited resources, but also on an ability to deploy different strategies for growth in response to abiotic stress cues.”

We are not aware of any other study that has addressed root growth under water deficit in the dark and in the absence of a carbon source.

• In addition, the authors claim that the longer root length in dark water stress was at least in part due to increased elongation (Fig. 7c). Elongation was only assessed by looking at the first elongating cell (~10-14um) and the differences found are on the order of magnitude of ~2um, but final cell size in Arabidopsis roots often reaches several hundred um. Therefore, a comparison of final cell size would be more appropriate. *

Results page 14:

“mature cell length… was highest in the dark, the condition with the shortest roots (Fig. 6b). Thus, neither meristem size nor mature cell length account for the fold-change in final organ length (Fig. 6g).”

*Finally, the authors phenotype plt1/2 double mutants and show that they fail to elongate in response to water limitation. Their interpretation is that this supports a centralized control model for the root apical meristem. PLT1/2 are important determinants of meristem function and are necessary to maintain stem cell identity. Given the strong phenotype of plt1/2 double mutants it is not surprising that they are unable to elongate in response to this stimulus. This does not necessarily indicate that only the RAM controls root growth, but rather that functional stem cells are required for root growth, which also involves subsequent steps such as cell elongation. *

This is an important point and we thank the reviewer for pointing it out. We now write:

Results page 15:

“Taken together, the cell length and anisotropy curves (Fig. 6) and genetic analyses (Fig. 6; Fig. S15f; Fig. S16) suggest that root length under our different environmental conditions is regulated by (i) the mitotic index, (ii) the timing of cell elongation or of exit from the meristem and (iii) cell geometry. We also conclude that these are differentially modulated to account for increased root length under different environmental conditions (Fig. 6c-e).”

We also modulate the conclusion and model (Fig 7c) to state that RAM function accounts “in part” for root growth. However, it is to be noted that mature cell length in our study did not correlate with root length (Fig. 6b, 6g). Our conclusion is now reached not solely based on plt1plt2 but also on a careful and quantitative cellular analysis of the root apical meristem in the wild-type and in bin2-3bil1bil3 mutants. The major contribution of our study, however, is the difference between the different conditions, and the ability to respond to stimulus.

*Reviewer #1 (Significance (Required)): *

* While the study system and some of the findings in this manuscript are interesting, there are major flaws in the authors' primary claims. *

Contested claims have been (i) deleted where unessential to the storyline or (ii) substantiated by independent methods.

*Reviewer # 2 *

1. I recommend to exchange shoot for hypocotyl when hypocotyls were examined to avoid to confuse the readers. We thank the reviewer for pointing this out and have exchanged shoot for hypocotyl throughout.

2. The authors have chosen SnRK2 (and should also indicate it in all Figures as SnRK2, to not confuse the readers with SnRK1), and implement ABA signaling in parallel to BR action, but this must be proven in higher order mutants of both pathways, at the moment the results are to preliminary to allow conclusions. *

We concur with the reviewer that higher order mutants between the BR and ABA pathways would be required to make this claim. We also concur that this would require numerous generations and therefore that it does not lie within the scope of this manuscript.

• When the authors are interested in shoot dominance/photosynthetic activity, why didn't they look on snrk1 mutants, which are known to regulate those processes. *

The issue of energy signaling is a key one, and we mention this in the final “perspective” paragraph of the discussion (p. 18) as follows:

“As a limited budget is an essential component of our screen conditions, the role of energy sensing and signaling (Baena-González and Hanson, 2017) in growth tradeoffs will need to be elucidated.”

• In Fig6d the authors propose a sketch of the mechanism, but the data of this study don't show direct interaction of the pathways and as indicated in the figure text parts of the information are taken from other papers, I recommend to remove this sketch or shift it to the supplements. * We concur with the reviewer and have deleted former panels 6d, 6e and 6f as well as reference to the mutants these included. We now focus on the BR pathway, as discussed below.

*To discriminate the role of downstream BR signaling events from other roles of BIN2, I suggest to complement the data with pharmacological experiments (eBL or bikini where appropriate), and if possible to implement phenotyping of OE lines. *

In response to this comment, we attempted bikinin experiments. Unfortunately, it is difficult to germinate seed on bikinin and seedlings grow poorly on this shaggy-like kinase inhibitor. As the assay relies on seed germination rather than on seedling transfer, applying bikinin was suboptimal. Because of the requirement for germination in the dark, and in lieu of eBL or PPZ or a combination thereof, we now include a null allele of a BR biosynthesis mutant, cpd, in Fig. 3b, to replace the leaky det2-1 mutant we had previously used.

How many independent ko lines were tested, can the authors exclude that the BR independent phenotype indeed corresponds to BIN2 activity and not to a off target effect.

Four independent bin2 mutants (B1, bin2-1, ucu1, dwarf12) were analyzed in our study. In total, 83000 M2 seed were used in our forward genetic screen; of these and for BIN2 the B1 line is the one we rescreened, mapped and characterized. We complemented B1 with bin2-1 and ucu1 alleles and compared it to bin2-1, ucu1 and dwarf12 alleles at the BIN2 locus; these three published mutant lines exhibited the same behavior as B1, including semi-dominance and phenotypes under single versus multiple stress conditions (Fig. 2c cf Fig. 3d; Fig. S6). Fine mapping (Fig. 2d), segregation analysis (Table S2), allele sequencing (Fig. 2e), backcrossing, outcrossing and complementation analysis provide independent lines of evidence that B1 is a BIN2 allele. Please note that the conclusions regarding BIN2 in this manuscript are based not on B1 but on the published bin2-1 and bin2-3bil1bil2 lines.

We write results page 10:

“We complemented B1 with bin2-1 and ucu1 alleles and compared it to bin2-1, ucu1 and dwarf12 (Perez-Perez et al., 2002; Choe et al., 2002) alleles at the BIN2 locus; these three published mutant lines exhibited the same behavior as B1, including semi-dominance and partial etiolation.”

*I further recommend to exchange the pictures in Fig7a showing BRI1-GFP to pictures showing fewer cells, but with higher resolution. *

We now show higher resolution images in Fig. 7b.

• Regarding the implementation of photoreceptor mutants and the claim that photoreceptors are more abundant in shoot, I want to point out that the situation is more complex, as the root also reacts differently to light of different quality and quantity, with different responses in the meristem, by inhibiting cell proliferation, or in the elongation zone by triggering negative phototropism. this should be corrected in the text. *

We are aware that light, especially when Arabidopsis is grown on media, is perceived by photoreceptors within the root system. Phototropic growth would not have affected measurements of root length as measurements were performed in ImageJ with the freehand tool. This is described in the methods on page 6, and in the supplementary method S5. For the model, we have now modulated our discussion as follows:

Discussion p. 16-17:

“ we postulate that a hypocotyl to root (basipetal) signal coordinates trade-offs in organ growth in response to light (Fig. 7c green arrow). However, and even though photoreceptors are considerably more abundant in the hypocotyl than in the root (van Gelderen et al., 2018), it needs to be borne in mind that photoreceptors in the root could be playing a role in root responses to light or to darkness (Mo et al., 2015).”

*The data and methods are presented in a clear and sufficient way, as well as the statistical analysis. *

We thank the reviewer for this positive assessment.

*Altogether, the hypothesis and work amount are worth to be recognized, but the manuscript also resembles partially more a review and I would suggest to shorten those parts in the manuscript, reduce the amount of described lines and focus strictly on the BR pathway, in response to the environmental changes. Before implementing photoreceptors and ABA/SnRK2 pathway into the story to either test higher order mutants between the signaling pathways of interest or come up with a pharmacological screen connecting the data. Therefore I suggest to reduce the amount of mutants investigated and focus on BIN2 action, implementing also a pharmacological screen to track a fluorescent tagged BIN2 upon the mentioned treatments. And if possible to add proteomics and phosphoproteomics to understand better what changes are undergoing in the bin2 mutant vs WT upon stress. *

We thank the reviewer for suggesting that we “focus strictly on the BR pathway, in response to the environmental changes”, as this has truly supported us in tightening the story line.

We have removed the sections of the manuscript that resembled a review and focus entirely on the BR pathway, with additional or tighter mutants. We also look at BIN2 more closely and at a cellular level, with SEM micrographs for the hypocotyl and CSLM for the root tip. The BIN2 interactome on BIOGRID comprises 36 well annotated interactions (https://thebiogrid.org/12898/summary/arabidopsis-thaliana/bin2.html), of which 2 are documented by multiple lines of evidence and 27 are from low throughput studies. Adding adequately validated interactions to this exceeds the scope of this manuscript. Furthermore, as we no longer make the claim that BIN2 mutants are the most severely impacted (see response to reviewer #1), BIN2 is no longer the primary focus of this study; we now refer more loosely to the BR pathway, or to facets thereof referred to as BR biosynthesis, perception, signaling or BR-responsive gene expression. We have also updated and extended the reference list to include references on light perception and energy sensing or signaling. Phosphoproteomics is an important suggestion that we have also taken into the perspective.

In brief, the manuscript has a new focus on what we consider is its true contribution: a cellular analysis of cell division, elongation and anisotropy in the wild type and in BR mutants under resting or additive stress conditions.

*Reviewer #3 *

1. *My major concern is that in the search of a decision mutant the authors performed the first screening not under 'a conflict of interest' scenario but under dark conditions. Can the authors explain the reasons behind this more clearly? * The reason we did not use the dark water stress condition as an initial but as a secondary screen is the variability of the response. In the new violin plots (Fig. 4a-c; Fig. S7), the variance especially in root length can be seen to be considerably greater in darkW than in dark even for the wild-type. This is why we initially screened individual M2 seed in the dark and then rescreened M3 populations under darkW conditions. Due to the relatively high variance, all conclusions in the manuscript are drawn on populations of seedlings rather than on individuals.

We write in the results section on page 9:

“We initially screened in the dark because the high variance in root growth under water deficit in the dark in the wild-type (see below) would obscure the distinction between putative mutants versus stochastically occurring wild-type seedlings with short roots under darkW.”

• Related to above, the role of the BR pathway in etiolation has been well established with the prominent constitutive photomorphogenesis phenotypes of BR related mutants; since both bin2 alleles are impaired in light responses this mutant may behave in dark vs darkW, like a wildtype plant in light vs. lightW (maybe also partially as shown in SFig. 5a). However, the authors show that the growth tradeoff was not evident under light conditions (Fig 2). I think to conclude that bin2 is a decision mutant it requires more evidence to excluded that a defect in efficient sensing and signaling of dark conditions are not the primary source of the 'confused' phenotype. In addition to the phenotype in SFig. 5a where light responses are attenuated in B1 when compared to Wt, a comparison of gene expression analysis of some established light regulated genes could help to show that bin2 is able to efficiently sense the absence of light. *

This is an important point. We have looked at the expression levels of the light responsive gene LHCB1.2 via qPCR in wild-type Ws-2 versus bin2-3bil1bil2. The data show that the gene expression is light-regulated in bin2-3bil1bil2 seedlings (Fig. S12) and are described in the Results on page 13.

In addition, Fig. S10 and Fig. S11 are dedicated to a careful analysis of light responses in all the BR pathway mutants we analyze. In Fig. S10d, bin2-1 can be seen to have a significant (P-value We write, in the Results on page 13.

“Interestingly, the BR mutant lines with the strongest etiolation phenotypes (cpd and bri1-116brl1brl3, Fig. S11a,b) in the dark were not the ones with the strongest deviation from the wild-type under water deficit in the dark (Fig. S8).”

3. Cells that fail to elongate in the dark may cannot - or only to a limited extent - reduce further their cell length in the darkW conditions. Since BR-mutants fail to expand hypocotyl cells in the dark, an analysis of the hypocotyl epidermis cell length in bin2 mutants compared to wt in light vs dark vs darkW (as in Fig. 8c) could be a feasible experiment to exclude that the general BR-related cell elongation defects led to the confused phenotypes of this mutant.

This is an excellent suggestion and we thank the reviewer for pointing it out. Accordingly, bin2-1 mutants were imaged via scanning electron microscopy (SEM) and cellular parameters assessed. We also investigated root meristem properties in bin2-3bil1bil2, which had the most aberrant root response to water stress in the dark (Fig. 3e; Fig. S8b). Our new observations are described in Fig. 5, Fig. 6h-j, Fig. S16 and in the results on pages 13-15 as follows:

“To explore whether general BR-related cell elongation defects led to the confused phenotypes of some BR pathway mutants, we analysed bin2-1 mutants, which were among the most severely impaired hypocotyl response to water stress in the dark (Fig. S8a). The data show a most striking impact of bin2-1 on growth anisotropy, assessed in 2D as length/width (Fig. 5f). Indeed, in a comparison between dark and dark with water stress (darkW), the anisotropy of hypocotyl cells decreased considerably in the wild type (Fig. 5c), but showed no adjustment in bin2-1 (Fig. 5f). Cell length alone showed the elongation defect typical of bin2-1 mutants, with a much greater deviation from the wild type under darkW than under dark or light conditions; nonetheless, there was a significant length adjustment to water stress in the dark, even in bin2-1 (Fig. 5e). These observations suggest that the impaired bin2-1 hypocotyl response can be attributed to an inability to differentially regulate cell anisotropy in response to the simultaneous withdrawal of light and water. ….

Meristem size and mature cell length followed the same trends in a comparison between bin2-3bil1bil2 (Fig. S16a, S16b) and the wild type (Fig. 6a, 6b), but the extent of elongation in cells proximal to the QC differed (Fig. S16c). Indeed, bin2-3bil1bil2 length and anisotropy curves lacked the steep slopes characteristic for darkW in the wild type (compare the green arrows in Fig. 6d, 6f & 6j to the purple arrows in Fig. 6j & Fig. S16c). We conclude that bin2-3bil1bil2 mutants fail to adjust their root length due to an inability to differentially regulate the elongation of meristematic cells in the root in response to water stress in the dark.”

• The experiments with the BR-deficient and signaling mutant and the bypass mutant may suggest that BR hormone is playing a relative minor role in the 'decision activity' of BIN2. bri1-6 was described to respond like wildtype (page10 line 6-8). Since this seems because of normal root responses in dark vs. darkW (Fig. 5) it could also be caused by the role of BRL1 and BRL3 in root drought responses (Fabregas et al., 2018). To verify if functional BRL1 and BRL3 in bri1-6 could cause the root response to water stress an additional experiment with bri1,brl1,brl3 triple mutant is required; In my opinion this is very important to state if the BR input is at all required for BIN2 signal integration or not. *

We have extended our analysis to include bri1brl1brl3 lines (Kang et al., 2017). These are dwarf mutants, yet able to respond to water stress in the dark with reduced hypocotyl and increased root growth (Figure panel former 5c replaced new Fig. 3c, shown left). Note that the lines have a null bri1-116 allele and segregate (bri1-/+ brl1-/- brl3 -/-)quite clearly, as was verified by propagating seedlings on plate after the scan on day 10 (Supplementary Method S5).

***Minor comments:** *

*5. The authors separate conceptually growth tradeoffs in sensing, signaling, decision making and execution processes. A clearer explanation of the expected phenotypes from mutants in only decision making with and without stress would be interesting to add (page 8)? *

We have now moved up phya phyb cry1 cry2 quadruple photoreceptor mutant and write:

Results on page 9

“Perception mutants would fail to perceive light or water stress; a good example of this is the phya phyb cry1 cry2quadruple photoreceptor mutant, which had a severely impaired light response (Fig. S4d), but a “normal” response to water stress in the dark (Fig. S4e). In contrast, execution mutants may have aberrantly short hypocotyls or roots that are nonetheless capable of differentially (and significantly) increasing in length depending on the stress conditions. Decision mutants would differ from perception or execution mutants as they would clearly perceive the single stress factors yet fail to adequately adjust their hypocotyl/root ratios in response to a gradient of single or multiple stress conditions. Failure to adjust organ lengths would be seen as a non-significant response, or as a significant response but in the wrong direction as compared to the wild-type. We thus used organ lengths, the hypocotyl/root ratio and the significance of the responses as decision read outs. We specifically looked for mutants in which at least one organ exceeded wild-type length under darkW.“

Later in the results on page 11 and in the legend to Fig. 4 we pick up on this as follows:

“For bin2-1, the response to water stress in the dark was severely impaired: the hypocotyl and root responses were non-significant …bin2-3bil1bil2 mutants fit the above definition of decision mutants as they have a significant root response but in the wrong direction as compared to the wild-type, as denoted by red asterisks (Fig. 3e)…

Figure 4. … bin2-3bil1bil2 mutants qualified as decision mutants on 3 counts: (i) failure to adjust the hypocotyl/root ratio to darkW (the ratio for darkW is the same as for dark in panel c), (ii) low or non-significant P-value (see panel f below) and (iii) one organ (here the hypocotyl in panel a) exceeded wild-type length under darkW.”

Line 26 page 17: BR responses in the epidermis of the hypocotyl have been shown to be already sufficient to control hypocotyl growth (Savaldi-Goldstein et al 2007), showing that not all cells of the hypocotyl need to receive the signal (at least in the case of brassinosteroids) We have deleted the sentence because it is too speculative. However, the issue of different tissue layers is now mentioned in the perspective on page 18, as follows:

“3D imaging will be required to assess the impact of abiotic stress and/or of BR signalling on different cell files or tissue layers in the root (see Hacham et al., 2011; Fridman et al., 2014; Fridman et al., 2021; Graeff et al., 2021). .”

Because of the importance of distinguishing between different cell files and cell layers, we have now removed the confocal images of BRI1-GFP under the different environmental conditions (formerly Fig. 7a); this needs to be extended to a 3D analysis, which is not within the scope of this manuscript.

1. *Page 6 Line 11: In the volcano blots the mean RQ ratio is shown in Fig. 6c and 6f. *

We thank the reviewer for pointing this out, we had accidentally written median RQratio, this has been rectified in the results text.

*Some parts of the ms could be shortened and the amount of Fig. could be reduced. Fig. 1-3 could be merged as one figure showing the optimal conditions to analyze tradeoffs in shoot vs. root growth and all the conditions not suitable could be supplementary figures. *

We concur with the reviewer and have merged the first three figures as suggested. Reviewer #2 has also requested that we slim the manuscript and all reviewers request that we strengthen our conclusions on the brassinosteroid pathway mutants. To reduce the number of figure panels, we have removed the analysis of all mutants that are not in the BR pathway, with the exception of the quadruple photoreceptor mutant in Fig. S4d,e and plethora mutants in Fig. S15. Nonetheless, incorporating the new data generated in response to reviewer comments leaves us with 7 main and 16 supplementary figures.

*In the ms several experiments are described as 'screen' this is confusing with the forward genetic screen that was performed. *

This is indeed ambiguous. We now use the terms “single versus multiple stress conditions/additive stress/conflict-of-interest scenario ” versus “forward genetic screen”.

*Reviewer #3 (Significance (Required)): *

* Mechanisms how growth trade-offs between multiple stresses are controlled are highly interesting. Growth vs. biotic stress tradeoffs have already been investigated and were found to be interdependent with light (Leone et al. 2014; Campos et al 2016; Fernandez-Milmanda et al. 2020) and hormone signaling (Lozano-Duran and Zifpel et al., 2016 and Ortiz-Morea et al 2020; van Butselaar and van den Ackerveken, 2020). Less is known about growth tradeoffs between two abiotic stress responses (Bechtold and Field, 2018; Hayes et al., 2019). The separation of root meristem growth and cell expansion in the hypocotyl is interesting. Whether the two directional root-to-shoot and shoot-to-root signals are independent or whether they may employ the same mechanism with a different output remains open. Different sensitivities of organs and cell types to BRs have for example been reported (Müssing et al. 2003 and Fridman et al. 2014). The findings that BIN2 most likely act to integrate multiple signals is in line with the reported roles of BIN2 to crosstalk with several pathways (reviewed by Nolan et al. 2020). In my point of view, it remains to be strengthened if this is through 'decision making' and not through signaling and execution. I think if the authors carefully separate the defects in bin2 this work will be interesting to many plant biologists. * We thank the reviewer for highlighting references we had not referred to in the former draft. The references pertaining to the growth versus defense trade-off are now included in the introduction (page 3) and the ones on abiotic stress factors in the Discussion on page 18:

“In addition to its role in light and drought responses… BIN2 has been implicated in regulating hypocotyl elongation in response to far-red light and salt stress (Hayes et al., 2019). Studies on responses to abiotic stress factors have typically addressed growth arrest or tradeoffs between growth and acclimation (Bechtold and Field, 2018). Indeed, root growth is inhibited by, for example, phosphate deprivation or salt stress (Balzergue et al., 2017; West et al., 2004). Recent efforts have addressed strategies for engineering drought resistant or tolerant plants that do not negatively impact growth (Fàbregas et al., 2018; Yang et al., 2019). In contrast to other studies, here we look at two abiotic stress factors that promote organ growth. Indeed, hypocotyl growth is promoted by darkness or low light and primary root growth by water deficit in this study.”

We emphasize the above point about decision making in the discussion. In the in the introduction and early on in the results we introduce conceptual frameworks for decision making. Yet after a forward genetic screen and mutant characterization, we revise this in the Discussion on page 18 as follows:

“In the judgement and decision-making model for plant behaviour put forth by Karban and Orrock (2018), signal integration might be considered integral to judgement. ….Whether judgement and decision making can be distinguished from each other empirically remains unclear. As BR signalling regulates cell anisotropy and growth rates in the hypocotyl and root apical meristem, it may play a role not only in signal integration but also in the execution of decisions (or in an implementation of the action; González-García et al., 2011; Vilarrasa-Blasi et al., 2014). Thus, this study does not enable us to empirically distinguish between decision making on the one hand and signalling and execution on the other.”

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Understanding decision making during growth tradeoffs is a very exciting goal for biologists. The ms by Kalbfuß et al. reports a role for BIN2 in signal integration during decision-making to balance root vs. hypocotyl growth. First the authors established a system to investigate differential growth decisions in arabidopsis seedlings. In this system they show that light signaling competes with resources for water stress adaptation, as the combination of dark and water stress promotes root growth at the expense of hypocotyl growth. In a forward genetic screen with the aim to identify decision mutants, a semidominant bin2 allele (identical to bin2-1) was identified that fails in controlling growth tradeoffs. Since mutants of the canonical BR signaling pathway through BZR1/BES1 and mutants of other known BIN2 interactors were not giving comparable phenotypes to bin2, the authors conclude that BIN2 likely integrates multiple signals to control root vs. shoot growth. Finally, the authors show that light vs. water stress are regulated as two independent modules.

Major comments:

My major concern is that in the search of a decision mutant the authors performed the first screening not under 'a conflict of interest' scenario but under dark conditions. Can the authors explain the reasons behind this more clearly?

Related to above, the role of the BR pathway in etiolation has been well established with the prominent constitutive photomorphogenesis phenotypes of BR related mutants; since both bin2 alleles are impaired in light responses this mutant may behave in dark vs darkW, like a wildtype plant in light vs. lightW (maybe also partially as shown in SFig. 5a). However, the authors show that the growth tradeoff was not evident under light conditions (Fig 2). I think to conclude that bin2 is a decision mutant it requires more evidence to excluded that a defect in efficient sensing and signaling of dark conditions are not the primary source of the 'confused' phenotype. In addition to the phenotype in SFig. 5a where light responses are attenuated in B1 when compared to Wt, a comparison of gene expression analysis of some established light regulated genes could help to show that bin2 is able to efficiently sense the absence of light.

Cells that fail to elongate in the dark may cannot - or only to a limited extent - reduce further their cell length in the darkW conditions. Since BR-mutants fail to expand hypocotyl cells in the dark, an analysis of the hypocotyl epidermis cell length in bin2 mutants compared to wt in light vs dark vs darkW (as in Fig. 8c) could be a feasible experiment to exclude that the general BR-related cell elongation defects led to the confused phenotypes of this mutant.

The experiments with the BR-deficient and signaling mutant and the bypass mutant may suggest that BR hormone is playing a relative minor role in the 'decision activity' of BIN2. bri1-6 was described to respond like wildtype (page10 line 6-8). Since this seems because of normal root responses in dark vs. darkW (Fig. 5) it could also be caused by the role of BRL1 and BRL3 in root drought responses (Fabregas et al., 2018). To verify if functional BRL1 and BRL3 in bri1-6 could cause the root response to water stress an additional experiment with bri1,brl1,brl3 triple mutant is required; In my opinion this is very important to state if the BR input is at all required for BIN2 signal integration or not.

Minor comments:

The authors separate conceptually growth tradeoffs in sensing, signaling, decision making and execution processes. A clearer explanation of the expected phenotypes from mutants in only decision making with and without stress would be interesting to add (page 8)? Line 26 page 17: BR responses in the epidermis of the hypocotyl have been shown to be already sufficient to control hypocotyl growth (Savaldi-Goldstein et al 2007), showing that not all cells of the hypocotyl need to receive the signal (at least in the case of brassinosteroids)

Page 6 Line 11: In the volcano blots the mean RQ ratio is shown in Fig. 6c and 6f.

Some parts of the ms could be shortened and the amount of Fig. could be reduced. Fig. 1-3 could be merged as one figure showing the optimal conditions to analyze tradeoffs in shoot vs. root growth and all the conditions not suitable could be supplementary figures.

In the ms several experiments are described as 'screen' this is confusing with the forward genetic screen that was performed.

Some parts of the ms could be shortened and the amount of Fig. could be reduced. Fig. 1-3 could be merged as one figure showing the optimal conditions to analyze tradeoffs in shoot vs. root growth and all the conditions not suitable could be supplementary figures.

In the ms several experiments are described as 'screen' this is confusing with the forward genetic screen that was performed.

Significance

Mechanisms how growth trade-offs between multiple stresses are controlled are highly interesting. Growth vs. biotic stress tradeoffs have already been investigated and were found to be interdependent with light (Leone et al. 2014; Campos et al 2016; Fernandez-Milmanda et al. 2020) and hormone signaling (Lozano-Duran and Zifpel et al., 2016 and Ortiz-Morea et al 2020; van Butselaar and van den Ackerveken, 2020). Less is known about growth tradeoffs between two abiotic stress responses (Bechtold and Field, 2018; Hayes et al., 2019). The separation of root meristem growth and cell expansion in the hypocotyl is interesting. Whether the two directional root-to-shoot and shoot-to-root signals are independent or whether they may employ the same mechanism with a different output remains open. Different sensitivities of organs and cell types to BRs have for example been reported (Müssing et al 2003 and Fridman et al. 2014). The findings that BIN2 most likely act to integrate multiple signals is in line with the reported roles of BIN2 to crosstalk with several pathways (reviewed by Nolan et al. 2020). In my point of view, it remains to be strengthened if this is through 'decision making' and not through signaling and execution. I think if the authors carefully separate the defects in bin2 this work will be interesting to many plant biologists.

My expertise: plant development, signaling, brassinosteroids

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors did a lot of work to characterize the regulatory role of BIN2, which is known to be a key hub of BR signaling, in a new role as modulator of environmental changes on plant growth. Including changing light conditions and thereby influence of photosynthesis on overall growth, shoot dominance, and root growth adaptation upon water stress, root dominance, the authors aim to describe its regulatory role.

It is well known that shoot and root are communicating depending on environmental changes, and that both contribute in their own way to proper plant growth, and when resources are low or stress is compromising growth this has a big impact on above and under ground tissues all together. Furthermore, several so-called cellular hubs, as TOR or SnRK1 and others, are known to reorganize shoot vs root growth, by reconstructing manifold signaling cascades, and are themselves targeted by other signaling cascades.

A lot of signaling pathways act interwoven in the regulation between shoot and root, and the authors also investigated several key players of those that are well described. But, to understand and prove their integrative role higher order mutants between those pathways are missing. This of course will take time and will be not considered for this manuscript.

Nevertheless, following claims should be changed, when speaking about shoot versus root dominance. Most of the measurements were done of hypocotyls, in Fig4 clearly from shoots. I recommend to exchange shoot for hypocotyl when hypocotyls were examined to avoid to confuse the readers.

The authors have chosen SnRK2 (and should also indicate it in all Figures as SnRK2, to not confuse the readers with SnRK1), and implement ABA signaling in parallel to BR action, but this must be proven in higher order mutants of both pathways, at the moment the results are to preliminary to allow conclusions. When the authors are interested in shoot dominance/photosynthetic activity, why didn't they look on snrk1 mutants, which are known to regulate those processes. In Fig6 d the authors propose a sketch of the mechanism, but the data of this study don't show direct interaction of the pathways and as indicated in the figure text parts of the information are taken from other papers, I recommend to remove this sketch or shift it to the supplements.

To discriminate the role of downstream BR signaling events from other roles of BIN2, I suggest to complement the data with pharmacological experiments (eBL or bikini where appropriate), and if possible to implement phenotyping of OE lines. How many independent ko lines were tested, can the authors exclude that the BR independent phenotype indeed corresponds to BIN2 activity and not to a off target effect. I further recommend to exchange the pictures in Fig7a showing BRI1GFP to pictures showing fewer cells, but with higher resolution.

Regarding the implementation of photoreceptor mutants and the claim that photoreceptors are more abundant in shoot, I want to point out that the situation is more complex, as the root also reacts differently to light of different quality and quantity, with different responses in the meristem, by inhibiting cell proliferation, or in the elongation zone by triggering negative phototropism. this should be corrected in the text.

The data and methods are presented in a clear and sufficient way, as well as the statistical analysis.

Altogether, the hypothesis and work amount are worth to be recognized, but the manuscript also resembles partially more a review and I would suggest to shorten those parts in the manuscript, reduce the amount of described lines and focus strictly on the BR pathway, in response to the environmental changes. Before implementing photoreceptors and ABA/SnRK2 pathway into the story to either test higher order mutants between the signaling pathways of interest or come up with a pharmacological screen connecting the data. Therefore I suggest to reduce the amount of mutants investigated and focus on BIN2 action, implementing also a pharmacological screen to track a fluorescent tagged BIN2 upon the mentioned treatments. And if possible to add proteomics and phosphoproteomics to understand better what changes are undergoing in the bin2 mutant vs WT upon stress.

Significance

The significance for the field would be to define BIN2 as another cellular hub orchestrating plant growth and especially shoot/hypocotyl vs root growth, but some more directed studies must be done to proof this claim. The scientific interest in shoot-root communication and how their communication is orchestrated by sugar-phytohormone-exogenous signal crosstalk is currently growing. The study consists of very interesting descriptive insights of plant growth adaptation upon additive stress response, but the direct interaction of all investigated players is missing. A pharmacological approach combined with Proteomics and Phosphoproteomics could support the hypothesis.

The manuscripts refers to all relevant literature supporting the hypothesis, but as described in the previous section, there are studies published showing a more complex situation, especially when talking about light perception. In general, I recommend to slim the manuscript and thereby also the parts resembling a review with suggestive character and focus more on conclusions drawn from actual experiments.

My research interest and expertise includes sugar-auxin crosstalk upstream of root growth adaptation, BR-auxin crosstalk, and light signaling upstream of plant growth adaptation.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this manuscript, the authors explore tradeoffs between root and shoot growth of seedlings in response to variable light and water availability. They first establish a scenario in which dark grown seedlings are exposed to water deficit via PEG treatments, which leads to a higher root/shoot ratio. An EMS mutagenesis screen was then performed. Mutants with an altered root/shoot ratio were selected and then rescreened for differential root/shoot ratios when exposed to water stress. From this screen, the authors identified a mutant, B1, that contains a semi-dominant gain-of-function mutation in BIN2. It turns out that B1 is allelic to the previous reported bin2-1 mutant, encoding a kinase that functions as an important negative regulator of Brassinosteroid signaling. This prompted the authors to explore the phenotypes of various BR signaling mutants as well as mutants in known BIN2 substrates. The authors claim that bin2 mutants have "confused" phenotypes. They then go on to propose a model that states that hypocotyl growth is regulated by a decentralized response whereas root growth is driven primarily by the root apical meristem. While the study system and some of the findings in this manuscript are interesting, there are major flaws in the author's primary claims that I detail below.

1. The authors claim that bin2 has a "confused" phenotype, which they define as high variability in shoot versus root lengths along with a low degree of response to water limitation. bin2-1 is a semi-dominant gain-of-function mutant, which can only be propagated as a heterozygote (homozygous individuals are viable, but don't produce seeds). There is no mention in the manuscript about genotyping or selection of homozygous bin2-1 individuals for the phenotyping assays. Could the high variability observed in fact be caused by the authors looking at a segregating population of bin2-1?
2. The authors state that bin2 mutants had considerably more severe phenotypes than other BR biosynthesis, perception, or transcription factor mutants. This is like comparing apples to oranges, as the set of mutants they've examined consists of gain-of-function and partial loss-of-function alleles. Null alleles for BR biosynthesis (e.g. cpd, dwf4), perception (bri1brl1brl3 triple mutants) and transcription factors (bzr1bes1beh1-4 sextuple mutants) are described in the literature and would need to be tested before arriving at such a conclusion.
3. For most of the phenotyping experiments a "RQ ratio" is presented. This is the ratio adjustment of the mutant/ratio adjustment of WT. While this derived quantity is useful for interpretation, we're missing plots of the raw data, and particularly those that show the underlying distribution of data points.
4. Root growth involves both cell division in meristematic cells at the tip of the root and subsequent elongation as cells exit the meristem and begin to differentiate. The authors claim a nine-fold difference in CycB1,1:GUS in the root meristem in dark vs darkW, however their images show similar CycB1,1:GUS expression patterns. Furthermore, the meristems of darkW are actually smaller than dark, which would be unexpected if cell division was increased.
5. In addition, the authors claim that the longer root length in dark water stress was at least in part due to increased elongation (Fig. 7c). Elongation was only assessed by looking at the first elongating cell (~10-14um) and the differences found are on the order of magnitude of ~2um, but final cell size in Arabidopsis roots often reaches several hundred um. Therefore, a comparison of final cell size would be more appropriate.
6. Finally, the authors phenotype plt1/2 double mutants and show that they fail to elongate in response to water limitation. Their interpretation is that this supports a centralized control model for the root apical meristem. PLT1/2 are important determinants of meristem function and are necessary to maintain stem cell identity. Given the strong phenotype of plt1/2 double mutants it is not surprising that they are unable to elongate in response to this stimulus. This does not necessarily indicate that only the RAM controls root growth, but rather that functional stem cells are required for root growth, which also involves subsequent steps such as cell elongation.

Significance

While the study system and some of the findings in this manuscript are interesting, there are major flaws in the authors' primary claims.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2020-00527

Corresponding author(s): Iva M. Tolić

1. General Statements [optional]

We thank the reviewers for providing thoughtful and constructive feedback on our manuscript. Given that the reviewers proposed numerous experiments, and that at the time when we received the reviews, we acquired a STED superresolution microscope for the lab, we decided to perform all experiments using STED microscopy. This brought our paper to a higher level with unique image quality of human spindles. We used STED microscopy to repeat almost all the experiments from the original manuscript, as well as to perform new experiments, on cells immunostained for tubulin, with or without HAUS6/8 depletion. Because this resulted in much clearer visualization and more precise quantification of k-fibers and bridging fibers, we show the new STED images and the corresponding quantifications in the revised main figures (new Fig. 1, Fig. 2J,K, Fig. 3, Fig. 5), whereas the old confocal images and the related measurements from the original manuscript are largely moved to the Supplementary figures as supporting data.

In addition to STED imaging, as a key part of the revision we took a functional approach where we tested how augmin depletion and the perturbation of bridging microtubules affects chromosome segregation and mitotic fidelity, as suggested by Reviewer 3. These exciting new results expanded the significance of our study, and we decided to include them in new Fig. 2 and reorganize the manuscript accordingly.

Please note that due to the numerous experiments suggested by the reviewers and the optimization of the super-resolution microscope, along with covid-related interruptions and delays, this extensive revision has taken a year and a half, which we hope you will understand.

Insert here any general statements you wish to make about the goal of the study or about the reviews.

2. Point-by-point description of the revisions

We thank the reviewers for providing insightful and constructive comments on our manuscript. We have carefully considered each point and have revised the paper as documented below, with reviewer comments in black and our response in blue.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

In the manuscript "Augmin regulates kinetochore tension and spatial arrangement of spindle microtubules by nucleating bridging fibers", Manenica et al. explore the impact of augmin-dependent microtubule nucleation on formation of a subset of spindle microtubules that bridge sister kinetochore fibers and investigate how this could affect the spindle forces and architecture. Using RNAi- and CRISPR-Cas9- based loss-of-function experimental approach, the authors propose that the bridging fibers are nucleated by augmin and that removal of augmin impairs proper spindle architecture, interkinetochore tension and microtubule poleward flux, specifically via its effect on the bridging fibers. Overall, the study is well designed and the manuscript well written. Expanding the knowledge on augmin contribution to the spindle functions and better understanding of the roles of bridging fibers would be important and of interest to cell biologists studying mitosis. Although this manuscript clearly shows that augmin depletion impairs the formation of bridging fibers (and other microtubules), the specific contribution of the bridging fibers to the augmin-dependent spindle functions is less clear.

We thank the reviewer for this criticism. To address it, we have toned down the conclusions about the specific contribution of the bridging fibers throughout the revised manuscript.

**Major comments:**

1) Using cold treatment-induced microtubule destabilization, Zhu et al. (JCB 2008) showed that augmin depletion affected exclusively kinetochore microtubules. Since the bridging microtubules are usually not visible in the cold-treated spindles (due to being less stable/cold resistant compared to the k-fibers), it is unlikely that the observed effects were mainly associated with the bridging fibers. Thus, it would be important to further clarify the respective contribution of augmin to the formation of k-fibers and the bridging fibers. The cold-treatment experiment performed by Zhu et al. could be used in RPE1 and HeLa-PRC1-GFP cells to address the contribution of augmin nucleation to kinetochore- vs. bridging microtubules from another angle.

Because of the above mentioned results by Zhu et al. it is difficult to grasp how augmin depletion could have a bigger effect on the bridging fibers than on the k-fibers, as concluded from the Fig. 2C data. In fact, Fig. 2A clearly shows a strong effect on k-fibers in spindles where the bridging fibers are reduced/missing.

Also, Fig. 1 D and E suggest that HAUS8 siRNA exclusively affected the bridging fibers, leaving the k-fibers intact, which is again against the data reported in Zhu et al. 2008 and in contrast with the representing image shown in Fig. 1B. Even if the RNAi was less efficient compared to HAUS6 RNAi, as the authors proposed, this could still not explain the observed discrepancy.

We thank the reviewer for this comment. To better address the contribution of augmin to either bridging or kinetochore microtubule nucleation, we repeated a major part of the experiments by using STED super-resolution microscopy on cells immunostained for tubulin, with or without HAUS6/8 depletion. STED imaging enabled much clearer visualization of k-fibers and bridging fibers (Fig. 1 and Fig. 3A), and confirmed our initial result that augmin depletion has a larger effect on bridging fibers than on k-fibers (Fig. 3D,E). Importantly, the new results for HAUS6 siRNA and HAUS8 siRNA were similar, and showed that the lack of augmin affects k-fibers to a certain extent in both cases (Fig. 3D,E). The data from the original manuscript, obtained by confocal microscopy, are now shown in Supplementary Fig. S3.

To independently test the effect of augmin depletion on k-fibers, we also performed experiments with cold treatment as suggested, imaged the cells by STED microscopy, and analyzed the images as in Zhu et al. (Fig. 3F,G). These experiments were done on RPE1 cells that stably express CENP-A-GFP. Cold treatment in HeLa-PRC1-GFP cells was no longer needed, as STED imaging clearly showed the absence of bridging fibers in cold treated cells. The new results are described on page 12:

“Quantification of STED images further revealed that HAUS6 depletion resulted in 68 ± 8% reduction of the bridging fiber signal intensity and 24 ± 6% reduction of the k-fiber signal intensity, with similar results obtained by HAUS8 depletion (Fig. 3D-E). These data indicate that augmin depletion affects not only k-fibers, but even more so bridging fibers. The contribution of augmin to the nucleation of k-fibers was independently tested by measuring their intensity in spindles exposed to cold treatment in which bridging fibers are removed (Fig. 3F). HAUS6 depletion resulted in a 37 ± 5% reduction of the k-fibers (Fig. 3G), which is consistent with a previous study (Zhu et al., 2008) and comparable to values under non-cold conditions.”

2) The authors showed that kinetochore pairs in the outer parts of Augmin-depleted spindles have larger inter-kinetochore distance compared to those in the inner parts of spindles. They indirectly related this to a predominant presence of the bridging fibers in the outer parts, concluding that augmin regulates inter-kinetochore tension via nucleation of the bridging fibers. A more direct way would be to show the eventual positive correlation between the inter-kinetochore distance and the bridging- and k- fibers intensity. Also, it would be nice to include the quantifications and correlation data for inter-kinetochore distance, distance from the spindle axis and the bridging- and k- fibers intensities for the control cells too.

We analyzed the new data and included the correlations in the altered manuscript. We explained the correlation data for the interkinetochore distance and the distance from the spindle axis as follows: “… we noticed that the interkinetochore distance was smaller in the inner part of the spindle in augmin-depleted cells (Fig. 5A-D, Supplementary Fig. S5B), where bridging fibers were most severely impaired (Fig. 3H and 4A). This was not the case in control cells, which showed no difference in interkinetochore distance between the inner and the outer part of the spindle (Fig. 5D, Supplementary Fig. S5B).”

We also included the correlation data for the interkinetochore distance and the bridging and k-fibers intensity: “… we found that although the interkinetochore distance correlated both with bridging and k-fiber intensity after augmin depletion, the correlation with bridging fiber intensity was stronger (Supplementary Fig. S5D-E). Such correlations were absent in control cells (Supplementary Fig. S5D-E).”

3) It is stated in the manuscript that the k-fibers without bridging fibers have shorter contour length compared to the k-fibers with bridging fibers, and that the curvature of k-fibers lacking the bridging fibers is drastically reduced. However, the data in Figure 5D and Table 1 show a slight effect on the contour length of the k-fibers lacking the bridging fibers compared to the ones containing the bridging fibers only in RPE1 siHAUS8 cells, while this effect seems to be missing in RPE1 HAUS8 KO cells, as well as in siHAUS6 in RPE1 and HeLa cells.

Fig. 2 shows that the kinetochore pairs without the bridging fibers are located closer to the spindle axis. Thus, it is not clear whether the effect on curvature observed in the augmin depleted cells is independent of the position of kinetochore pairs within the spindle, as the spindle axis-proximal pairs would anyway have a bigger radius compared to the more distant ones.

As these analyses were previously performed on bundles stained with SiR-tubulin and using confocal microscopy, we have now determined their curvature on spindles immunostained for tubulin and imaged by STED microscopy, where the shape of these bundles can be determined more precisely, in control and HAUS6 depleted cells. In the revised manuscript, only those spindles were taken for further analysis (Supplementary Fig. S3I-K). We revised the text as follows: “Whereas the bundles without kinetochores in HAUS6 siRNA-treated cells had a significantly longer contour when compared to all other bundle types (Supplementary Fig. S3J), k-fibers without bridging fibers in augmin-depleted cells had a significantly larger radius of curvature than any of the other bundle types in augmin-depleted or control cells (Supplementary Fig. S3K). Taken together, the outer interpolar bundles without associated kinetochores are excessively long and make the spindle wider, whereas k-fibers lacking a bridging fiber are overly straight, ultimately resulting in a diamond-like shape of the spindle.”

As for Fig. 2, in all experiments regarding shape, we only analyzed the outermost bundles, so the potential effect of the position of kinetochore pairs within the spindle can be excluded. We explained that in the Methods section and highlighted it in the caption of the Supplementary Fig. 3I: “In control cells, only the outermost bundle was tracked. In HAUS6 siRNA treated cells, three different groups of outermost bundles were tracked: bundles with visible bridging fibers, bundles with no visible bridging fibers and curved bundles extending far from the metaphase plate” and “Examples of each bundle type are shown in insets. From left to right: the outermost bundle in control cells, the outermost bundle with a bridging fiber, the outermost bundle without a bridging fiber and the outermost bundle without kinetochores in HAUS6-depleted cells”, respectively.

4) The authors reported that augmin depletion impairs microtubule poleward flux and conclude that this happens exclusively due to the perturbation of bridging fibers. While the results from this and other studies clearly show that augmin depletion perturbs spindle microtubules in general, it is not clear whether this had a stronger effect on the bridging microtubules (see the comments in point 1). Thus, the impact of augmin depletion on kinetochore microtubules or other antiparallel microtubules within the spindle (e.g. the ones recently shown in O'Toole et al., MBoC 2020) cannot be ruled out as a potential cause of the impaired microtubule flux. Also, Steblyanko et al. (EMBO J, 2020) showed that PRC1 depletion had no effect on microtubule poleward flux in metaphase cells. Since it has been previously shown by the authors of this manuscript that PRC1 depletion disrupts the formation of bridging fibers, it is unlikely that the bridging fibers are the main cause of the augmin depletion-mediated effect on the microtubule flux.

We modified the text on poleward flux to include the contribution of both bridging and k-fibers. We also performed new experiments on U2OS cells and included references to the new work from our lab (Risteski et al., 2021), which was able to distinguish between the effect of augmin depletion on bridging and k-fibers. We also included a comment on PRC1 depletion: “Recent speckle microscopy experiments in RPE1 cells, which were able to separate the effect of augmin on poleward flux of bridging and k-fibers, revealed that both k-fibers and the remaining bridging fibers were significantly slowed down (Risteski et al., 2021 Preprint). Bridging fibers fluxed faster than k-fibers in control and augmin-depleted cells (Risteski et al., 2021 Preprint), supporting the model in which poleward flux is largely driven by sliding apart of antiparallel microtubules (Brust-Mascher et al., 2009; Mitchison, 2005; Miyamoto et al., 2004). We propose that augmin depletion results in slower flux of bridging fibers because the remaining bridging microtubules are likely nucleated at the poles, where microtubule depolymerization mechanisms might curb poleward flux speed (Ganem et al., 2005). In contrast, PRC1 depletion does not affect the flux (Risteski et al., 2021 Preprint; Steblyanko et al., 2020) even though it reduces bridging fibers (Kajtez et al., 2016; Polak et al., 2017), possibly because the remaining bridging microtubules are generated away from the poles via augmin and can thus flux freely.”

Minor comments:

1) Introduction: chromatin- and kinetochore- mediated generation of spindle microtubules are ignored when describing the origins of spindle microtubules in human somatic cells.

We included the chromatin- and kinetochore-mediated generation of spindle microtubules in the Introduction. We revised the text as follows: “Spindle microtubules in human somatic cells are generated by several nucleation mechanisms, including centrosome-dependent and augmin-dependent nucleation (Kirschner and Mitchison, 1986; Pavin and Tolić, 2016; Petry, 2016; Prosser and Pelletier, 2017; Wu et al., 2008; Zhu et al., 2008), with an addition of chromatin- and kinetochore-dependent nucleation as a third mechanism that contributes to the directional formation of k-fibers (Maiato et al., 2004; Sikirzhytski et al., 2018; Tulu et al., 2006).”

2) The authors proposed less efficient HAUS8 depletion as a potential reason of discrepancy between the siHAUS6 and siHAUS8 results. This should be shown by Western blot, like it is presented for the RNAi efficiency of siHAUS6.

We agree with the reviewer that it would be best to include Western blot for the RNAi efficiency of siHAUS8. However, as we explained in the Methods section, commercially available HAUS8 antibodies resulted in no detectable bands in our hands, regardless of the modifications in the Western blot protocol. We explained this in Methods section, as follows: “Rabbit polyclonal HAUS8 antibody (diluted 1:1000, PA5-21331, Invitrogen and NBP2-42849, Novus Biologicals) resulted in no detectable bands under these conditions”. For this reason, we performed immunocytochemistry to determine the efficiency of siHAUS8. Discrepancy was now also addressed as a part of our new STED analysis, where depletion of HAUS6 and HAUS8 produced the same results.

3) The measurements of total PRC1 intensities are mentioned in the manuscript text, but not shown in the figures.

PRC1 measurements are now performed on both RPE1 and HeLa cells with corresponding graphs shown in Fig. 4C and Supplementary Fig. S4C.

4) Supplementary Videos 3 and 4 are wrongly annotated as Supplementary Videos 1 and 2 in the text.

As we have a new set of videos, this is no longer applicable.

5) Given the spindle length phenotypes are opposite in HeLa and RPE1 cells, in order to be consistent with the other experiments it would be better to perform the PRC1 measurements in RPE1 cells (e.g. using the anti-PRC1 antibody as shown in Supplementary Fig. 3B).

We have now performed size measurements in all three cell lines: RPE1 cells stably expressing CENP-A-GFP and Centrin1-GFP, RPE1 cells stably expressing PRC1-GFP and HeLa cells stably expressing PRC1-GFP treated with MG-132. These results are now shown in Supplementary Fig. S4J-K. The phenotypes remained the same as in the original experiments. We revised the text to better explain the observed differences as follows: “While the spindles in RPE1 cells shortened following augmin depletion, those in HeLa cells were longer (Supplementary Fig. S4J), consistent with previous observations on Drosophila S2 cells and Xenopus egg extracts (Goshima et al., 2007; Petry et al., 2011). This difference in spindle length might be due to the overlaps remaining the same length after augmin depletion in RPE1 cells, while being longer and thereby able to push the spindle poles further apart in HeLa cells (Supplementary Fig. S4K).”

6) Why are the microtubule flux rates for RPE1-PA-GFP-α-tubulin cells measured in this study largely different than the rates reported for the same cell line in Dudka et al., Nat Comms 2018 and Dudka et al., Curr Biol 2019? In order to better understand this difference and strengthen the microtubule flux data, it would be helpful to increase the experimental numbers to match the ones used in the mentioned studies.

We performed photoactivation experiments on a higher number of U2OS cells stably expressing CENP-A GFP, mCherry-tubulin and PA-tubulin (N = 30 measured photoactivation spots in 30 control and HAUS6-depleted cells, see Supplementary Fig. S3L-M). U2OS cells with labelled kinetochores and tubulin were used to exclude the potential effects of SiR-tubulin on poleward flux, as well as to better determine the position of the metaphase plate. The results in control cells are comparable to the poleward flux measured in the same cell line (Steblyanko et al., 2020).

7) The number of cells used per each experiment should be clearly stated.

In all experiments included in the main figures, we have now performed 3 independent experiments with at least 10 cells each. The numbers are also clearly stated in the captions of figures for all experiments.

Reviewer #1 (Significance (Required)):

This study expands the analysis of augmin contribution to the spindle functions and focuses on its role in formation of the bridging fibers, which is of interest to cell biologists studying mitosis. It clearly shows that in addition to its effect on the k-fibers, augmin depletion also impairs the formation of bridging fibers. However, the exact contribution of the bridging fibers to the spindle functions affected by augmin depletion remains unclear.

We thank the reviewer for the thoughtful comments and hope that our new experiments clarified the contribution of the bridging fibers to the augmin-dependent spindle functions.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

**Summary:**

The authors found that the microtubules in the bridging fibres of the mitotic spindle in a human cell line are predominantly supplied via augmin-dependent nucleation. On the other hand, the contribution of augmin to kinetochore fibre formation is ~40%. Augmin-depleted cells showed reduced inter-kinetochore tension and slower poleward flux of spindle microtubules, suggesting that bridging fibres play a role in these events. This study expands our knowledge on the role of augmin and augmin-mediated microtubules in animal somatic cells.

**Major comments:**

*-Are the key conclusions convincing?*

Yes.

*-Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?*

In the current manuscript, the slower flux is attributed solely to the lack of bridging fibres in the augmin-depleted cells. This is an overinterpretation, as the augmin's role in the spindle is not limited to generating bridging fibres.

We agree with the reviewer and modified this part in the Results section (part of Supplementary Fig. S3) to include the contribution of both bridging and k-fibers to poleward flux. We also included references to the new work from our lab (Risteski et al., 2021), which was able to distinguish between the effect on bridging and k-fibers: “Recent speckle microscopy experiments in RPE1 cells, which were able to separate the effect of augmin on poleward flux of bridging and k-fibers, revealed that both k-fibers and the remaining bridging fibers were significantly slowed down (Risteski et al., 2021 Preprint). Bridging fibers fluxed faster than k-fibers in control and augmin-depleted cells (Risteski et al., 2021 Preprint), supporting the model in which poleward flux is largely driven by sliding apart of antiparallel microtubules (Brust-Mascher et al., 2009; Mitchison, 2005; Miyamoto et al., 2004). We propose that augmin depletion results in slower flux of bridging fibers because the remaining bridging microtubules are likely nucleated at the poles, where microtubule depolymerization mechanisms might curb poleward flux speed (Ganem et al., 2005). In contrast, PRC1 depletion does not affect the flux (Risteski et al., 2021 Preprint; Steblyanko et al., 2020) even though it reduces bridging fibers (Kajtez et al., 2016; Polak et al., 2017), possibly because the remaining bridging microtubules are generated away from the poles via augmin and can thus flux freely.”

*-Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.*

No.

*-Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.*

N/A

*-Are the data and the methods presented in such a way that they can be reproduced?*

Yes.

*-Are the experiments adequately replicated and statistical analysis adequate?*

Yes.

**Minor comments:**

*-Specific experimental issues that are easily addressable.*

None.

*-Are prior studies referenced appropriately?*

Yes.

*-Are the text and figures clear and accurate?*

1) Page 15: "To determine the curvature of the bundles, we ..... with all other bundles types (Fig. 5E)." - I could not understand this sentence well, and would like to ask for a revision.

The text has now been changed to: “To gain insight into the contribution of each of these functionally distinct microtubule bundles to the maintenance of spindle geometry, we traced the outermost bundles in HAUS6 siRNA treated RPE1 cells imaged using STED microscopy and fitted a circle to the bundle outline (Supplementary Fig. S3I, see Methods)”.

2) The following words may be too strong:

Page 20: whereas k-fiber microtubules are "mainly" nucleated in an augmin-independent manner (could 61% contribution be called "mainly?").

We revised this sentence on page 24 as follows: “K-fibers were also thinner, though to a lesser extent, indicating that they are largely nucleated in an augmin-independent manner, at the centrosome or kinetochores and chromosomes.”

Page 21, bottom: "demonstrates".

As we changed this section of the manuscript, this is no longer applicable.

*-Do you have suggestions that would help the authors improve the presentation of their data and conclusions?*

No.

Reviewer #2 (Significance (Required)):

*-Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.*

The presence of bridging fibres has been recognised for decades; however, until recently, little attention has been paid to this structure from a mechanistic and functional point of view. The Tolic lab has been shedding light on this structure for the past several years. The current study represents another step forward in the research of the origin and function of bridging fibres.

*-Place the work in the context of the existing literature (provide references, where appropriate).*

Augmin's critical contribution to microtubule nucleation in the human somatic spindle has been well documented, as cited by the authors. The current study is the first to show that augmin also contributes to bridging fibres. The >70% contribution may be more than expected, given that centrosomal microtubules frequently reach the spindle midzone.

Reduced inter-kinetochore tension has also been documented, but previous studies attributed this exclusively to reduced number of kinetochore microtubules. The current study has revised this view.

*-State what audience might be interested in and influenced by the reported findings.*

Spindle researchers.

*-Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.*

This review is written by a researcher who is familiar with the literature of the mitotic spindle.

We thank the reviewer for an accurate summary of our work and perceptive comments.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In this study Manenica et study how the presence of the augmin complex affects the overall spindle architecture and the different types of spindle microtubules. The authors propose that depletion of augmin affects particularly bridging microtubules, leading to their disappearance on sister-kinetochores located in the central part of the metaphase plate.

Overall the manuscript is well written, clear and supported by excellent explanatory schemes. The main conclusion of the manuscript, i.e. that augmin plays an essential role in the formation of bridging microtubules is generally well supported by the data. A number of other conclusions, however, are less well supported by the data and would benefit from a number of additional experiments, repetitions or analysis. Specifically:

1. Throughout all the figures the authors use a t-test, which is fine when comparing two conditions, but not for multiple experimental conditions. The authors should instead use an ANOVA test or apply a Bonferroni correction. This can strongly affect the significance of some of the reported results.

We agree and have performed either ANOVA with post-hoc Tukey test or Mann-Whitney U-test instead of t-test where appropriate throughout the whole manuscript. The statistical analyses that were used are clearly stated in the captions of the figures.

Another general concern is that the authors rely throughout the manuscript on live cell imaging data from few cells (5-10). Live cell imaging data has the advantage to avoid fixation artifacts, but the low sample size is a major concern, as for every experiment the authors rely on 10 cells (and for inter-kinetochore distances on 5) in three independent experiments overall. This means that two our of three of those independent experiments are based on 3 cells only, which is too low, given that siRNA depletions are known to be variable in their efficiencies. With such low number of cells, there is always the danger of an unconscious selection bias, which can skew a result. Just to take an example the spindle length, structure and density for HAUS-8 depleted RPE1 cells looks very different in the examples show in Figure 1B, 2A, or 5B.It is therefore essential to work with a higher sample size, at minimum 10 cells per independent experiment.

This is a valid critique, which we addressed by performing 3 independent experiments with at least 10 cells each for all of our new analyses included in the main figures.

Throughout all experiments the authors use 100nm Sir-Tubulin, which in our hands already leads to substantial changes in microtubule dynamics, as it stabilizes spindle microtubules. I understand why the authors did this, as they wanted to also stain for weak bridging fibers, but tt would be important to validate some of the obtained results with an independent approach, for example fixed-cell imaging and tubulin staining, to rule out artifacts introduced by SiR-tubulin.

We thank the reviewer for this suggestion. To validate our results, we performed tubulin immunostaining, as suggested. Moreover, we imaged the immunostained cells by using super-resolution STED microscopy and included these results in the main figures (Fig. 1, Fig. 2J and K, Fig. 3, Fig. 5). The data obtained from cells stained with SiR-tubulin and imaged using live-cell confocal microscopy are now shown in Supplementary figures.

Figure 1: Given that the authors later report that augmin affects more strongly bridging fibers in the central part of the spindle, how were the values in terms of microtubule densities obtained in the experiments in Figure 1: only on the outer microtubules, or overall in the spindle?

Values in Figure 1 (now Figure 3) were obtained overall in the spindle. We described the selection in the text as follows: “We measured tubulin signal intensity of randomly selected bridging (Ib) and k-fibers (Ik) which had no other microtubules in their immediate neighborhood…”

Figure 2: the authors conclude that depletion of augmin has a much stronger effect on the bridging fibers located in the central part of the spindle. This is a very interesting result, but it begs the question as to the origin of this difference. If the authors analyze in control cells the inter-kinetochore distances and the density of the bridging fibers of the kinetochores located in the central part of the metaphase plate vs those located at the outer part of the plate, do they already see a difference? In other words, is the effect of augmin due to already weaker bridging fibers in the central part of the spindle, or is the depletion effect indeed specific for those bridging fibers located in the middle. This analysis should be possible with the existing data (+ a higher sample size)

This was now analyzed in the cells imaged using STED microscopy with a higher sample size. From our new data, it seems that the depletion effect is indeed specific for bridging fibers located in the middle as there was no significant difference between the interkinetochore distance in the inner and the outer part of the spindles in control cells (Fig. 5D and Supplementary Fig. S5B). The same trend can also be seen for bridging fiber density (Fig. 3H). We modified the text as follows: “However, we noticed that the interkinetochore distance was smaller in the inner part of the spindle in augmin-depleted cells (Fig. 5A-D, Supplementary Fig. S5B), where bridging fibers were most severely impaired (Fig. 3H and 4A). This was not the case in control cells, which showed no difference in interkinetochore distance between the inner and the outer part of the spindle (Fig. 5D, Supplementary Fig. S5B).”

Figure 4: the authors study spindle width, length and diameter of the metaphase plate in a small number of cells (10). One concern is that these values might change as cells progress from late prometaphase to anaphase onset (metaphase plate width decreases for example). Given the low number of cells the authors do not know if they are comparing cells at similar mitotic times. To circumvent this issues, they could: either arrest the cells with MG132 for 1 hour, to obtain an end-point, or record these different values as cells progress through mitosis and thus be able to compare similar conditions.

We agree with this suggestion, and we performed new experiments by arresting the cells with MG-132: “… in HeLa (Kajtez et al., 2016) and RPE1 (Asthana et al., 2021) cells stably expressing PRC1-GFP with and without MG-132 treatment (Fig. 4A-B, Supplementary Fig. S4A).” We measured spindle width, length and diameter of the metaphase plate in arrested RPE1 cells stably expressing CENP-A-GFP and Centrin1-GFP, RPE1 cells stably expressing PRC1-GFP, and HeLa cells stably expressing PRC1-GFP. We treated the cells with MG-132 for 30 minutes, as this was in our hands enough to arrest the cells, without causing other changes, e.g., problems with spindle orientation that occur after 1 hour of treatment. The results are now part of the Supplementary Fig. S4 and are obtained from three independent experiments with at least 10 cells per experiment.

In the discussion the authors conclude that the longer bundles and the reduction in microtubule poleward flux is due to the absence of bridging microtubules. This is an over-interpretation as augmin could in theory affect these parameters independently of the bridging microtubules, longer bundles could be generally due to the reduced number of microtubules in the k-fibers and the bridging microtubules. A better control would be to affect bridging microtubules with an independent tool, such as PRC1 depletion, and to measure these paramenters in the same RPE1 cell line, since differences can arise from cell line to cell line as the authors also document in their study (for example spindle length in Figure 4).

We modified the Discussion based on new results, so these statements are now in the Results section. For the long, curved bundles, we modified the sentence as follows: “These bundles likely arose either due to PRC1 crosslinking excessively long astral microtubules that were now able to reach the spindle midzone or due to PRC1 activity combined with the excess of free tubulin present as a consequence of less tubulin being incorporated in bridging and k-fibers.”

Regarding the reduced poleward flux following augmin depletion, we revised the text as follows: “Recent speckle microscopy experiments in RPE1 cells, which were able to separate the effect of augmin on poleward flux of bridging and k-fibers, revealed that both k-fibers and the remaining bridging fibers were significantly slowed down (Risteski et al., 2021 Preprint). Bridging fibers fluxed faster than k-fibers in control and augmin-depleted cells (Risteski et al., 2021 Preprint), supporting the model in which poleward flux is largely driven by sliding apart of antiparallel microtubules (Brust-Mascher et al., 2009; Mitchison, 2005; Miyamoto et al., 2004). We propose that augmin depletion results in slower flux of bridging fibers because the remaining bridging microtubules are likely nucleated at the poles, where microtubule depolymerization mechanisms might curb poleward flux speed (Ganem et al., 2005). In contrast, PRC1 depletion does not affect the flux (Risteski et al., 2021 Preprint; Steblyanko et al., 2020) even though it reduces bridging fibers (Kajtez et al., 2016; Polak et al., 2017), possibly because the remaining bridging microtubules are generated away from the poles via augmin and can thus flux freely.”

**Minor comment:**

-the reported flux rate for control-depleted cells is substantially higher than the flux rates normally reported for human cells. This could be due to the experimental conditions (slight changes in temperature), but at minimum the authors should comment on this.

We performed photoactivation experiments on a higher number of U2OS cells stably expressing CENP-A GFP, mCherry-tubulin and PA-tubulin (N = 30 measured photoactivation spots in 30 control and HAUS6-depleted cells, see Supplementary Fig. S3L-M). U2OS cells with labelled kinetochores and tubulin were used to exclude the potential effects of SiR-tubulin on poleward flux, as well as to better determine the position of the metaphase plate. The results in control cells are comparable to the poleward flux measured in the same cell line (Steblyanko et al., 2020).

Reviewer #3 (Significance (Required)):

The significance of the study is that the authors performed a detailed description of the effects of augmin depletion on the spindle architecture, in particular bridging fibers. Nevertheless, many of the reported results are already known (and as cited by the authors): the reduction in inter-kinetochore distances or the change in spindle architecture. The 3 main novel results, is the fact that augmin affects more bridging microtubules, particularly in the central part of the spindle, and that it also affect poleward microtubule flux, which limits the impact of this study to a specialized mitotic spindle audience. Nevertheless, if the authors address the reviewers concerns, this could be a nice, descriptive study for the mitotic field.

One way to expand the significance of this study would be to test how augmin depletion and the lack of bridging microtubules in the central part of the metaphase plate affects chromosome segregation. Does the specific absence of bridges in this part lead to more lagging chromosomes, chromosome segregation errors, or micronuclei amongst sister chromatids located in the central part of the spindle? Is there a differential anaphase A speed for those kinetochore vs those at the periphery that still are associated to bridging fibers? Such a functional approach could allow to highlight the most interesting aspect of this study, the spatial difference in the effects of augmin depletion. Such experiments would, however, not be part of a revision, but rather a substantial enhancement of the present study.

Patrick Meraldi

This is a great idea! We performed new experiments to study lagging chromosomes and indeed found that they were more often found in the inner part of the spindle in HAUS6-depleted than in control cells, which is likely due to the specific impairment of bridging fibers in that area. We also found that lagging chromosomes typically had a lower interkinetochore distance and a higher kinetochore tilt just before the onset of anaphase, which is a signature of perturbed bridging fibers. We dedicated an entire new section on pages 6-11 and a new Fig. 2 to these exciting new results.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

In this study Manenica et study how the presence of the augmin complex affects the overall spindle architecture and the different types of spindle microtubules. The authors propose that depletion of augmin affects particularly bridging microtubules, leading to their disappearance on sister-kinetochores located in the central part of the metaphase plate.

Overall the manuscript is well written, clear and supported by excellent explanatory schemes. The main conclusion of the manuscript, i.e. that augmin plays an essential role in the formation of bridging microtubules is generally well supported by the data. A number of other conclusions, however, are less well supported by the data and would benefit from a number of additional experiments, repetitions or analysis. Specifically:

1.Throughout all the figures the authors use a t-test, which is fine when comparing two conditions, but not for multiple experimental conditions. The authors should instead use an ANOVA test or apply a Bonferroni correction. This can strongly affect the significance of some of the reported results

2.Another general concern is that the authors rely throughout the manuscript on live cell imaging data from few cells (5-10). Live cell imaging data has the advantage to avoid fixation artifacts, but the low sample size is a major concern, as for every experiment the authors rely on 10 cells (and for inter-kinetochore distances on 5) in three independent experiments overall. This means that two our of three of those independent experiments are based on 3 cells only, which is too low, given that siRNA depletions are known to be variable in their efficiencies. With such low number of cells, there is always the danger of an unconscious selection bias, which can skew a result. Just to take an example the spindle length, structure and density for HAUS-8 depleted RPE1 cells looks very different in the examples show in Figure 1B, 2A, or 5B.It is therefore essential to work with a higher sample size, at minimum 10 cells per independent experiment.

3.Throughout all experiments the authors use 100nm Sir-Tubulin, which in our hands already leads to substantial changes in microtubule dynamics, as it stabilizes spindle microtubules. I understand why the authors did this, as they wanted to also stain for weak bridging fibers, but tt would be important to validate some of the obtained results with an independent approach, for example fixed-cell imaging and tubulin staining, to rule out artifacts introduced by SiR-tubulin.

4.Figure 1: Given that the authors later report that augmin affects more strongly bridging fibers in the central part of the spindle, how were the values in terms of microtubule densities obtained in the experiments in Figure 1: only on the outer microtubules, or overall in the spindle?

5.Figure 2: the authors conclude that depletion of augmin has a much stronger effect on the bridging fibers located in the central part of the spindle. This is a very interesting result, but it begs the question as to the origin of this difference. If the authors analyze in control cells the inter-kinetochore distances and the density of the bridging fibers of the kinetochores located in the central part of the metaphase plate vs those located at the outer part of the plate, do they already see a difference? In other words, is the effect of augmin due to already weaker bridging fibers in the central part of the spindle, or is the depletion effect indeed specific for those bridging fibers located in the middle. This analysis should be possible with the existing data (+ a higher sample size)

6.Figure 4: the authors study spindle width, length and diameter of the metaphase plate in a small number of cells (10). One concern is that these values might change as cells progress from late prometaphase to anaphase onset (metaphase plate width decreases for example). Given the low number of cells the authors do not know if they are comparing cells at similar mitotic times. To circumvent this issues, they could: either arrest the cells with MG132 for 1 hour, to obtain an end-point, or record these different values as cells progress through mitosis and thus be able to compare similar conditions.

7.In the discussion the authors conclude that the longer bundles and the reduction in microtubule poleward flux is due to the absence of bridging microtubules. This is an over-interpretation as augmin could in theory affect these parameters independently of the bridging microtubules, longer bundles could be generally due to the reduced number of microtubules in the k-fibers and the bridging microtubules. A better control would be to affect bridging microtubules with an independent tool, such as PRC1 depletion, and to measure these paramenters in the same RPE1 cell line, since differences can arise from cell line to cell line as the authors also document in their study (for example spindle length in Figure 4).

Minor comment:

-the reported flux rate for control-depleted cells is substantially higher than the flux rates normally reported for human cells. This could be due to the experimental conditions (slight changes in temperature), but at minimum the authors should comment on this.

Significance

The significance of the study is that the authors performed a detailed description of the effects of augmin depletion on the spindle architecture, in particular bridging fibers. Nevertheless, many of the reported results are already known (and as cited by the authors): the reduction in inter-kinetochore distances or the change in spindle architecture. The 3 main novel results, is the fact that augmin affects more bridging microtubules, particularly in the central part of the spindle, and that it also affect poleward microtubule flux, which limits the impact of this study to a specialized mitotic spindle audience. Nevertheless, if the authors address the reviewers concerns, this could be a nice, descriptive study for the mitotic field.

One way to expand the significance of this study would be to test how augmin depletion and the lack of bridging microtubules in the central part of the metaphase plate affects chromosome segregation. Does the specific absence of bridges in this part lead to more lagging chromosomes, chromosome segregation errors, or micronuclei amongst sister chromatids located in the central part of the spindle? Is there a differential anaphase A speed for those kinetochore vs those at the periphery that still are associated to bridging fibers? Such a functional approach could allow to highlight the most interesting aspect of this study, the spatial difference in the effects of augmin depletion. Such experiments would, however, not be part of a revision, but rather a substantial enhancement of the present study.

Patrick Meraldi

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

The authors found that the microtubules in the bridging fibres of the mitotic spindle in a human cell line are predominantly supplied via augmin-dependent nucleation. On the other hand, the contribution of augmin to kinetochore fibre formation is ~40%. Augmin-depleted cells showed reduced inter-kinetochore tension and slower poleward flux of spindle microtubules, suggesting that bridging fibres play a role in these events. This study expands our knowledge on the role of augmin and augmin-mediated microtubules in animal somatic cells.

Major comments:

-Are the key conclusions convincing?

Yes.

-Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

In the current manuscript, the slower flux is attributed solely to the lack of bridging fibres in the augmin-depleted cells. This is an overinterpretation, as the augmin's role in the spindle is not limited to generating bridging fibres.

-Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

No.

-Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

N/A

-Are the data and the methods presented in such a way that they can be reproduced?

Yes.

-Are the experiments adequately replicated and statistical analysis adequate?

Yes.

Minor comments:

-Specific experimental issues that are easily addressable.

None.

-Are prior studies referenced appropriately?

Yes.

-Are the text and figures clear and accurate?

1)Page 15: "To determine the curvature of the bundles, we ..... with all other bundles types (Fig. 5E)." - I could not understand this sentence well, and would like to ask for a revision.

2)The following words may be too strong: Page 20: whereas k-fiber microtubules are "mainly" nucleated in an augmin-independent manner (could 61% contribution be called "mainly?").

Page 21, bottom: "demonstrates".

-Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

No.

Significance

-Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

The presence of bridging fibres has been recognised for decades; however, until recently, little attention has been paid to this structure from a mechanistic and functional point of view. The Tolic lab has been shedding light on this structure for the past several years. The current study represents another step forward in the research of the origin and function of bridging fibres.

-Place the work in the context of the existing literature (provide references, where appropriate).

Augmin's critical contribution to microtubule nucleation in the human somatic spindle has been well documented, as cited by the authors. The current study is the first to show that augmin also contributes to bridging fibres. The >70% contribution may be more than expected, given that centrosomal microtubules frequently reach the spindle midzone. Reduced inter-kinetochore tension has also been documented, but previous studies attributed this exclusively to reduced number of kinetochore microtubules. The current study has revised this view.

-State what audience might be interested in and influenced by the reported findings.

Spindle researchers.

-Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

This review is written by a researcher who is familiar with the literature of the mitotic spindle.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In the manuscript "Augmin regulates kinetochore tension and spatial arrangement of spindle microtubules by nucleating bridging fibers", Manenica et al. explore the impact of augmin-dependent microtubule nucleation on formation of a subset of spindle microtubules that bridge sister kinetochore fibers and investigate how this could affect the spindle forces and architecture. Using RNAi- and CRISPR-Cas9- based loss-of-function experimental approach, the authors propose that the bridging fibers are nucleated by augmin and that removal of augmin impairs proper spindle architecture, interkinetochore tension and microtubule poleward flux, specifically via its effect on the bridging fibers. Overall, the study is well designed and the manuscript well written. Expanding the knowledge on augmin contribution to the spindle functions and better understanding of the roles of bridging fibers would be important and of interest to cell biologists studying mitosis. Although this manuscript clearly shows that augmin depletion impairs the formation of bridging fibers (and other microtubules), the specific contribution of the bridging fibers to the augmin-dependent spindle functions is less clear.

Major comments:

1)Using cold treatment-induced microtubule destabilization, Zhu et al. (JCB 2008) showed that augmin depletion affected exclusively kinetochore microtubules. Since the bridging microtubules are usually not visible in the cold-treated spindles (due to being less stable/cold resistant compared to the k-fibers), it is unlikely that the observed effects were mainly associated with the bridging fibers. Thus, it would be important to further clarify the respective contribution of augmin to the formation of k-fibers and the bridging fibers. The cold-treatment experiment performed by Zhu et al. could be used in RPE1 and HeLa-PRC1-GFP cells to address the contribution of augmin nucleation to kinetochore- vs. bridging microtubules from another angle.

Because of the above mentioned results by Zhu et al. it is difficult to grasp how augmin depletion could have a bigger effect on the bridging fibers than on the k-fibers, as concluded from the Fig. 2C data. In fact, Fig. 2A clearly shows a strong effect on k-fibers in spindles where the bridging fibers are reduced/missing.

Also, Fig. 1 D and E suggest that HAUS8 siRNA exclusively affected the bridging fibers, leaving the k-fibers intact, which is again against the data reported in Zhu et al. 2008 and in contrast with the representing image shown in Fig. 1B. Even if the RNAi was less efficient compared to HAUS6 RNAi, as the authors proposed, this could still not explain the observed discrepancy.

2)The authors showed that kinetochore pairs in the outer parts of Augmin-depleted spindles have larger inter-kinetochore distance compared to those in the inner parts of spindles. They indirectly related this to a predominant presence of the bridging fibers in the outer parts, concluding that augmin regulates inter-kinetochore tension via nucleation of the bridging fibers. A more direct way would be to show the eventual positive correlation between the inter-kinetochore distance and the bridging- and k- fibers intensity. Also, it would be nice to include the quantifications and correlation data for inter-kinetochore distance, distance from the spindle axis and the bridging- and k- fibers intensities for the control cells too.

3)It is stated in the manuscript that the k-fibers without bridging fibers have shorter contour length compared to the k-fibers with bridging fibers, and that the curvature of k-fibers lacking the bridging fibers is drastically reduced. However, the data in Figure 5D and Table 1 show a slight effect on the contour length of the k-fibers lacking the bridging fibers compared to the ones containing the bridging fibers only in RPE1 siHAUS8 cells, while this effect seems to be missing in RPE1 HAUS8 KO cells, as well as in siHAUS6 in RPE1 and HeLa cells.

Fig. 2 shows that the kinetochore pairs without the bridging fibers are located closer to the spindle axis. Thus, it is not clear whether the effect on curvature observed in the augmin depleted cells is independent of the position of kinetochore pairs within the spindle, as the spindle axis-proximal pairs would anyway have a bigger radius compared to the more distant ones.

4)The authors reported that augmin depletion impairs microtubule poleward flux and conclude that this happens exclusively due to the perturbation of bridging fibers. While the results from this and other studies clearly show that augmin depletion perturbs spindle microtubules in general, it is not clear whether this had a stronger effect on the bridging microtubules (see the comments in point 1). Thus, the impact of augmin depletion on kinetochore microtubules or other antiparallel microtubules within the spindle (e.g. the ones recently shown in O'Toole et al., MBoC 2020) cannot be ruled out as a potential cause of the impaired microtubule flux. Also, Steblyanko et al. (EMBO J, 2020) showed that PRC1 depletion had no effect on microtubule poleward flux in metaphase cells. Since it has been previously shown by the authors of this manuscript that PRC1 depletion disrupts the formation of bridging fibers, it is unlikely that the bridging fibers are the main cause of the augmin depletion-mediated effect on the microtubule flux.

Minor comments:

1)Introduction: chromatin- and kinetochore- mediated generation of spindle microtubules are ignored when describing the origins of spindle microtubules in human somatic cells.

2)The authors proposed less efficient HAUS8 depletion as a potential reason of discrepancy between the siHAUS6 and siHAUS8 results. This should be shown by Western blot, like it is presented for the RNAi efficiency of siHAUS6.

3)The measurements of total PRC1 intensities are mentioned in the manuscript text, but not shown in the figures.

4)Supplementary Videos 3 and 4 are wrongly annotated as Supplementary Videos 1 and 2 in the text.

5)Given the spindle length phenotypes are opposite in HeLa and RPE1 cells, in order to be consistent with the other experiments it would be better to perform the PRC1 measurements in RPE1 cells (e.g. using the anti-PRC1 antibody as shown in Supplementary Fig. 3B).

6)Why are the microtubule flux rates for RPE1-PA-GFP-α-tubulin cells measured in this study largely different than the rates reported for the same cell line in Dudka et al., Nat Comms 2018 and Dudka et al., Curr Biol 2019? In order to better understand this difference and strengthen the microtubule flux data, it would be helpful to increase the experimental numbers to match the ones used in the mentioned studies.

7)The number of cells used per each experiment should be clearly stated.

Significance

This study expands the analysis of augmin contribution to the spindle functions and focuses on its role in formation of the bridging fibers, which is of interest to cell biologists studying mitosis. It clearly shows that in addition to its effect on the k-fibers, augmin depletion also impairs the formation of bridging fibers. However, the exact contribution of the bridging fibers to the spindle functions affected by augmin depletion remains unclear.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a response at this time.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors found that the expression of CXCR2 is decreased in patients with moderate COVID-19. However, the mechanisms were not explored. The hyperactivation status of neutrophils is not well defined, and proteomics data are not validated. The rationale for comparing healthy controls and severe COVID-19 patients is unclear. The manuscript in its current form raised more questions than answers.

Major concerns:

1. No information is available on the healthy control group. How do they compare to the COVID-19 group? Age-, sex-differences? Comorbidities?
2. Figure 1E. While the decrease in the level of CXCR2 expression in the moderate group is statistically significant, the functional significance of this finding is unclear. The MFI mean value of approximately five hundred units is still high. Whether it would it be translated into decreased neutrophil migratory activity and tissue recruitment is unknown. As with any G-protein coupled receptor, the ligand-dependent stimulation of CXCR2 would induce its internalization. Do the authors consider the possibility of increased levels of CXCR2 ligands causing lower cell surface levels of CXCR2 in patients with moderate illness?
3. The proteomic analysis would be helpful in the identification of potential mechanisms involved in the reduced level of CXCR2 in the moderate group. However, the authors have decided to perform this analysis on healthy controls and patients with severe COVID-19 illness, two groups with a similar level of CXCR2 expression.
4. Figure 2. No information is available on the selection criteria for the samples used in proteomic analysis. How representative were those four healthy controls and three COVID-19 patients for their respective groups?
5. Figure 2. It is unclear why the authors believe that the changes identified in proteomic analysis indicate the hyperactivation status of neutrophils. The analysis is performed by comparing neutrophils from the severe COVID-19 group against healthy control subjects. Would it be different for mild or moderate illness groups if compared to patients with severe illness or healthy subjects? Without these data, it is hard to understand if reported changes indicate hyperactivation.
6. The authors' statement on neutrophil activation is not confirmed by any measurements in vitro or in vivo. It is unclear if these neutrophils produce more proinflammatory cytokines or reactive oxygen species? Are they more prone to undergo NETosis?

Minor:

1. It is unclear why the statistical approach in Figures 1A and B is different from the approach used in Figures 1C, D, and E.
2. Figure 1A, flow cytometric dot plot: It is interesting to see that the immature neutrophils are represented by a distinct subset of CD10- cells. In other studies, including those cited by the authors, immature neutrophils are characterized by gradually decreased expression of CD10, not distinctly separated from mature neutrophils.
3. In Supplemental Figure 1 - the gating strategy for singlets is mislabeled; should be FSC-A vs. FSC-H, but listed as FSC-A vs. SSC-A.
4. It may increase the translational value of the study if the authors perform an analysis of immune markers against clinical parameters demonstrating the severity of illness, e.g., hospital length of stay or hospital-free days, patients in an intensive care unit (ICU) versus non-ICU, and lab tests, serum CRP, WBC, NLR.

Significance

In the current study, Rice et al. investigated the subpopulation of peripheral blood neutrophils obtained from patients with COVID-19 and healthy controls. The authors performed flow cytometric and proteomic analyses to determine the association between immunophenotype and activation of neutrophils and the severity of COVID-19 illness. The flow cytometric analysis is meticulously executed and informative and confirms previously published data on the immature status of circulating neutrophils in COVID-19.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary

In this manuscript, the authors used flow cytometry to investigate activity and phenotypic diversity of circulating neutrophils in acute and convalescent COVID-19 patients (acute COVID-19 patients: 34; healthy controls: 20). Further analysis indicated that hyperactivation of immature CD10- subpopulations in severe disease. Additionally, the authors found CXCR2 was down-regulated in moderately ill patients, and CD10- and CXCR2hi neutrophil subpopulations were enriched in severe disease. This work is interesting, yet the main problem of this work is that it lacks of novelty, and the conclusion was proposed without solid evidence.

Major points:

1. The author 's main conclusions were based on flow cytometry. However, they didn't validate the purity of neutrophiles sorted by their sorting strategy.
2. The statical analysis should be checked by statisticians.
3. The author indicated they detected decreased expression of CD10 from moderate and severe COVID-19 patients, and concluded the potential of its prognostic utility. However, this conclusion is not novel, previous research performed by Silvin et al. and others have presented the immunosuppressive profile of CD10lowCD101-CXCR4+/- neutrophils in severe form of COVID-19 (PMID: 32810439, PMID: 33968405).
4. It seems that the author specifically picked CD10 to present its difference between patients and heathy controls, yet, for one thing the author didn't show how they detect the expression of CD10, did they perform western blotting, transcriptome or proteome? For another, the author did not show explain if CD10 is the only proteins or the top-ranked protein that show prognostic value.
5. To further explore the neutrophil activation and chemotactic capacity, the author compared the proteomes of circulating neutrophils from severe and healthy controls. However, comparing to the published work, the sample numbers were too small, for there are only three severe patients enrolled, the author should include more samples for analysis.
6. The author performed UMAP analysis, and conclude long term perturbations to the myeloid compartments of convalescent patients. This conclusion is too rash, the author should include clinical index, such as absolute neutrophil counts, neutrophil percentage for integrative analysis.
7. The proteins that the author indicated to be neutrophil functional related are more likely to be functional universal. The author should include neutrophil specific datasets and screen out neutrophil specific markers for further analysis.
8. The author utilized X-Shift analysis to analyze the distinct neutrophil phenotypes in different disease states, yet, only one or two markers can hardly describe the whole picture. The author should conduct single cell transcriptome or proteome to systematically depict the diverse neutrophile phenotypes in different disease status.
9. There are multiple published papers describe the immune cell subsets of COVID-19 (PMID: 32838342, PMID: 33657410), the author should compare with them.

Minor point:

1. In table 1, the authors did not provide the p value among Mild, Moderate, and Severe groups.
2. In Sup Fig 1B, Sup Fig 1C, Sup Fig 2E-G, I-K, Sup Fig 3D, the authors did not provide p value.
3. The author assumed "Principle component analysis (PCA) demonstrated heterogeneity amongst the severe patients, which was explained by patient outcome (Fig 2C)." Again, too small sample numbers, can hardly show the diversity.
4. In Fig2G, the authors descripted patient neutrophils, and not descripted which type of patients.
5. The authors mentioned Fig1G in the sentence "Ingenuity pathway analysis (IPA) identified pathways related to chemotaxis, such as 'Signalling by Rho family GTPases', 'RhoA signalling' and 'Regulation of Actin-based Motility by Rho' as significantly enriched in patient neutrophils (Fig 2G), which aligns with maintained expression of CXCR2 (Fig 1G)", however we did not see the corresponding Fig1G.

Significance

The paper lacks arguments regarding the novelty of the findings, as well as context with the current literature available for COVID-19 (several examples of the available literature references are provided) including comparison to published single cell dataset of COVID-19 (PMID: 32838342, PMID: 33657410, PMID: 32810439, PMID: 33968405). The paper focused more on known example, which are indeed useful to assess their strategy, but failed to detail their findings about unknown protein candidate which would bring more value to the manuscript.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a response at this time.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

The manuscript entitled "Proximity labelling identifies pro-migratory endocytic recycling cargo and machinery of the Rab4 and Rab11 families" by Wilson et al, presents an approach, BioID, able to identify and characterize protein complexes associated with Rab proteins in an ovarian cancer cell line. They started the study by coupling a proximity labelling method to mass spectrometry. By doing so they identified the interactomes associated with Rab4a, Rab11a and Rab25. Next, the authors proceeded to detect directly biotinylated peptides. Then, using knock sideways experiments, the authors validated novel links between Rab11/Rab25 and some of the direct interactors identified. Lastly, they propose that SH3BP5L and CRACR2A are required for migration of ovarian cancer cells, in 3D-cell derived matrix.

Major comments:

1) A major limitation of the study is the reliance on a single migratory cell line, the A2780 cell line. As such the authors should include additional cell lines for their key experiments throughout the manuscript.

2) The authors state that BioID-Rabs are expressed at a "level close to endogenous". This should be quantified. Also, authors should clearly show that BioID-Rabs co-localize with the endogenous Rabs. So, immunofluorescence labelling of endogenous Rabs and markers for Early Endosomes (e.g. Rab5, EEA1, etc) and Recycling Endosomes should be performed.

3) In the dot-plot of the high-confidence proximal analysis, the average intensity (represented in the circle colour) should be normalized by the abundance of protein.

4) The knock sideways experiments validated high affinity prey interactions, including of sorting nexins with Rab4/11/25. SNX1 and SNX3 showed that they would only significantly redistribute in FKBP-GFP-Rab11a and FKBP-GFP-Rab25, respectively. Authors should comment on why the role of SNX1 and SNX3 was not assessed in migration studies.

5) Knock sideways showed that Rab4 was unable to induce significant re-localization of CLINT1. This would suggest that CLINT1 would be a candidate less robust than others identified by BioID and validated by knock sideways experiments. Why did the authors decide to proceed to assess the role of CLINT1 in migration studies?

6) Although the authors reported a lack of significant re-localization of CLINT1 by Rab4a, they state that "CLINT1 plays a role in Rab4 (but not Rab25) dependent migration in 3D-CDM". Can the authors comment on this?

7) "CLINT1 was identified as a Rab4, -11 and -25 proximal protein (Figure 2)". The study would benefit from additional evidence showing that CLINT1 does not act downstream of Rab11 to control migration of A2780 cells.

8) Authors should include immunofluorescence studies to better characterise the role of Rab4a, Rab11a and Rab25 networks in migration, adhesion and leading-edge related processes. Focal adhesions should be quantified, and actin cytoskeleton described. Such studies should be coupled to the cell migration studies. These would validate and support the conclusions drawn from the GO analysis.

9) In the discussion, the authors mention two other papers in which "proximity labelling methods have proven an excellent tool for identification of protein complexes, including for Rab4 and Rab11". The authors should also discuss if there are overlapping results.

Minor comments:

1) Figure 1: Panel A is too small. Insets are hard to interpret. The size of the whole panel should be increased.

2) Description of results regarding the trafficking machinery associated with Rab4a, Rab11a and Rab25 does not follow the same organization and structure as in Figure 2. The authors should try to match the organization of data and its description to improve readability.

3) In Figure 4B and S4C there are two labels for 1 and 2.

4) Figure S4E merge of GFP-FKBP Rab11a cells shows poor overlap. A replacement should be considered.

5) There are several typos in the discussion and in Figure 7 ("CRACRA" should be CRACR2A)

Significance

• The manuscript presents an approach that allow the identification of Rab-associated networks and the direct comparison between GTAses. This is of relevance since we still lack robust methodologies to identify the endosomal trafficking machinery underlying migration in cancer cells. By not targeting Rab4 specific machinery (e.g. TBC1D5), the authors missed the opportunity to expand the knowledge regarding the machinery sustaining Rab4-dependent migration in cancer cells.

• The work targets an audience interested in endosomal trafficking and protein recycling in cancer cell migration.

• The reviewer is a translational cancer biologist with expertise in cytoskeleton, endosomal recycling, signaling and cancer.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Wilson et al. submitted a paper entitled: "Proximity labelling identifies pro-migratory endocytic recycling cargo and machinery of the Rab4 and Rab11 families". The goal of the paper is to identify new interactors for RAB4/11 and 25 that could be involved in Rab-dependent migration. To do so, they used BioID of the aforementioned 3 Rabs in mesenchymal and migratory ovarian cancer cell line A2780. They validate some of the interactors using the knock-sideways technique and test the requirement of some interactor for migration/invasion in a 3D matrix. This is a very descriptive paper that could benefit from more in-depth mechanistic analysis of fewer candidates.

Major comments:

• For the most part, the data appears of excellent quality and most of the conclusions or interpretations are correct (see below for a few points that can be improved). Some key concepts are missing in the introduction. For example, the concept of GEFs and GAPs only appears later in the experimental section - this should be introduced earlier.

• The description of the BioID data is poorly structured and descriptive, a recurring challenge with big data paper. One suggestion to improve the manuscript would be to exploit the best-known interactions to clearly benchmark the efficiency of the screens. Next the new interactions could be described and figure 2 could be better exploited in that respect (the mentioned complexes could be better drawn etc.). The text could also be more focused on fewer interactors such that it is more digestible for the readers. The major weakness of the manuscript, in my opinion, is the lack of depth in testing functionally some of the uncovered novel interactions.

• Some additional experiments that would be needed to support the claim of novelty in the paper include testing the function of some of the tested interactions. For example, the novel GEF interactions would benefit from biochemical testing in addition to BioID. Likewise, the section on biotinylation and interaction domain mapping is interesting but is, as presented, a theory. Using one interaction to dissect in more details to support this claim is needed. Alternatively, can the authors demonstrate that this approach can be used to confirmed known protein domains involved in protein-protein interactions of these Rabs? Finally, the authors end their manuscript by screening candidates issued from their BioID which have not been implicated in migration/invasion before. This is somewhat preliminary and fails to provide some depth into the function of one of these potential interactions (domain mapping, knockdown rescue of wt or mutants etc.).

• The authors use the knock-sideways technique to validate the strength of their interaction. This is a clever way to validate interaction in cellulo which could be difficult using conventional IP. However, it looks like the expression of FRB-MITO leads to mitochondria fragmentation and aggregation. Is it possible that this cause a bias in their quantification analysis because it becomes difficult to clearly delineate individual mitochondria? In some cases (ex. Fig 5C), the recruitment of the candidate is obvious. However, in other cases (ex. Figure 5A) the recruitment to the mitochondria is not very convincing and looks more like the candidates collapse around the aggregated mitochondria. The authors should therefore describe the limitations in more details.

Minor comments:

• The authors aim to identify new interactors involved in migration, but they performed the BioID on confluent cells where cell migration is likely limited. Would comparing a BioID performed on confluent cells with one where the cells are sparse enough to migrate possibly interesting to conduct? This could be discussed.

• In Figure 1C, it is difficult to read the name on the candidates. The authors should fit the entire name in the nodes (maybe use an ellipse instead of a circle).

• In Figure 1C and 2 the known interactors could be in a different color emphasize the new potential interactors.

• Figure 4 is very heavy and the images are small making difficult to see the results clearly. Instead of showing 10 time points per condition, 3 or 4 time point with higher resolution images would have been more appropriate.

• Methods: The methods are well described. It is a bit surprising that the BioID samples are run on SDS-PAGE and that bands are cut when on beads digestion is currently done by many lab for this technique.

• Statistics: Statistics should be provided for all quantification, not only the one that are significant. For the non-significant, the P-value should be indicated on the figure.

• The authors looked at endogenous Rab11 vs BioID-Rab11. Why no do it for the other 2 Rabs. Also, quantification of endo/exo expression should be done.

Significance

• The advance of this work is to expand the potential functional interactome of three Rabs involved in slow recycling of endosomes. Some novel interactions are reported and some screening approaches have been use to reveal functional ones (this could be improved).

• This work is potentially important and part of the priorities in the field to ascribe the overlapping and specific interactions/functions of Rab subfamilies. Similar work has been done for Rho proteins and selected Ras oncogenes.

• The work presented here would be of broad interest for people in the cell biology field.

• The expertise of this reviewer is in Ras-superfamily proteins, proteomics, cell migration/invasion and as such was qualified to assess this manuscript in its entirety.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

From methodology and reproducibility point of view it is an excellent manuscript. It is also well-written.

Significance

• This is a manuscript that presents an in-depth analysis of potential interactome and cross-interactome of Rab11a, Rab4a and Rab25 GTPases. BioID and knock-sideway data presented in first half of the manuscript is very interesting and undoubtedly will be of a good use for many laboratories. However, authors tend to over-interpret some of their data, suggesting functional connections between specific Rabs and BioID hits without any additional data. Authors admit themselves that there are some disconnects between BioID and knock-sideways data. Furthermore, BioID measure proximity and not functional connection.

• Second half of the manuscript focuses on taking some of the BioID hits and testing whether they are required for mediating cell migration. By itself, it is a great idea since that would provide that functional connection that is missing in the original BioID screen. Unfortunately, the data is limited to few knock-downs without any further analyses of the involvement of these proteins in regulating migration. Consequently, as it stands, this manuscript is essentially a BioID screen with limited insights or validation of specific "hits", thus, does not really lead to any new conclusions about cross-function of Rab11, Rab25 and Rab4 networks.

• Additional comments:

1) There are no blots shown (only boxes) for Figure S1C-D. Data in Figure S1 doe shown that BirA-Rab11a is expressed in similar levels as endogenous Rab11. However, no data supporting similar statement for Rab4 and Rab25 is shown.

2) The presence of specific proteins in BioID does not mean that they either directly bind or regulate particular BirA-Rab. For example, authors state "DENND4C, related to Drosophila Rab11 GEF CRAG, was enriched to Rab11a, suggesting that this could be an alternate GEF for Rab11". There is no data supporting such a statement in this manuscript. Actually, DENND4C is better known GEF for Rab10. Rab10 is also known as Rab present in recycling endosomes, thus, could have easily be present in Rab11a-positive recycling endosomes. There are numerous similar statements in the manuscript that implies functional connections between Rabs and BioID "hits" without providing any other functional data.

3) Authors should not use RCP term to refer to Rab11FIP1 since Rab11FIP1 is its established name and using other names only creates confusion. RCP term was first used to indicate that Rab11FIP1 can bind to both Rab4 and Rab11, the hypothesis that since then was proven to be incorrect.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a response at this time.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

The metalloprotease ADAM17 is a key drug target for inflammatory diseases and tumors. The authors previously demonstrated that ADAM17 activity is controlled by iRhom proteins and by a largely uncharacterized protein called iTAP, which had been mostly investigated in vitro. The current manuscript extends the previous findings to in vivo functions, in particular in pathophysiological conditions. The authors demonstrate that iTAP-deficient mice are viable and largely without overt phenotypes under physiological conditions, but do show phenotypes upon inflammatory conditions and during tumorigenesis. During LPS-induced inflammation, iTAP-deficient mice are reported to show defects in epithelial repair functions. Upon lung tumor cell injection, iTAP-deficient mice revealed reduced tumor growth in a cell autonomous and a non-cell autonomous manner, raising the possibility to use iTAP as a potential new drug target for certain tumors.

The study is novel, the manuscript is well written and easy to understand and the conclusions are largely justified by the data.

My only major concern is the choice of the control LLC cells. The cells used are not the ideal control for the iTAP knock-out cells. Both wild-type and iTAP knock-out cells were transduced with a Cas9 expressing vector, as it should be. But only the knock-out cells were further transduced with a virus expressing the gRNAs against iTAP, whereas the control cells apparently were not transduced with a virus expressing control gRNAs. Three single cell clones of the iTAP ko cells were pooled for in vivo injection, whereas the parental pool (and not clones) where apparently used as a control. My concern is that the ko cells do not only differ from the wild-type cells due to the knock-out of iTAP, but potentially also due to other gene expression alterations resulting from the additional transduction of the knock-out cells with a gRNA virus and because of the selection of single cell clones. Such expression changes beyond the simple lack of iTAP may have a major influence on those tumor phenotypes in vivo, where these cells were used. Ideally, the authors would generate an additional, independent pool of iTAP knock-out cells and repeat one of the crucial in vivo experiments. As a time-saving alternative, the authors need to demonstrate that the iTAP knock-out cells are nearly identical to the control cells (with the exception of iTAP). This could be done by RNA sequencing or cell lysate proteomics or by blotting for several different proteins (at least 10 from different compartments) and demonstrating that there is no significant change in protein abundance - apart from iTAP.

I do have a number of additional, but minor points.

1. Indicate the concentrations of the used drugs (marimastat, PMA) in the figure legends.
2. Indicate in the manuscript that LLC cells are of mouse origin.
3. Page 6, top paragraph: it is not clear to me, whether there is an eye phenotype or not. Please rephrase this sentence.
4. Figure legend 1: "...with 3 replicates per experiment". Indicate whether this refers to biological or technical replicates.
5. Indicate in figure legends which statistical test was used.
6. Fig. 2F. The y-axis label should be body weight and not body weight loss.
7. Fig. 4C: the increase in the 75 kDa fragment upon iTAP OE is difficult to see. Can you quantify the increase? And also the reduction in the KO cells?

Review Cross-commenting

When reading the comments from reviewer 1 and 2, it is not always obvious to me which experiments must be done (as a requirement) and which ones are "just" nice to add. It would be great if this could be specified clearly in their reviews.

Significance

This study is exciting. It shows for the first time the pathophysiological role of iTAP in vivo and has major implications for ADAM17, which is a drug target in numerous diseases, in particular sepsis, inflammation and tumors. However, systemic ADAM17 inhibition induces severe side effects so that approaches are sought that allow a tissue-specific inhibition of ADAM17. One way to achieve this, is to block the protein iRhom2 which is a non-proteolytic subunit of an ADAM17-iRhom2 complex. Loss of iRhom2 allows a tissue-specific inhibition of ADAM17 specifically in immune cells, because other tissues express iRhom1 that can largely (but not fully) compensate for loss of iRhom2. Thus, iRhom2 inhibition is currently pursued in drug development. The current manuscript demonstrates an additional way (through iTAP) of selectively blocking pathophysiological functions of ADAM17 in tumors (and potentially sepsis), while maintaining physiological functions. This study is an important step towards the use of iTAP as a drug target. Thus, this study will be of interest to basic scientists studying ADAM17, its regulation, its substrate specificity and its physiological functions. The study will also be of interest to translational scientists in academia and pharma/biotech studying the numerous ADAM17-dependent diseases. A clear strength of the study is the inclusion of different disease models, where iTAP plays a role (protective or non-protective), and the demonstration that iTAP contributes to tumors both in the tumor niche and in the tumor itself. A limitation of the study is that the underlying mechanisms remain unclear apart from reduced ADAM17 activity. In particular, it remains open which substrate(s) contribute on the tumor side or the niche side. This lack of mechanistic insight is addressed in the discussion section, where a number of future follow-up experiments are suggested. Another central open mechanistic point is the question of why iTAP, that binds to both iRhom1 and iRhom2, apparently only affects iRhom2 function in vivo. Maybe iTAP only acts on iRhom2-dependent ADAM17 substrates? Despite these mechanistic weaknesses that need to be addressed in future studies, the study is exciting. I have expertise in ADAM17 and iRhoms, but cannot fully judge the tumor histology.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

In "The ADAM17 sheddase complex regulator iTAP modulates inflammation, epithelial repair, and tumor growth" the authors investigate the role of iTAP (FRMD8) in regulation of the ADAM17 sheddase complex. This manuscript is a follow-up to a previous study (Oikonomidi et al. 2018) in which the same group (and another group, Künzel et al. 2018) defined iTAP and generated an iTAP-deficient mouse model via CRISPR. The current work uses in vivo models of sepsis (LPS injection), colitis (DSS administration), and tumor growth and metastasis (LCC subcutaneous and IV transfer models) to further investigate the role of iTAP during disease. The authors find that mature ADAM17 levels were decreased in immune cells from iTAP-deficient mice and shedding of L-selectin was impaired. They next showed that iTAP KO mice have reduced TNF serum levels in a sepsis model. During experimental colitis, iTAP KO mice had higher levels of intestinal disease indicators. In a subcutaneous tumor model, iTAP KO mice showed decreased tumor burden. Furthermore, the authors observed tumor cell autonomous and cell-non-autonomous roles for iTAP in subcutaneous and IV LLC transfer models. While this study nicely adds to our knowledge about in vivo effects of iTAP-deficiency, it is largely descriptive with little investigation into the mechanisms by which iTAP/ADAM17 promote disease. Despite these limitations, the authors make claims about mechanism in the title, abstract, and text without data to support these statements. For example, one of the conclusions of the manuscript is that iTAP influences tumor growth via control of cell proliferation yet there are no data to support this claim. Therefore, I have serious reservations that need to be addressed before I could consider publication of this work.

Major comments:

Figure 1: The findings regarding L-selectin shedding are very clear and perhaps meaningful. However, a discussion putting these findings in context with the disease models used later in the manuscript is warranted. Currently, inclusion of these data does not add much to the story if not discussed or referenced later in the manuscript.

Figure 2: The authors observe that iTAP KO mice have worse outcomes following DSS-colitis. In the text, they mention that iRhom2 KO mice do not phenocopy the iTAP KO mice following DSS-colitis, yet no explanation is offered. If the mechanism of iTAP is proposed to be through iRhom2 activity and ADAM17 shedding, you would expect the iRhom KOs to demonstrate similar intestinal phenotypes. The authors should comment on this discrepancy.

Additionally, the conclusion about the importance of iTAP in intestinal repair would be better supported if the DSS colitis experiments were continued to later time points to include the recovery phase (once the mice return to original body weight), rather than just ending the experiment at peak repair.

Figure 3: The authors make the statement that "...although inflammatory infiltrates were modest in the lungs of mice..." Is this based on histology alone? If the authors want to make this claim, they must assess immune infiltrates directly (e.g. using flow cytometry).

The authors evaluate lung metastasis in the LLC subcutaneous model but any conclusion about metastasis cannot be made in this model without looking at primary tumors of a similar size. Metastasis tends to be associated with the size of the primary tumor so smaller primary tumors usually mean lower levels of metastasis (without being able to parse apart direct effects on the metastatic process). I assume that the data in Fig 3H are from mice with different tumor sizes--in order to properly evaluate this, the authors need to euthanize WT and KO animals with similar tumor burdens and compare metastatic burden.

Including total mRNA levels of cytokines does not add to this figure. First, bulk levels of mRNA are not a good way to evaluate the state of a tumor (immune cell phenotype/activity would be better). Second, TNF and IL-6 were used in previous figures as readouts of ADAM17 activity (or not) and here are just markers of inflammation? This is confusing/contradictory. If included, this should be moved to the supplement.

Figure 4: Claims about proliferation cannot be made here because the results as shown are not significant (Fig 4K). Additional readouts for proliferation should be used to support this conclusion.

Similar to Figure 3, claims about metastasis cannot be made from these experiments without comparing mice with similar primary tumor burden. The metastasis data in Figure 5 are much more solid and convincing.

Figure 5: The authors use Fig 5 K & L as evidence that tumor cells proliferated more or less rapidly, depending on expression levels of iTAP. The data do not support this statement. If I understand the methods correctly, this assay involves plating of 500K tumor cells and then harvesting after several days. Upon harvest, there were 100 fold fewer cells (~5K). To me this indicates effects on survival, not proliferation. Proliferation was never measured in this assay. Without these data, the authors can make no claim regarding the mechanisms of tumor cell autonomous functions of iTAP.

Minor comments:

The language regarding any results that are not statistically-significant need to be softened in the text. In several places, there are statements about non-significant results that are much too definitive and somewhat misleading. Non statistically-significant results can be useful to include to show trends (as in Fig 5 G-I), but the interpretation should not be overstated.

The title is overstated. In this manuscript, the authors do not show clear mechanistic links for iTAP promoting epithelial repair (worse outcomes after DSS are not just caused by decreased repair). The strongest data in the manuscript are those regarding tumor growth. This should be highlighted in the title.

Significance

This work adds additional data to support the importance of iTAP/sheddase complex/ADAM17 in disease development. Most importantly, it suggests a role for iTAP in tumor progression. However, the mechanisms leading to increased tumor growth still remain unknown. Additional work is required to elucidate the molecular mechanisms underpinning these observations.

The target audience of this work would include cancer biologists and experts studying growth factors and metallopeptidases. For context, my background is in tumor immunology and immune-stromal interactions.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The study analyzes the function of the FREM domain containing protein Frmd8/iTAP, which the authors have identifies as a binding partner of iRhom2. This rhomboid pseudoprotease has earlier been identified as a binding partner of the membrane-bound metalloprotease ADAM17. The iRhom2 protein is necessary for trafficking of ADAM17 through the ER/Golgi network to eventually reach the cell surface. Apparently, the proteins Frmd8/iTAP, iRhom2 and ADAM17 form a sheddase complex. In the present study, the authors have used knock-out mice for the gene coding for Frmd8/iTAP to analyze the role of the Frmd8/iTAP protein in vivo. The authors found that maturation of ADAM17 in hematopoietic cells was impaired and that shedding of ADAM17 substrates was strongly reduced. In a DSS inflammatory bowel disease model, Frmd8/iTAP knock-out mice were slightly more affected than WT mice. When tumor cells were injected into WT or Frmd8/iTAP knock-out mice, tumors were smaller in the absence of the Frmd8/iTAP protein. The deficiency of Frmd8/iTAP in tumor cells resulted in less tumor growth whereas the overexpression of Frmd8/iTAP in tumor cells led to more tumor growth. I.v. injection of tumor cells deficient for Frmd8/iTAP led to significantly less metastases, tumor volume and tumor burden. Th authors suggest that therapeutic intervention at the level of Frmd8/iTAP might be helpful during inflammatory diseases or cancer.

This is an interesting study, which addresses the important role of ADAM17 and the pathways controlled by this protease. There are, however, some points the authors should address.

Major points:

1. Although the Frmd8/iTAP protein was identified as a binding partner of the iRhom2/ADAM17 complex, it remains unclear whether this protein also serves as a binding partner of other proteins. When analyzing Frmd8/iTAP knock-out mice, this might be an important aspect, which is not addressed in the manuscript. Is Frmd8/iTAP always co-expressed with iRhom2 and ADAM17?
2. It has been shown that iRhoms have additional clients apart from ADAM17. For instance, the adaptor protein STING has been reported to be constitutively associated with iRhom2. Therefore, it is possible that Frmd8/iTAP also plays a role in the STING pathway. This point needs to be addressed.
3. All Western blots shown in the figures and supplemental figures should be quantified by a suitable software such as Image J.
4. In Fig. 2C,D, the authors use a sepsis model and they show that Frmd8/iTAP knock-out mice have lower TNFa levels than WT mice. Is this also true for sIL-6R levels? Was survival of the mice affected by the absence of Frmd8/iTAP?
5. In Fig. 2E-J, the authors employ a DSS-driven inflammatory bowel disease model. It has been shown before (Chalaris et al, 2010; cited in the manuscript) that the higher susceptibility of hypomorphic ADAM17 mice was related to reduced shedding of EGF-R ligands in this model. Therefore, the authors should address shedding of these ligands in Frmd8/iTAP knock-out mice.
6. In the experiment shown in Fig. 5, the authors inject parental and Frmd8/iTAP knock-out LLC tumor cells into WT mice. The note that the number of metastases, tumor volume and tumor burden is dramatically decreased. In the study by Bolik et al, 2022 (cited in the manuscript) it has been shown that in hypomorphic ADAM17 mice, metastasis formation by LLC tumor cells was dramatically reduced. In this study it was also shown that ADAM17 activity in endothelial cells was responsible for this effect, which was at least in part mediated by TNF-RI and TNF-RII. This mechanistic difference should be addressed in the manuscript.
7. Along the same line: when tumor cells are injected i.v., the cells need to extravasate before they can form tumors. The authors need to mechanistically address whether the effects of Frmd8/iTAP are on extravasation or on tumor growth (or both).

Minor points:

1. The authors name the protein Frmd8/iTAP sometimes as Frmd8 and sometimes as iTAP. This is confusing for the reader. Since the protein has been characterized under both names, the authors should stick to Frmd8/iTAP.
2. Along the same line: the authors should stick to the name ADAM17 and not sometimes switch to the older name TACE.
3. The authors use Frmd8/iTAP knock-out mice. It is not clear from the statement of p5, whether they use the mice described in Künzel et al, 2018 or the mice described in Oikonomidi et al, 2018. This should be clarified.
4. Some references (e.g. Dong et al, 1999 and Gschwind et al, 2003) are incomplete.

Significance

Nature and significance of the advance:

Knowledge about the susceptibility of Frmd8/iTAP knock-out mice to some disease models of inflammation and cancer.

Compare to existing published knowledge:

It was known before that Frmd8/iTAP plays a role in ADAM17 maturation and that the absence of Frmd8/iTAP leads to lower shedding of several substrates.

Audience:

ADAM17 governs important pathways such as TNFa, IL-6R, EGF-R and others and therefore, the regulation of ADAM17 activity is of interest to many readers.

Your expertise:

I work on the cytokine IL-6 and the IL-6 trans-signaling pathway, which relies on the soluble IL-6R, generated by ADAM17. Therefore I feel competent to review the manuscript.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

__Manuscript number: __RC-2022-01357

__Corresponding author(s): __Peter Novick and Gang Dong

1. General Statements [optional]

We would like to thank both reviewers for their thorough and constructive evaluation and comments on our manuscript. Following their suggestions, we have reworked our manuscript and added several pieces of new data to address questions from them, including (1) evaluation of how M7 mutant of Sso2 affects its interaction with Sec3 using three independent methods (in vitro); (2) investigation of how the M7 mutant affects the interaction of Sso2 with Sec3 by co-immunoprecipitation (in vivo). We hope that, with all these further introduced changes, this manuscript will be suitable for publication in your journal. Detailed point-to-point responses are shown below.

2. Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity (Required)): *

Using the entire cytoplasmic domain of Sso2 and protein crystallization, Peer and colleagues show that two N-terminal peptides (NPY) of Sso2 synergistically interact with the Sec3 PH domain. This interaction provides an additional low affinity binding site to the previously published interface between the Sso2 four-helix bundle and the PH domain. Mutagenesis, in particular of both NPY motifs, results in reduced cell growth, in the accumulation of transport vesicles at the budding site, and in decreased secretion of invertase and Bgl2. The paper is well written, the data are convincing and the characterization of these novel peptide interaction sites clearly advances the field. Although, the exact role of the Sec3 NPY - Sec3 interaction still needs to be established, the overall functional relevance is apparent and thus the paper could be published with minor changes. *

__Response: __We really appreciate the reviewer for his/her positive comments and clear/constructive feedbacks.

*Nevertheless, the authors may consider to address the following issues to improve the manuscript. - To strictly exclude the possibility that the Sso2 NPY motif also interacts with other components of the exocytosis machinery (e.g. Sec1), thereby causing the observed phenotypes, Sec3 mutagenesis of the NPY motif-binding site would be required. *

__Response: __It would be a good idea to generate reverse mutants on Sec3. However, the pocket on Sec3 bound by the NPY motifs of Sso2 is mostly hydrophobic and contains many semi-buried residues that are in close contact with other residues in the hydrophobic core of structure (including L78, Y82, I109, V112, V208, etc.; see Fig. S3D, E) and thus essential in maintaining the folding of Sec3. Making mutations on these residues would destabilize the folding of Sec3. This was why we have not done this as suggested by the reviewer.

*- The authors suggest that the NPY-peptide binding contributes to the initial interaction/recruitment of Sso2 to the exocytosis site, defined by the localization of Sec3 (exocyst). Further data sustaining this concept/hypothesis could improve the impact of the manuscript. Thus, an experiment analyzing the co-distribution of the Sec3 with Sso2 would directly support the authors' conclusion. (In Figure 7, the authors already show the highly polarized distribution of Sec3-3xGFP.) The M7 mutant could impact the distribution of Sso2. In addition, it would be helpful to determine to which degree the Sso2 NPY - Sec3 PH domain interaction increases the overall affinity of Sso2 for the Sec3 PH domain; e.g. comparison of the binding of Sso2 (1-270) wt and M7 to Sec3 PH domain using ITC. *

Responses:

• We greatly value the reviewer’s suggestion. For the suggestion to investigate how the M7 mutant affects the co-distribution of Sso2 with Sec3 in yeast, we have tried a variety of conditions with both the original serum and affinity purified Sso antibodies. In neither case did we see a clear concentration at sites where we would expect to see Sec3, such as the tips of small buds. We were able to see some detectable concentration of HA-tagged Sso2 in small buds using anti-HA Ab, but it would be difficult to tag the M7 mutant at the same site since it is so close to the M7 mutation. We are also worried that the tag might interfere with Sec3 binding due to the proximity. Given the lack of detectable concentration of WT Sso2, it would not be possible to see a loss of localization in M7.
• For the suggestion to check the binding of Sec3 with either the WT or M7 mutant of Sso2 (aa1-270), we have generated M7 mutant within the same fragment of Sso2 as the WT (i.e. aa1-270) and carefully checked how this M7 mutant affects the interaction of Sso2 with the Sec3 PH domain using three independent methods. Our ITC data show that WT Sso2 bound Sec3 very robustly, with a Kd of approximately 2 µM (Fig. 8C). Surprisingly, however, the M7 mutant of Sso2 (aa1-270) completely abolished its interaction with Sec3 (Fig. 8D). To further verify this observation, we carried out electrophoresis mobility shift assays (EMSA) and size-exclusion chromatography (SEC). Our EMSA data on a native PAGE gel shows that WT Sso2 (aa1-270) bound Sec3, whereas the M7 mutant did not (Fig. S5A, B). Similarly, our SEC data demonstrate that Sec3 was co-eluted with WT Sso2 in the higher molecular weight peak; in contrast, Sec3 and the M7 mutant of Sso2 (aa1-270) were eluted in separate peaks and no stable complex of the two was formed (Fig. S5C, D). All these new data confirm that the NPY motifs play an essential role in maintaining the stable interaction between Sso2 and Sec3, which would explain why the M7 mutant gave such dramatic phenotype in vivo (Fig. 4B-E; Fig. 5D-F; Fig. 6D, E). *Minor point: In the discussion, the authors should mention to which degree the NPY binding site within Sec3 is accessible for / occupied by other known exocyst components, or PI(4,5)P2, etc. *

Response: __Thank you for the suggestion. A new diagram has been added to __Fig. 9E to compare the structures of the previously reported Sec3/Rho1 complex and the Sso2/Sec3 complex determined by us. It shows that the NPY binding site on Sec3 is on the opposite side of the membrane-binding surface patch. The NPY binding site is also far away from the Rho1 interacting site on Sec3 and thus does not interfere with Rho1 binding either.

*Reviewer #1 (Significance (Required)):

The manuscript significantly contributes to our understanding of how the vesicle tethering machinery interacts and coordinates the assembly of the membrane fusion machinery and will be of broad interest in the field of membrane trafficking. I am not an expert in X-ray crystallography. *

__Response: __We sincerely appreciate this reviewer’s positive feedbacks.

***Referees cross-commenting**

I agree with the comments of the other reviewer. It would be nice to show the effect of the M7 mutant in a reconstituted liposome fusion assay, but as already mentioned this may require an additional collaboration. Whether the relatively weak Sec3 - NPY interaction can be resolved in the liposome fusion assay needs to be shown.*

__Response: __Please check our detailed answer to the other reviewer’s question about this.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): * The manuscript of Peer et al. Describe the structural characterization of the interaction of the syntaxin-like Sso2 protein with the exocyst subunit Sec3. The authors identify here a dual NPY motif at the N-terminal part of Sso2 that binds to Sec3 and thus confers functionality. Using x-ray crystallography, they show a nearly full-length Sso2 in complex with Sec3, which reveals how Sso2 binds to Sec3. Subsequent mutagenesis shows that both NPY motifs act together in binding, and are both required for functionality in vivo, using established assays in localization of exocyst subunits, secretion assays and growth tests. Their data suggest an overall model how Sso2 is efficiently recruited by exocyst to promote vesicle secretion.

This is__ an overall very complete and clear manuscript__, where the authors nicely demonstrate, how the two NPY motifs both contribute to efficient Sso2 interaction with Sec3. Their data further show that each motif alone can contribute to function, whereas loss of both motifs (the M7 mutant) result in deficient binding. Likewise, their established assays to determine cellular importance of the NPY motifs in Sso2 show that trafficking and localization in the secretory pathway is strongly impaired in the mutant. I only have a few questions and suggestions. *

__Response: __Thank you for the positive feedback.

*1. The authors present in Figure 4 the mutants. I recommend to show the alignment of the mutants (M5,M6,M7) similar to panel A in Figure S4 here to orient the reader. They could also be listed in Figure 3, since the authors have here the sequences. *

Response: __Alignment of M5-M7 has been added in __Fig. 4A as suggested. Thank you.

2. The authors previously showed that Sso2 mutants affect the Sec3 driven assembly and also the fusion. I am wondering if they have the tools ready to also conduct this assay with their M7 mutant, which has the strongest defect. I am aware that this may be challenging if the tools are not established here as in the previous collaboration (Yue et al., 2017). It may provide additional information on the functional crosstalk.

Responses:

• Thank you for the suggestion. However, we do not think it is necessary to perform such assay based on our new results. As shown in 8C&D and Fig. S5, we found that the M7 mutant of Sso2 (aa1-270) completely abolished its interaction with Sec3, which is in contrast to the robust interaction between the WT Sso2 (aa1-270) and Sec3. Therefore, we expect that the M7 mutant would fail to accelerate liposome fusion in the same way as we had previously seen for the WT Sso2.
• On the other hand, we have to admit that to perform such assay would indeed be challenging for us as the PhD student who had carried out the in vitro liposome fusion assay has left our previous collaborator’s lab and it would take quite a while to re-establish the assay in our own group and to optimize various parameters in that assay. *3. Along the same line, it would be good if the authors show that the mutation also impairs the interaction of Sec3 and Sso2 in vivo. *

Response: __We appreciate the reviewer’s suggestion and have carried out co-immunoprecipitation of Sec3-3×Flag and Sso2 from yeast extract to find out how the M7 mutant affects Sso2’s interaction with Sec3 (__Fig. S6). Our results show that in contrast to the clear signal of WT Sso2 pulled down by Sec3-3×Flag, the pull-down band for the M7 mutant was much weaker and at a similar level to the negative control. This is consistent with what we saw in our in vitro binding assays (Fig. 8D; Fig. S5).

*4. I really like the similarity of the different Munc18-Syntaxin interactions and the Sec3-Sso2 interaction. Do the authors think that Sec3 is an ancestral fragment of a Sec1 like protein, which just maintained this interaction? *

__Response: __This is a very interesting idea. However, it seems too speculative to us to draw such conclusion. It could also be due to co-evolution in function for Sec3 to use a simpler structure (i.e. PH domain) to mimic syntaxin binding of SM proteins and to employ the extra “add-on” NPY motifs as a handle to facilitate and regulate their interaction.

1. *Small mistake in the discussionResponses: "plasmas membrane" *

__Response: __This has been corrected. Thank you.

*Reviewer #2 (Significance (Required)): Important advance in our understanding of Exocyst function, which deserves publication. I only had minor issues that can be addressed quickly. *

__Response: __We sincerely appreciate the reviewer’s positive feedbacks and constructive suggestions.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The manuscript of Peer et al. Describe the structural characterization of the interaction of the syntaxin-like Sso2 protein with the exocyst subunit Sec3. The authors identify here a dual NPY motif at the N-terminal part of Sso2 that binds to Sec3 and thus confers functionality. Using x-ray crystallography, they show a nearly full-length Sso2 in complex with Sec3, which reveals how Sso2 binds to Sec3. Subsequent mutagenesis shows that both NPY motifs act together in binding, and are both required for functionality in vivo, using established assays in localization of exocyst subunits, secretion assays and growth tests. Their data suggest an overall model how Sso2 is efficiently recruited by exocyst to promote vesicle secretion.

This is an overall very complete and clear manuscript, where the authors nicely demonstrate, how the two NPY motifs both contribute to efficient Sso2 interaction with Sec3. Their data further show that each motif alone can contribute to function, whereas loss of both motifs (the M7 mutant) result in deficient binding. Likewise, their established assays to determine cellular importance of the NPY motifs in Sso2 show that trafficking and localization in the secretory pathway is strongly impaired in the mutant. I only have a few questions and suggestions.

1. The authors present in Figure 4 the mutants. I recommend to show the alignment of the mutants (M5,M6,M7) similar to panel A in Figure S4 here to orient the reader. They could also be listed in Figure 3, since the authors have here the sequences.
2. The authors previously showed that Sso2 mutants affect the Sec3 driven assembly and also the fusion. I am wondering if they have the tools ready to also conduct this assay with their M7 mutant, which has the strongest defect. I am aware that this may be challenging if the tools are not established here as in the previous collaboration (Yue et al., 2017). It may provide additional information on the functional crosstalk.
3. Along the same line, it would be good if the authors show that the mutation also impairs the interaction of Sec3 and Sso2 in vivo.
4. I really like the similarity of the different Munc18-Syntaxin interactions and the Sec3-Sso2 interaction. Do the authors think that Sec3 is an ancestral fragment of a Sec1 like protein, which just maintained this interaction?
5. Small mistake in the discussion: "plasmas membrane"

Significance

Important advance in our understanding of Exocyst function, which deserves publication. I only had minor issues that can be addressed quickly.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Using the entire cytoplasmic domain of Sso2 and protein crystallization, Peer and colleagues show that two N-terminal peptides (NPY) of Sso2 synergistically interact with the Sec3 PH domain. This interaction provides an additional low affinity binding site to the previously published interface between the Sso2 four-helix bundle and the PH domain. Mutagenesis, in particular of both NPY motifs, results in reduced cell growth, in the accumulation of transport vesicles at the budding site, and in decreased secretion of invertase and Bgl2. The paper is well written, the data are convincing and the characterization of these novel peptide interaction sites clearly advances the field. Although, the exact role of the Sec3 NPY - Sec3 interaction still needs to be established, the overall functional relevance is apparent and thus the paper could be published with minor changes.

Nevertheless, the authors may consider to address the following issues to improve the manuscript.

• To strictly exclude the possibility that the Sso2 NPY motif also interacts with other components of the exocytosis machinery (e.g. Sec1), thereby causing the observed phenotypes, Sec3 mutagenesis of the NPY motif-binding site would be required.
• The authors suggest that the NPY-peptide binding contributes to the initial interaction/recruitment of Sso2 to the exocytosis site, defined by the localization of Sec3 (exocyst). Further data sustaining this concept/hypothesis could improve the impact of the manuscript. Thus, an experiment analyzing the co-distribution of the Sec3 with Sso2 would directly support the authors' conclusion. (In Figure 7, the authors already show the highly polarized distribution of Sec3-3xGFP.) The M7 mutant could impact the distribution of Sso2. In addition, it would be helpful to determine to which degree the Sso2 NPY - Sec3 PH domain interaction increases the overall affinity of Sso2 for the Sec3 PH domain; e.g. comparison of the binding of Sso2 (1-270) wt and M7 to Sec3 PH domain using ITC.

Minor point:

In the discussion, the authors should mention to which degree the NPY binding site within Sec3 is accessible for / occupied by other known exocyst components, or PI(4,5)P2, etc.

Significance

The manuscript significantly contributes to our understanding of how the vesicle tethering machinery interacts and coordinates the assembly of the membrane fusion machinery and will be of broad interest in the field of membrane trafficking. I am not an expert in X-ray crystallography.

Referees cross-commenting

I agree with the comments of the other reviewer. It would be nice to show the effect of the M7 mutant in a reconstituted liposome fusion assay, but as already mentioned this may require an additional collaboration. Whether the relatively weak Sec3 - NPY interaction can be resolved in the liposome fusion assay needs to be shown.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

This study is interesting on finding that necroptosis may regulate axonal degeneration in the dentate gyrus, which led to the loss of synaptic transmission and plasticity and impaired the performance of mice in water maze. Genetic ablation of MLKL, a key factor for necroptotic pathway, or pharmacological inhibition of necroptosis with GSK'872, the inhibitor to another necroptotic key factor RIPK3, prevented mice from axonal degeneration, synapse dysfunction, and memory loss. They also tested long term potentiation (LTP) and found LTP that was disrupted in aged mice, was rescued by MLKL knockout or GSK'872 treatments. The authors further compared normally aged mice (more than 20 months old) with aged MLKL-knockout mice or aged mice with GSK'872 treatments for altered proteins by single-shot label-free mass spectrometry, and discovered that in 7000 detected proteins, 2516 proteins were increased while 2307 were decreased in the aging hippocampus. They carried out bioinformatic analysis and clustered these proteins for biofunctions of synaptic mechanisms, senescence, etc. With the bioinformatic analysis, they further examined cell senescence by SA-βgalactosidase (SA-βgal) staining and concluded that the cellular senescence was also rescued by necroptosis inhibition.

Although it is an exciting idea that inhibiting necroptosis may be a potential approach to combating aging and rejuvenating the brain, I have many of concerns about the reliability and consistency of the data that did not show strong supports to the conclusion.

Major comments:

1. The authors used axonal degeneration as a major readout for brain aging. However, the conclusion of axonal degeneration was simply based on immunostaining. These staining results are not consistent in different parts, and their conclusion is hard to be supported by the representative images. It is not convincing that axonal integrity was altered as concluded by the authors as shown in the representative images of Fig. 1e, Fig. 2d, Fig. 3a, as well as those in the supplementary figures. Electron microscopy and other convincing means are necessary.

We agree with the reviewer, we are performing new staining and incorporating new imaging techniques, including confocal microscopy to better define axons in different regions of the hippocampus. We propose to use Light Sheet Microscopy in clarified hippocampus in order to perform 3D analyses of the axons in the entire hippocampus (ongoing experiments). The Light Sheet microscope is currently available in our Center and we have settled the clarity protocol in brain tissue, particularly in the hippocampus (see pictures below of an hippocampi before and after the clarification protocol).

As suggested by the reviewer, electron microscopy could be a very good addition, nevertheless this technique is not implemented in the laboratory at the moment. Nevertheless, we have initiated conversations with a possible collaborator in the UK to explore the possibility to perform 3D reconstructions at the EM level for a future publication.

Similarly, they tested the involvement of necroptosis also simply by immunostaining of necroptotic key factors. These staining results were not consistent in different figures. Western blotting is better for the examination of protein level changes of MLKL, pMLKL, RIPK3, and pRIPK3.

We will perform western blot for pMLKL and pRIPK3 in the different conditions, including different ages, aged Mlkl-KO and aged GSK-treated mice.

It is very confusing which kind of neurons and which circuit is influenced by necroptosis. As emphasized in the description for Fig. 1b in Line 91, axonal degeneration was restricted to the hilus of dentate gyrus (revealed by Fluoro Jade C staining). However, synaptic transmission (Fig. 4a-f, Fig. 6a-e) and plasticity (Fig. 8c,d) were tested for CA3-CA1 projection, instead of DG-CA3 projection. Moreover, cellular senescence, as detected by SA-beta-gal in Fig. S11, was not in granule cells or hilar cells at the dentate gyrus.

We agree with the reviewer. Considering his comments, we propose to extend our imaging analysis of axonal degeneration and necroptosis activation to the entire hippocampus, including CA1-CA3 subfields. We consider that recording CA1-CA3 circuit represents and overall response of the hippocampus, but also this subfield contains most of the axonal inputs of this brain region. We will now analyze by confocal microscopy Schaffer collaterals axons which correspond to those axons given off by CA3 pyramidal cells that project to CA1. We already showed by immunohistochemistry in Figure 2f that pMLKL levels are increased in Schaffer collaterals axons in aged mice, but we will perform 3D analysis of pMLKL in NF positive axons by immunofluorescence in this region.

Axonal tracts for DG-CA3 projection were from granule cells at DG. However, pMLKL was found to be increased in hilar cells. In contrast, the authors concluded that pMLKL in granule cells at DG did not exhibit difference during aging (Line 115). The fact is pMLKL can be easily visualized in many cells including granule cells in adult mice that were not aged (Fig.2a, Fig. S1). Moreover, the signal of pMLKL in granule cells can be seen to be increased in aged mice, although they overlapped DAPI on it. These facts lead to a doubt that their immunostaining of pMLKL was not specific, or they did not analyze the signal accurately.

As the reviewer remarked, we did not observe an increase in pMLKL levels in the granular cell layer of the DG (see the quantification below). Several reports have demonstrated that necroptosis is an axonal-self destruction program that is not necessarily involved in the death of the whole neuron, which suggests that pMLKL could be detected in aged axons without showing changes in the soma. We will include a paragraph in the discussion section to address this issue. By contrast, we did observe increased pMLKL in hilar cells, CA3 neurons and Schaffer collateral axons, as we demonstrated both by immunofluorescence and immunohistochemistry in Fig 2. In order to clarify the reviewer’s doubts regarding our images, we will include the same image presented in Fig 2, showing the pMLKL signal without DAPI. We will also include the pMLKL channel alone in main figures. Moreover, we believe that the new confocal analyses that we are currently performing will help us to better define necroptosis activation and axonal colocalization in the different subfields of the hippocampus.

The pattern of non-pNF staining in Fig. 1c is not consistent with that in Fig. 3d, Fig. 5a.

We will repeat these immunostainings and analyze the staining pattern of the non-pNF antibody to give a clear response to this comment, improving the extent of the analysis.

Minor comments:

For Fig. 3d,e and Fig. S4, GFAP staining is also suggested since astrocytes are the other glia that are easily reactive to inflammatory pathogenic conditions.

This is an excellent suggestion. We are currently performing GFAP staining to establish astrocyte activation in the different conditions (aged wt, MLKL KO, and GSK intervention compared to vehicle in aged animals). This data will be included in a revised manuscript.

Why was there no colocalization of pMLKL with NF in degenerating axonal tracts?

We are performing confocal studies to study colocalization of these proteins. Indeed, colocalization was found but a better analysis is needed to demonstrate this, which will be included in a new version of the manuscript.

Fig. 3a showed no hilar cells stained for pMLKL in aged mice, which is different from that shown in Fig. 2b.

We have reviewed all the available images and there are some variabilities in aged mice that explain different patterns of pMLKL staining. This is not surprising considering the intrinsic heterogeneity of the aging process. Some mice show more axonal staining while other present clear staining in cell layer (soma) and axons. In a revised manuscript, we will include representative images of the different patterns observed.

Images in Fig. S4 lack labels.

Label on the figure indicates ‘Iba1’, but the color used does not allow to get a good view. Label will be changed to increase the contrast.

Fig. S6, pRIPK3 staining pattern is different from that of pMLKL. They were not activated in the same cells?

We observed pRIPK3 staining in the hilar cells of the hippocampus. We are currently performing double immunostaining against pMLKL and pRIPK3 to determine whether they colocalize within the same cell-type in the hippocampus.

Fig. S7, pMLKL staining pattern is different from that in Fig. 2a,f?

As we have detailed in point 8, this could be explained by the variability of the pMLKL staining in aged mice. In a revised manuscript we will review these images and include a supplementary image with the different staining patters found.

Resolution for signaling pathway annotations in Fig. 8, Fig. S12, Fig. S13, and Fig. S14, is too low.

We will increase resolution for this data. In addition, we will include the original images in our final version to avoid loss of quality during file conversion to PDF.

The titles for Table S1 and S2 should be on the top of the tables.

This has been corrected.

Reviewer #1 (Significance (Required)):

The finding that systemic administration of GSK'872 improved synaptic plasticity and mouse performances in water maze is exciting, indicating a potential medicine for brain rejuvenation.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

The authors (in the research group of Filipe Court in Chile) previously studied the contributions of the necroptosis pathway to the degeneration of axons following nerve damage. In this paper, the authors ask whether necroptosis pathway contributes to axon loss, inflammation and cognitive decline in naturally aging mice. The study presents some promising observations that suggest necroptosis is activated in the brain of aged mice and that inhibiting necroptosis through genetics or pharmacology can rescue some cognitive defects in aged mice. The potential implications are exciting, however the scope of what is presented thus far is preliminary. I'll list below several issues with both the experimental design and the presentation of data that strongly diminish from the potential conclusions and significance of this work.

Major comments:

1) The n is limited to 3 mice per condition in most of the experiments in this study, and it is not mentioned what sex the animals were. If data was pooled from both sexes than the n is not large enough to take into account potential sex differences. The absence of discussion of sex in the methods weakens my trust in the experimental design.

WT mice of different ages are all male, purchased from Jackson Laboratory and shipped to Chile (USA). In a revised version, we will specify the sex of the mice in the methods section of the manuscript. This also applies for the group of mice used to pharmacologically inhibit necroptosis with GSK’872, which were also purchased from Jackson Labs. Regarding Mlkl-KO and their WT littermates we used both sexes. We will include a table detailing all the animals used and their age and sex in a revised manuscript. Moreover, as the reviewer suggested, we are currently increasing the n for morphological analysis from 3 to 5, which will be included in the new version of this work. For the behavioral experiments, we have used large group of animals. All details about this and sex of the KO animals will be included in a table with the raw data files.

2)The studies are not thorough. For instance, there is only one age presented for the mlkl-KO mice. Do these mice still age-dependent changes in axon degeneration or inflammation markers?

We have the data for other ages in the Mlkl-KO animals, which will be included in the revised manuscript.

The strain background of the mlkl-KO mice is not mentioned and it is not clear what steps (if any) have been taken to control for strain background and rearing conditions. For instance, WT mice of different ages were purchased from Jackson labs while mlkl-KO mice were apparently bred in house.

We will include this information in the revised manuscript. Mlkl knockout mice (Mlkl-KO) were kindly provided by Dr Douglas Green (St. Jude Children’s Research Hospital, Memphis, TN, USA). As we have described in the manuscript, the details regarding Mlkl-KO mice are cited in reference 71, which details the generation of Mlkl deficient mice and background. Age-matched control mice correspond to WT mice obtained by Mlkl heterozygous breeding in our animal facility. In addition, we systemically check genotype of mice (PCR-based genotyping protocol is now included in the method section of our manuscript).

Reference 71. Murphy, J. M. et al. The pseudokinase MLKL mediates necroptosis via a molecular switch mechanism. Immunity 39, 443–453 (2013).

3) For the inhibitor studies, use of littermates for the vehicle control would have been feasible, but it is not mentioned if this was done.

As we detailed in point 1, we have used Jackson mice for the inhibitor studies. Mice were selected randomly for both vehicle and GSK’872 groups. We are currently increasing the number of mice (10 more animals per condition) for behavioral and morphological analyses in order to control for eventual variations.

4) The Morris water tank test is a stressful condition for aged mice. Differences in performance could be confounded by differences in swimming ability and potentially stress response. Its a pity that this is the only behavioral test shown, since there are many others (eg Y-maze or novel object recognition) that would be appropriate for the questions posed.

We evaluated swimming ability of mice and we did not observe differences between WT and KO mice of same age (see figure below), as we discussed in the manuscript. However, we agree with the reviewer that the use of other behavioral test to evaluate memory in aged mice without a stressful condition will improve the quality of our work and will help to support our data. Therefore, we will perform Y-maze and NOR in aged MLKL WT and KO mice as well as in aged animals treated with GSK-872.

Minor comments:

5) It is striking that some very relevant citations are absent. For instance, PMID: 34515928 (october 2021) noted a compelling increase in necroptosis markers in the aging CNS, and effects on neuroinflammation in aging mice. These conclusions have some overlap with conclusions in this study. The other study did not address contributions of necroptosis to cognitive or synaptic defects, so the current study still has some novelty, and is supported by other work that should be cited.

This article was included in the introduction and discussion section of the original manuscript. As there are two version of the manuscript uploaded in bioRxiv file, is possible that the reviewer is referring to the first version (November 11). In fact, the second version (April 18) was uploaded to specifically include this reference.

https://www.biorxiv.org/content/10.1101/2021.11.10.468052v2.full

6) The methods used for analysis need to be described with more detail and rigor. For instance, how many sections are analyzed and where and how? How is normalization done and how is it determined that analogous regions are compared across animals and conditions? Likewise, the method for scoring axonal fragmentation needs to be described, and clarified where in the brain this is analyzed.

We thank the reviewer for this suggestion. We will include a detailed description of the analysis performed, including the details referred by the reviewer and the new analyses.

7) There are numerous typos, including impactful ones (such as legend of figure 1 where 'old' mice are 12-25 months).

We will check and correct for typos in a revised version of the manuscript.

8) Figure 8A is not legible. Perhaps the findings can be highlighted in a merged form on a single pathway cartoon.

We will change the image as reviewer suggests. Moreover, we will include original images with better quality as raw data.

Reviewer #2 (Significance (Required)):

The investigation of the role of necroptosis in the CNS during aging is of high impact and has translational relevance, since necroptosis is a viable pathway for pharmaceutical targeting.

The idea that it contributes to axonal degeneration and/or synaptic changes in the aging brain is novel and under-explored.

• *

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors (in the research group of Filipe Court in Chile) previously studied the contributions of the necroptosis pathway to the degeneration of axons following nerve damage. In this paper, the authors ask whether necroptosis pathway contributes to axon loss, inflammation and cognitive decline in naturally aging mice. The study presents some promising observations that suggest necroptosis is activated in the brain of aged mice and that inhibiting necroptosis through genetics or pharmacology can rescue some cognitive defects in aged mice. The potential implications are exciting, however the scope of what is presented thus far is preliminary. I'll list below several issues with both the experimental design and the presentation of data that strongly diminish from the potential conclusions and significance of this work.

Major comments:

1) The n is limited to 3 mice per condition in most of the experiments in this study, and it is not mentioned what sex the animals were. If data was pooled from both sexes than the n is not large enough to take into account potential sex differences. The absence of discussion of sex in the methods weakens my trust in the experimental design.

2) The studies are not thorough. For instance, there is only one age presented for the mlkl-KO mice. Do these mice still age-dependent changes in axon degeneration or inflammation markers? The strain background of the mlkl-KO mice is not mentioned and it is not clear what steps (if any) have been taken to control for strain background and rearing conditions. For instance, WT mice of different ages were purchased from Jackson labs while mlkl-KO mice were apparently bred in house.

3) For the inhibitor studies, use of littermates for the vehicle control would have been feasible, but it is not mentioned if this was done.

4) The Morris water tank test is a stressful condition for aged mice. Differences in performance could be confounded by differences in swimming ability and potentially stress response. Its a pity that this is the only behavioral test shown, since there are many others (eg Y-maze or novel object recognition) that would be appropriate for the questions posed.

Minor comments:

5) It is striking that some very relevant citations are absent. For instance, PMID: 34515928 (october 2021) noted a compelling increase in necroptosis markers in the aging CNS, and effects on neuroinflammation in aging mice. These conclusions have some overlap with conclusions in this study. The other study did not address contributions of necroptosis to cognitive or synaptic defects, so the current study still has some novelty, and is supported by other work that should be cited.

6) The methods used for analysis need to be described with more detail and rigor. For instance, how many sections are analyzed and where and how? How is normalization done and how is it determined that analogous regions are compared across animals and conditions? Likewise, the method for scoring axonal fragmentation needs to be described, and clarified where in the brain this is analyzed.

7) There are numerous typos, including impactful ones (such as legend of figure 1 where 'old' mice are 12-25 months).

8) Figure 8A is not legible. Perhaps the findings can be highlighted in a merged form on a single pathway cartoon.

Significance

The investigation of the role of necroptosis in the CNS during aging is of high impact and has translational relevance, since necroptosis is a viable pathway for pharmaceutical targeting.

The idea that it contributes to axonal degeneration and/or synaptic changes in the aging brain is novel and under-explored.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

This study is interesting on finding that necroptosis may regulate axonal degeneration in the dentate gyrus, which led to the loss of synaptic transmission and plasticity, and impaired the performance of mice in water maze. Genetic ablation of MLKL, a key factor for necroptotic pathway, or pharmacological inhibition of necroptosis with GSK'872, the inhibitor to another necroptotic key factor RIPK3, prevented mice from axonal degeneration, synapse dysfunction, and memory loss. They also tested long term potentiation (LTP) and found LTP that was disrupted in aged mice, was rescued by MLKL knockout or GSK'872 treatments. The authors further compared normally aged mice (more than 20 months old) with aged MLKL-knockout mice or aged mice with GSK'872 treatments for altered proteins by single-shot label-free mass spectrometry, and discovered that in 7000 detected proteins, 2516 proteins were increased while 2307 were decreased in the aging hippocampus. They carried out bioinformatic analysis and clustered these proteins for biofunctions of synaptic mechanisms, senescence, etc.. With the bioinformatic analysis, they further examined cell senescence by SA-βgalactosidase (SA-βgal) staining, and concluded that the cellular senescence was also rescued by necroptosis inhibition.

Although it is an exciting idea that inhibiting necroptosis may be a potential approach to combating aging and rejuvenating the brain, I have many of concerns about the reliability and consistency of the data that did not show strong supports to the conclusion.

Major comments:

1. The authors used axonal degeneration as a major readout for brain aging. However, the conclusion of axonal degeneration was simply based on immunostaining. These staining results are not consistent in different parts, and their conclusion is hard to be supported by the representative images. It is not convincing that axonal integrity was altered as concluded by the authors as shown in the representative images of Fig. 1e, Fig. 2d, Fig. 3a, as well as those in the supplementary figures. Electromicroscopy and other convincing means are necessary.
2. Similarly, they tested the involvement of necroptosis also simply by immunostaining of necroptotic key factors. These staining results were not consistent in different figures. Western blotting is better for the examination of protein level changes of MLKL, pMLKL, RIPK3, and pRIPK3.
3. It is very confusing which kind of neurons and which circuit is influenced by necroptosis. As emphasized in the description for Fig. 1b in Line 91, axonal degeneration was restricted to the hilus of dentate gyrus (revealed by Fluoro Jade C staining). However, synaptic transmission (Fig. 4a-f, Fig. 6a-e) and plasticity (Fig. 8c,d) were tested for CA3-CA1 projection, instead of DG-CA3 projection. Moreover, cellular senescence, as detected by SA-beta-gal in Fig. S11, was not in granule cells or hilar cells at the dentate gyrus.
4. Axonal tracts for DG-CA3 projection were from granule cells at DG. However, pMLKL was found to be increased in hilar cells. In contrast, the authors concluded that pMLKL in granule cells at DG did not exhibit difference during aging (Line 115). The fact is pMLKL can be easily visualized in many cells including granule cells in adult mice that were not aged (Fig.2a, Fig. S1). Moreover, the signal of pMLKL in granule cells can be seen to be increased in aged mice, although they overlapped DAPI on it. These facts lead to a doubt that their immunostaining of pMLKL was not specific, or they did not analyze the signal accurately.
5. The pattern of non-pNF staining in Fig. 1c is not consistent with that in Fig. 3d, Fig. 5a.

Minor comments:

1. For Fig. 3d,e and Fig. S4, GFAP staining is also suggested since astrocytes are the other glia that are easily reactive to inflammatory pathogenic conditions.
2. Why was there no colocalization of pMLKL with NF in degenerating axonal tracts?
3. Fig. 3a showed no hilar cells stained for pMLKL in aged mice, which is different from that shown in Fig. 2b.
4. Images in Fig. S4 lack labels.
5. Fig. S6, pRIPK3 staining pattern is different from that of pMLKL. They were not activated in the same cells?
6. Fig. S7, pMLKL staining pattern is different from that in Fig. 2a,f?
7. Resolution for signaling pathway annotations in Fig. 8, Fig. S12, Fig. S13, and Fig. S14, is too low.
8. The titles for Table S1 and S2 should be on the top of the tables.

Significance

The finding that systemic administration of GSK'872 improved synaptic plasticity and mouse performances in water maze is exciting, indicating a potential medicine for brain rejuvenation.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2021-01158

Doi preprint: https://doi.org/10.1101/2021.11.16.468835

Corresponding author(s): Salah, MECHERI

[Please use this template only if the submitted manuscript should be considered by the affiliate journal as a full revision in response to the points raised by the reviewers.

If you wish to submit a preliminary revision with a revision plan, please use our "Revision Plan" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

2. Point-by-point description of the revisions

This section is mandatory. Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

__Whole sporozoite vaccines confer sterilizing protection against Plasmodium infection. However, further improvements of whole sporozoite vaccines is needed and requires a thorough understanding of the immune processes that mediate protection and the deployment of novel strategies further augment protective immunity while limiting the impact of factors that are detrimental to protection. Work from the Mecheri laboratory and others had previously established that IL-6 signaling plays a critical role in the immune response to a liver stage infection; engagement of IL-6 signaling promotes the initial control of a liver stage infection and enhances the protective adaptive immune response. Given this potent protective role for IL-6, Belhimeur and colleagues design a parasite strain in rodent malaria parasites that encodes and secrete murine IL-6 during liver stage infection. They show that upon infection of wildtype mice, these transgenic parasites i) are unable to transition to blood stage infection, ii) produce Il-6 and iii) induce a durable adaptive immune response that can protect against sporozoite challenge. This study is novel and intriguing. However, a superficial analysis of the transgenic parasite strain, an incomplete analysis of the immune response to infection and the lack of data regarding the possibility of IL-6 mediated immunopathology have dampened this reviewer's enthusiasm for the work.

**Major Concerns:** __

1)The data in Figure 3b-3d clearly indicate that the IL-6 encoding transgenic parasites exhibit a defect in parasite development within HepG2 cells that is maintained in vivo. The authors propose that an arrest of these parasites in the liver stage precludes their transition to blood stage infection and that this arrest is dependent on IL-6 signaling. To better support that claim the authors should:

a.Better characterize in vivo liver stage arrest using infected liver tissue analysis with immunofluorescence microscopy to determine when and how precisely IL-6 transgenic parasites are impacted in development.

Done. New data in figure 3B, C, D

b.Determine if arrested development of IL-6 transgenic parasites is truly dependent on IL-6 signaling using antibody blockade of IL-6 signaling and mice with genetic defects in IL-6 signaling.

Experiments were done using anti-IL-6 receptor blocking antibodies, but did not work. This was commented in the text and shown in Supplementary Fig 2 .

2)The authors claim that IL-6 production and secretion into the liver tissue augments the adaptive immune response to liver stage infection. This in turn results in a durable adaptive immune responses that protect against infection. However, the mechanistic underpinning of IL-6 signaling in the liver that is induced by their transgenic parasites and the impact on adaptive immune responses is poorly characterized:

a.There is no evidence that the protective adaptive immune response induced by IL-6 trangenic parasite infection is dependent on IL-6 signaling. Is superior protection and immunogenicity lost in IL-6 signaling deficient animals that are infected with IL-6 transgenic parasites?

Not addressed but the point is that IL-6 leads to attenuation.

b.What elements of the adaptive immune response are impacted? One can imagine that IL-6 mediated killing of infected hepatocytes might introduce more parasite antigen that can be acquired by antigen presenting cells, or that IL-6 mediated pro-inflammatory signaling might regulate the maturation of antigen presenting cells, increased differentiation of helper T cells, the downregulation of regulatory T cell function and frequency and/or the differentiation of effector CD8 T cells into long-lived hepatic memory CD8 T cells. The authors should conduct a more comprehensive analysis of how parasite-encoded IL-6 impacts adaptive immunity.

Done. An extensive analysis of CD4 and CD8 phenotype and status of activation is represented in Fig 9.

3)While IL-6 transgenic parasites induce a potent and durable adaptive immune response, the authors should show how this compares to published whole sporozoite immunizations. The authors should determine if immunization with IL-6 transgenic parasites is superior to for example immunization with radiation-attenuated sporozoites and generically attenuated sporozoites.

It not the point. The work presented here emphasizes the proof of concept that the proposed new strategy works. Follow up studies will compare this model to previous ones.

4) IL-6 signaling is a major player in inflammatory diseases and the induction of immunopathology. As such the authors should carefully examine the duration and magnitude of IL-6 protein production in the liver, and serum after IL-6 Tg parasite infection and determine if IL-6 signaling promotes liver immunopathology.

Not done but this point was discussed in the text. Also, we made it clear in the material and methods section that the way the construct was made, i.e the IL-6 production is time-frame restricted to the first 48h of liver infection, precisely because of the expression of IL-6 gene is under the control of LISP-2 promoter. Therefore there is no persistence of IL-6 production by liver stage parasites.

Reviewer #1 (Significance (Required)):

The paper is reporting a novel strategy to generate a whole sporozoite vaccine. Expression of IL6 in a transgenic parasite. This could be a significant contribution to the field if additional experiments as outlined in the critique are conducted.The work might also inform vaccine design for other pathogens.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

The manuscript describes the construction of a Plasmodium berghei that expresses murine interleukin-6 in exoerythrocytic (liver stage) parasites and the analysis of mice infected with sporozoites of this parasite line. They find that such parasites do not complete development in liver cells and therefore do not produce subsequent infection in red blood cells. The ability of prior infection with these parasites on the ability of the host to resist both wild type and heterologous species challenge is then examined.

The key assumption that underlies the study is that the observed phenotypes result from parasite expression of bioactive IL-6 that functions to modulate the immune system. Other explanations are not considered, for example the over-expression of secreted IL-6 may prevent the complete maturation of the intracellular parasite by clogging up the parasite secretory pathway. The authors use the 'wild type' parasite as the control but not only does the wild type not express IL-6 it also does not express the human DHFR gene used as a selection system. A much better control parasite would be one that expresses a non-bioactive IL-6 so that the potential effects on parasite maturation can be differentiated from those on the mouse immune system. Another control to be considered would be comparison with a genetically attenuated parasite with a block in late stage development, and which does not produce a host cytokine.

Interesting comment but key novel result is that co-infection studies show reversed phenotype of IL-6 transgenic parasites, likely due to counteracting Of IL-6 effect by Wild type parasites (Supplementary Fig 1)

Another assumption is that IL-6 is secreted from the infected liver cell and mediates its effects, presumably by binding to its cell surface receptor. The expectation of Il-6 secretion from the parasite is that it would accumulate in the parasitophorous vacuole - how would it get out of the infected host cell? While evidence is provided of IL-6 in the in vitro culture supernatant of infected cells - this might arise from damaged cells in rather artificial conditions. Have the authors considered doing the experiment of concurrent mouse infection with both wild type and recombinant parasites? If the mechanism of parasite killing in infected liver cells is as proposed, then a reduction of wild type parasites in the subsequent asexual blood stage would be expected.

Experiments done. We discussed both experiments: IL-6 receptor blocking antibody experiement (Suppl Fig 2), and mixed infection (Suppl Fig 1).

Figure 3 indicates that IL-6 TgPbA/LISP2 parasites are as efficient or better than wild type parasites at invading host cells but then they do not develop to maturity. What is the evidence that the key factor in their ability to immunize the host is expression of IL-6 rather than the effect of an attenuated parasite?

This is an interesting observation made by the reviewer. With the available data, we cannot really tell which of the two possibilities is operating in thin system. It could also be that the two option are interconnected.

In this model malaria infection, it looks like there are two lethal outcomes: one associated with experimental cerebral malaria at relatively low blood stage parasitemia (which I understand is a controversial model for human cerebral malaria) and the second associated with high blood stage parasitemia. Some of the protocols affect which outcome occurs (see for example Fig 6), but this observation is not properly discussed.

In many occasions, we did see in the past a discrepancy between anti-parasite immunity and anti-disease protection. In this particular experiment (Fig 6), we explored the dose effect of the IL-6 mutant. What is clear from this model is that at the high dose, 104 SPZ, we observe both anti-parasite and anti-disease protection and immunity, whereas at the lower doses, 103 and 102 SPZ, although there was no efficient anti-parasite immunity, mice did not die from cerebral malaria but much later from hyperparasitemia. We consider that the two low doses of IL-6 transgenic parasites did protect against disease expression.

For the data presented in Fig 7, why was there a challenge with WT PbA sporozoites before the heterologous Py challenge? If this step is excluded is there still an effect against P. yoelii? Why was the parasite chosen for the heterologous challenge Py17XNL? Since this parasite is largely restricted to reticulocytes in the blood stream would a different effect have been observed if the heterologous challenge parasite was, for example, P. chabaudi?

Out of scope.

Although the expectation is that IL-6 expression would not occur in the asexual blood stage, I think it would be important to demonstrate experimentally that this is the case.

Done. IL-6 transgenic parasite, when inoculated as infected erythrocytes have no development defect and grow normally in infected mice.

In Fig. 4A the y-axis is labelled IL-6 rRNA when it should be IL-6 mRNA.

Corrected

Reviewer #2 (Significance (Required)):

The significance of the report does depend on whether or not the experimental evidence is sufficient to support the claim that parasite expression of IL-6 is important in generating immunity. There has been a number of studies to show that infection with sporozoites that have been genetically attenuated to not complete subsequent development in the infected liver cell can provide immunity to subsequent infection; what is different about this study is that the authors specifically target the parasite to express a host protein that is likely to be important in acquisition of immunity. Therefore for the study to have high significance they have to show convincingly that it is the expression and activity of IL-6 that is important and I do not think this is the case with the experiments reported. If the authors are correct, then the idea of manipulating the host response by expression of host proteins by the parasite may be an attractive approach to dissect the key elements of immunity to sporozoite infection. At the moment, although there is a lot of focus on developing an attenuated whole sporozoite vaccine against malaria, and this study may provide proof of principle for including a host component in the parasite, there would still be long way to go before any practical application of this approach.

The key message was toned down. As the formal demonstration that the expression and activity of IL-6 is direcxtly involved in IL-6 transgenic parasites to confer protective immunity, we suggest to tone down the message by saying that IL-6 attenuates parasite virulence, the mechanism being likely through IL6 signaling detrimental effect on parasite development.

The audience would be those interested in parasite immunology.

__

Reviewer expertise: malaria parasite cell and molecular biology; host immunity.

**Referees cross commenting** __

__ I think all reviewers are of the opinion that there needs to be a better demonstration that the observed phenotype is mediated by expression and signaling of IL-6, for example by antibody blockade or using a mouse line with a genetic defect in IL-6 signaling. Looking at all the issues that have been raised by the reviewers and need to be addressed with further experimentation, my feeling is that this will take longer than 6 months.

__

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

__ **Summary** This study explores the expression of murine IL-6 by rodent Plasmodium berghei as a means to generate transgenic parasites whose development in the liver is arrested, which may be used as a genetically attenuated pre-erythrocytic vaccine against malaria. The authors conclude that IUL-6-expressing Plasmodium parasites elicit CSD8+ T-cell mediated immune responses that protect against a subsequent challenge with infectious sporozoites.

**Major Comments** __

In Figure 3, the authors show the results of qRT-PCR analysis of mouse livers infected with WT or transgenic parasites. They then use HepG2 cells to assess hepatic parasite numbers and development. Why didn't the authors assess this also in vivo, in liver sections of infected mice?

Done. New data are presented in Fig 3B, C, D

Linked to the above, a more complete analysis of the parasite's behavior in HepG2 cells should be provided. The authors write in the discussion that "IL-6 transgenic parasites develop perfectly well in cultured hepatocytic cells". Does this mean that they develop to the production of infectious merozoites? This could be confirmed by allowing the infected cultures to progress for 60-70 hours and then collecting the supernatants of these cultures and injecting them into naïve mice, to understand whether or not infectious merozoites are formed in vitro.

New analysis demonstrate that IL-6 transgenic parasites actually display a developmental defect at the pre-erythrocytic stage in vivo.

Figure 3C: The authors mention this result almost in passing but fail to provide an explanation for this observation. Why is the number of transgenic parasite EEFs approximately double that of WT parasite EEFs?

A new figure 3 is provided and show that the EEF density (Fig 3B) was drastically reduced both at 24h and at 48h in mice infected with the IL-6 transgenic parasites as compared to those infected with WT PbA parasites, although the differences were not statistically significant. We also examined the size (Fig. 3C) of EEFs, and found the same tendency, namely a reduced size and diameter of IL-6 transgenic EEF as compared to those of WT PbA EEFs with a statistical difference only at 40h.

Figure 3D: The EEF area units (mm2) on the YY axis are certainly wrong. However, they cannot be um2 either, as 15-30 um2 would be far too small for EEFs at 48 hours post-infection. What is it then?

New data are now provided in a new Fig 3.

The authors write "... suggest that the failure of IL-6 Tg-PbANKA/LISP2 parasites to develop in the liver of infected mice is likely due to an active anti-parasite immune response mediated by parasite-encoded IL-6 in vivo". I have several issues with this statement. 1) as mentioned above, the in vitro data cannot be used to draw definitive conclusions about the parasites' behavior in vivo; 2) the transgenic parasites do not "fail to develop in the liver of infected mice". If anything, they develop less than their WT counterparts, which is different from "failing to develop". Clarifying how much they do develop would be important (see next comment).

We provide new in vivo data as to the development of IL-6 transgenic parasites. A new figure 3 is provided and show that the EEF density (Fig 3B) was drastically reduced both at 24h and at 48h in mice infected with the IL-6 transgenic parasites as compared to those infected with WT PbA parasites, although the differences were not statistically significant. We also examined the size (Fig. 3C) of EEFs, and found the same tendency, namely a reduced size and diameter of IL-6 transgenic EEF as compared to those of WT PbA EEFs with a statistical difference only at 40h. We replaced failure by a defect in development.

In connection with the above, I would like to know more about the time when the development of IL-6 Tg-PbANKA/LISP2 parasites is arrested in vivo, in the liver. Are these early- or late-arresting parasites? Is the liver stage of infection compromised during parasite development or at egress? To clarify this, the manuscript would benefit from a timecourse analysis of liver sections of mice infected with this parasite, including data on EEF numbers and sizes up to and beyond 48 h after sporozoite inoculation.

Done. See new figure 3.

Still linked to the issue of parasite arrest in vivo and the possibility of breakthroughs, the manuscript would benefit from an experiment where mice were injected with a high number of transgenic sporozoites and parasitemia is monitored thereafter, much like what was done in Figure 2D, but starting off with a larger inoculum of at least 5 x 10^5 sporozoites.

This was done and there was no breakthrough even with doses as high as 106 sporozoites

While the results shown to suggest that secreted IL-6 restricts the parasite's liver stage development in vivo, this could be more definitely demonstrated by performing an infection with the transgenic parasites in the context of blocking or absence of the host's IL-6 receptor. This experiment was done but unfortunately did not work (Suppl. Fig 2). That is, the treatment of mice infected with IL-6 transgenic parasites with anti-IL-6 receptor blocking antibodies did not reverse the infection phenotype. This was also discuss in the manuscript.

**Minor Comments**

__

The manuscript needs to be improved in terms of both language and format. Some examples, solely from the abstract, are listed below, but the manuscript needs to be appropriately revised in terms of language, grammar, punctuation and format throughout:__

-Space missing between "P." and "berghei"

Done

-Gene names should be italicized

Done

-Rephrase "Considering IL-6 as a critical proinflammatory signal..." to "Considering that IL-6 is a critical proinflammatory signal..."

Done

-"transgenic IL-6 sporozoites" should be "transgenic IL-6-expressing P. berghei sporozoites"

Done

-"impairs Plasmodium infection at the liver stage" should be "impairs the liver stage of Plasmodium infection"

Done

INTRODUCTION

The sentence "Among them, parasites lacking integrity of the parasitophorous vacuole, or late during development, and..." appears to be incomplete and needs rephrasing.

Done

The references used in sentence "During the last decade, in search of key mechanisms that determine the host inflammatory response, a set of host factors turned out to be critical for malaria parasite liver stage development (Mathieu et al., 2015); (Demarta-Gatsi et al., 2017; Demarta-Gatsi et al., 2016) (Grand et al., 2020)" do not all relate to the liver stage of infection. The authors need to select references that are relevant for their statement or else change the statement.

Rephrased

RESULTS

I suggest the authors change the title of Results section "Transgenic P. berghei parasites expressing IL-6 during the liver stage lose infectivity to mice" not only to improve the quality of the English language employed but also to better clarify the notion that they are talking about hepatic infectivity.

On the same section, please correct "timely specific timely".

Done

Transfectants are not "verified". If anything, the insertion of the gene in the parasite's genome is verified or, better still, confirmed.

Done

Sentence "The two lines behave similarly" is redundant.

Done

The legend of Figure 1 must include the definitions of all the acronyms in that figure.

Acronyms in the whole manuscript are defined elsewhere

"IL-6 transgenic sporozoites" is not an appropriate designation. If anything, they should be called IL-6-expressing P. berghei sporozoites".

Done

Figure 2 B: The YY axis should clarify that it refers to sporozoite numbers, as there are many other parasite stages in mosquitoes.

Done

Figure 2C: This scheme is hardly necessary. It would suffice to label the plots in D and E with the names of the parasite lines employed rather than "Group 1", "Group 2", "Group 3". The scheme is provided for more clarity and easy reading of the accompanying figures

Figure 2D, 2E: Why didn't the authors use the same scale on the XX axis of the two plots?

The qRT-PCR data per se do not substantiate the statement "Therefore, RT-qPCR analysis in the liver confirms that the loss of infectivity of IL-6 Tg-PbANKA/LISP2 SPZ is due to a defect in liver stage development in vivo", as a defect in invasion of hepatocytes cannot be excluded. The term "loss of infectivity" is also misleading. Do the authors mean loss of blood stage infectivity?

Yes

Sentence "... all parasites were able to invade and develop inside HepG2 cells." is misleading. The authors probably mean "parasites of both lines".

Changed

Figure 4: Why did the authors swap the order of the two experimental groups from one plot to the next? The same order should be used, to avoid confusion! Also, the authors should make the width of the bars in similar between the two plots.

Done

The authors should consider moving Figure 5 to the Supplementary materials.

Reviewer #3 (Significance (Required)):

*Nature and significance of the advance. Compare to existing published knowledge. Audience.*

This study extends our current knowledge on genetically attenuated malaria vaccine candidates and validates the concept of suicide parasites for immunization against malaria. This paper will be of interest to researchers working on malaria vaccination, as well as all those interested in transgenic Plasmodium parasites, and the biology and immunology of liver stage infection by malaria parasites.

*Your expertise.*

The co-reviewer and the reviewer are experts on the liver stage of Plasmodium infection and on pre-erythrocytic malaria vaccination.

**Referees cross commenting**

I agree with all of Reviewers 1 and 2's remarks and, upon consideration, I would like to revise my "Estimated time to Complete Revisions" to become between 3 and 6 months

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary

This study explores the expression of murine IL-6 by rodent Plasmodium berghei as a means to generate transgenic parasites whose development in the liver is arrested, which may be used as a genetically attenuated pre-erythrocytic vaccine against malaria. The authors conclude that IUL-6-expressing Plasmodium parasites elicit CSD8+ T-cell mediated immune responses that protect against a subsequent challenge with infectious sporozoites.

Major Comments

In Figure 3, the authors show the results of qRT-PCR analysis of mouse livers infected with WT or transgenic parasites. They then use HepG2 cells to assess hepatic parasite numbers and development. Why didn't the authors assess this also in vivo, in liver sections of infected mice?

Linked to the above, a more complete analysis of the parasite's behavior in HepG2 cells should be provided. The authors write in the discussion that "IL-6 transgenic parasites develop perfectly well in cultured hepatocytic cells". Does this mean that they develop to the production of infectious merozoites? This could be confirmed by allowing the infected cultures to progress for 60-70 hours and then collecting the supernatants of these cultures and injecting them into naïve mice, to understand whether or not infectious merozoites are formed in vitro.

Figure 3C: The authors mention this result almost in passing but fail to provide an explanation for this observation. Why is the number of transgenic parasite EEFs approximately double that of WT parasite EEFs?

Figure 3D: The EEF area units (mm2) on the YY axis are certainly wrong. However, they cannot be um2 either, as 15-30 um2 would be far too small for EEFs at 48 hours post-infection. What is it then?

The authors write "... suggest that the failure of IL-6 Tg-PbANKA/LISP2 parasites to develop in the liver of infected mice is likely due to an active anti-parasite immune response mediated by parasite-encoded IL-6 in vivo". I have several issues with this statement. 1) as mentioned above, the in vitro data cannot be used to draw definitive conclusions about the parasites' behavior in vivo; 2) the transgenic parasites do not "fail to develop in the liver of infected mice". If anything, they develop less than their WT counterparts, which is different from "failing to develop". Clarifying how much they do develop would be important (see next comment).

In connection with the above, I would like to know more about the time when the development of IL-6 Tg-PbANKA/LISP2 parasites is arrested in vivo, in the liver. Are these early- or late-arresting parasites? Is the liver stage of infection compromised during parasite development or at egress? To clarify this, the manuscript would benefit from a timecourse analysis of liver sections of mice infected with this parasite, including data on EEF numbers and sizes up to and beyond 48 h after sporozoite inoculation.

Still linked to the issue of parasite arrest in vivo and the possibility of breakthroughs, the manuscript would benefit from an experiment where mice were injected with a high number of transgenic sporozoites and parasitemia is monitored thereafter, much like what was done in Figure 2D, but starting off with a larger inoculum of at least 5 x 10^5 sporozoites.

While the results shown to suggest that secreted IL-6 restricts the parasite's liver stage development in vivo, this could be more definitely demonstrated by performing an infection with the transgenic parasites in the context of blocking or absence of the host's IL-6 receptor.

Minor Comments

The manuscript needs to be improved in terms of both language and format. Some examples, solely from the abstract, are listed below, but the manuscript needs to be appropriately revised in terms of language, grammar, punctuation and format throughout:

-Space missing between "P." and "berghei"

-Gene names should be italicized

-Rephrase "Considering IL-6 as a critical proinflammatory signal..." to "Considering that IL-6 is a critical proinflammatory signal..."

-"transgenic IL-6 sporozoites" should be "transgenic IL-6-expressing P. berghei sporozoites"

-"impairs Plasmodium infection at the liver stage" should be "impairs the liver stage of Plasmodium infection"

INTRODUCTION

The sentence "Among them, parasites lacking integrity of the parasitophorous vacuole, or late during development, and..." appears to be incomplete and needs rephrasing.

The references used in sentence "During the last decade, in search of key mechanisms that determine the host inflammatory response, a set of host factors turned out to be critical for malaria parasite liver stage development (Mathieu et al., 2015); (Demarta-Gatsi et al., 2017; Demarta-Gatsi et al., 2016) (Grand et al., 2020)" do not all relate to the liver stage of infection. The authors need to select references that are relevant for their statement or else change the statement.

RESULTS

I suggest the authors change the title of Results section "Transgenic P. berghei parasites expressing IL-6 during the liver stage lose infectivity to mice" not only to improve the quality of the English language employed but also to better clarify the notion that they are talking about hepatic infectivity.

On the same section, please correct "timely specific timely".

Transfectants are not "verified". If anything, the insertion of the gene in the parasite's genome is verified or, better still, confirmed.

Sentence "The two lines behave similarly" is redundant.

The legend of Figure 1 must include the definitions of all the acronyms in that figure.

"IL-6 transgenic sporozoites" is not an appropriate designation. If anything, they should be called IL-6-expressing P. berghei sporozoites".

Figure 2 B: The YY axis should clarify that it refers to sporozoite numbers, as there are many other parasite stages in mosquitoes.

Figure 2C: This scheme is hardly necessary. It would suffice to label the plots in D and E with the names of the parasite lines employed rather than "Group 1", "Group 2", "Group 3".

Figure 2D, 2E: Why didn't the authors use the same scale on the XX axis of the two plots?

The qRT-PCR data per se do not substantiate the statement "Therefore, RT-qPCR analysis in the liver confirms that the loss of infectivity of IL-6 Tg-PbANKA/LISP2 SPZ is due to a defect in liver stage development in vivo", as a defect in invasion of hepatocytes cannot be excluded. The term "loss of infectivity" is also misleading. Do the authors mean loss of blood stage infectivity?

Sentence "... all parasites were able to invade and develop inside HepG2 cells." is misleading. The authors probably mean "parasites of both lines".

Figure 4: Why did the authors swap the order of the two experimental groups from one plot to the next? The same order should be used, to avoid confusion! Also, the authors should make the width of the bars in similar between the two plots.

The authors should consider moving Figure 5 to the Supplementary materials.

Significance

Nature and significance of the advance. Compare to existing published knowledge. Audience.

This study extends our current knowledge on genetically attenuated malaria vaccine candidates and validates the concept of suicide parasites for immunization against malaria. This paper will be of interest to researchers working on malaria vaccination, as well as all those interested in transgenic Plasmodium parasites, and the biology and immunology of liver stage infection by malaria parasites.

Your expertise.

The co-reviewer and the reviewer are experts on the liver stage of Plasmodium infection and on pre-erythrocytic malaria vaccination.

Referees cross commenting

I agree with all of Reviewers 1 and 2's remarks and, upon consideration, I would like to revise my "Estimated time to Complete Revisions" to become between 3 and 6 months

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The manuscript describes the construction of a Plasmodium berghei that expresses murine interleukin-6 in exoerythrocytic (liver stage) parasites and the analysis of mice infected with sporozoites of this parasite line. They find that such parasites do not complete development in liver cells and therefore do not produce subsequent infection in red blood cells. The ability of prior infection with these parasites on the ability of the host to resist both wild type and heterologous species challenge is then examined.

The key assumption that underlies the study is that the observed phenotypes result from parasite expression of bioactive IL-6 that functions to modulate the immune system. Other explanations are not considered, for example the over-expression of secreted IL-6 may prevent the complete maturation of the intracellular parasite by clogging up the parasite secretory pathway. The authors use the 'wild type' parasite as the control but not only does the wild type not express IL-6 it also does not express the human DHFR gene used as a selection system. A much better control parasite would be one that expresses a non-bioactive IL-6 so that the potential effects on parasite maturation can be differentiated from those on the mouse immune system. Another control to be considered would be comparison with a genetically attenuated parasite with a block in late stage development, and which does not produce a host cytokine.

Another assumption is that IL-6 is secreted from the infected liver cell and mediates its effects, presumably by binding to its cell surface receptor. The expectation of Il-6 secretion from the parasite is that it would accumulate in the parasitophorous vacuole - how would it get out of the infected host cell? While evidence is provided of IL-6 in the in vitro culture supernatant of infected cells - this might arise from damaged cells in rather artificial conditions. Have the authors considered doing the experiment of concurrent mouse infection with both wild type and recombinant parasites? If the mechanism of parasite killing in infected liver cells is as proposed, then a reduction of wild type parasites in the subsequent asexual blood stage would be expected.

Figure 3 indicates that IL-6 TgPbA/LISP2 parasites are as efficient or better than wild type parasites at invading host cells but then they do not develop to maturity. What is the evidence that the key factor in their ability to immunize the host is expression of IL-6 rather than the effect of an attenuated parasite?

In this model malaria infection, it looks like there are two lethal outcomes: one associated with experimental cerebral malaria at relatively low blood stage parasitemia (which I understand is a controversial model for human cerebral malaria) and the second associated with high blood stage parasitemia. Some of the protocols affect which outcome occurs (see for example Fig 6), but this observation is not properly discussed.

For the data presented in Fig 7, why was there a challenge with WT PbA sporozoites before the heterologous Py challenge? If this step is excluded is there still an effect against P. yoelii? Why was the parasite chosen for the heterologous challenge Py17XNL? Since this parasite is largely restricted to reticulocytes in the blood stream would a different effect have been observed if the heterologous challenge parasite was, for example, P. chabaudi?

Although the expectation is that IL-6 expression would not occur in the asexual blood stage, I think it would be important to demonstrate experimentally that this is the case.

In Fig. 4A the y-axis is labelled IL-6 rRNA when it should be IL-6 mRNA.

Significance

The significance of the report does depend on whether or not the experimental evidence is sufficient to support the claim that parasite expression of IL-6 is important in generating immunity. There has been a number of studies to show that infection with sporozoites that have been genetically attenuated to not complete subsequent development in the infected liver cell can provide immunity to subsequent infection; what is different about this study is that the authors specifically target the parasite to express a host protein that is likely to be important in acquisition of immunity. Therefore for the study to have high significance they have to show convincingly that it is the expression and activity of IL-6 that is important and I do not think this is the case with the experiments reported. If the authors are correct, then the idea of manipulating the host response by expression of host proteins by the parasite may be an attractive approach to dissect the key elements of immunity to sporozoite infection. At the moment, although there is a lot of focus on developing an attenuated whole sporozoite vaccine against malaria, and this study may provide proof of principle for including a host component in the parasite, there would still be long way to go before any practical application of this approach.

The audience would be those interested in parasite immunology.

Reviewer expertise: malaria parasite cell and molecular biology; host immunity.

Referees cross commenting

I think all reviewers are of the opinion that there needs to be a better demonstration that the observed phenotype is mediated by expression and signaling of IL-6, for example by antibody blockade or using a mouse line with a genetic defect in IL-6 signaling. Looking at all the issues that have been raised by the reviewers and need to be addressed with further experimentation, my feeling is that this will take longer than 6 months.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Whole sporozoite vaccines confer sterilizing protection against Plasmodium infection. However, further improvements of whole sporozoite vaccines is needed and requires a thorough understanding of the immune processes that mediate protection and the deployment of novel strategies further augment protective immunity while limiting the impact of factors that are detrimental to protection. Work from the Mecheri laboratory and others had previously established that IL-6 signaling plays a critical role in the immune response to a liver stage infection; engagement of IL-6 signaling promotes the initial control of a liver stage infection and enhances the protective adaptive immune response. Given this potent protective role for IL-6, Belhimeur and colleagues design a parasite strain in rodent malaria parasites that encodes and secrete murine IL-6 during liver stage infection. They show that upon infection of wildtype mice, these transgenic parasites i) are unable to transition to blood stage infection, ii) produce Il-6 and iii) induce a durable adaptive immune response that can protect against sporozoite challenge. This study is novel and intriguing. However, a superficial analysis of the transgenic parasite strain, an incomplete analysis of the immune response to infection and the lack of data regarding the possibility of IL-6 mediated immunopathology have dampened this reviewer's enthusiasm for the work.

Major Concerns:

1)The data in Figure 3b-3d clearly indicate that the IL-6 encoding transgenic parasites exhibit a defect in parasite development within HepG2 cells that is maintained in vivo. The authors propose that an arrest of these parasites in the liver stage precludes their transition to blood stage infection and that this arrest is dependent on IL-6 signaling. To better support that claim the authors should:

a.Better characterize in vivo liver stage arrest using infected liver tissue analysis with immunofluorescence microscopy to determine when and how precisely IL-6 transgenic parasites are impacted in development.

b.Determine if arrested development of IL-6 transgenic parasites is truly dependent on IL-6 signaling using antibody blockade of IL-6 signaling and mice with genetic defects in IL-6 signaling.

2)The authors claim that IL-6 production and secretion into the liver tissue augments the adaptive immune response to liver stage infection. This in turn results in a durable adaptive immune responses that protect against infection. However, the mechanistic underpinning of IL-6 signaling in the liver that is induced by their transgenic parasites and the impact on adaptive immune responses is poorly characterized:

a.There is no evidence that the protective adaptive immune response induced by IL-6 trangenic parasite infection is dependent on IL-6 signaling. Is superior protection and immunogenicity lost in IL-6 signaling deficient animals that are infected with IL-6 transgenic parasites?

b.What elements of the adaptive immune response are impacted? One can imagine that IL-6 mediated killing of infected hepatocytes might introduce more parasite antigen that can be acquired by antigen presenting cells, or that IL-6 mediated pro-inflammatory signaling might regulate the maturation of antigen presenting cells, increased differentiation of helper T cells, the downregulation of regulatory T cell function and frequency and/or the differentiation of effector CD8 T cells into long-lived hepatic memory CD8 T cells. The authors should conduct a more comprehensive analysis of how parasite-encoded IL-6 impacts adaptive immunity.

3)While IL-6 transgenic parasites induce a potent and durable adaptive immune response, the authors should show how this compares to published whole sporozoite immunizations. The authors should determine if immunization with IL-6 transgenic parasites is superior to for example immunization with radiation-attenuated sporozoites and generically attenuated sporozoites.

4) IL-6 signaling is a major player in inflammatory diseases and the induction of immunopathology. As such the authors should carefully examine the duration and magnitude of IL-6 protein production in the liver, and serum after IL-6 Tg parasite infection and determine if IL-6 signaling promotes liver immunopathology.

Significance

The paper is reporting a novel strategy to generate a whole sporozoite vaccine. Expression of IL6 in a transgenic parasite. This could be a significant contribution to the field if additional experiments as outlined in the critique are conducted.The work might also inform vaccine design for other pathogens.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

Reviewers 1 & 3 make the very valid point that we do not have evidence for HDAC6 as the molecular target for the effects of ACY1215 on T cell development. We agree entirely, and do not claim to have defined the molecular target of ACY1215. However, these findings have direct relevance to the current use of ACY1215 as a cancer therapeutic. In addition, they provide a valuable new means of understanding the sequence of events in β-selection at higher resolution than was previously possible.

A second major aspect of concern was whether the drug acted upon T cell development directly, or through effects on OP9 stromal cells. We hope you will agree that our new data (detailed below) has put that concern to rest.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

*Reviewer #1 (Evidence, reproducibility and clarity (Required)):

In this work, Russell and colleagues study the differentiation steps of thymocytes around the time of expression and function of the pre-TCR. They use CD2 as a new marker of an intermediate population of differentiation between DN3a thymocytes and DN4 thymocytes. The CD2+ thymocytes would be and a later stage of differentiation than the CD2 negative ones. In this way, they define a DN3b-Pre and a DN3b-Post populations. The study also aims to study the role of histone deacetylase HDAC6 in thymocytes differentiation at the time of pre-TCR signaling by using as a tool the inhibitor ACY1215 and conclude that HDAC plays an important role during the DN3-DN4 transition. The method the authors use to study consist of the sorting of precursor cells from fetal or adult thymuses and studying the effect of the inhibitor during differentiation in vitro promoted by interaction of the thymocytes with the OP9-DL1 cell line, a well-characterized cell line that expresses a ligand of Notch and promotes DN3 differentiation up to the DP stage. There are major concerns with the approach used by the researchers that make their conclusions unsustainable. 1) They use the inhibitor ACY1215 in the co-culture of thymocytes with OP9-DL1 cells to examine the effect of HDAC inhibition in thymocytes on their differentiation. However, the authors do not provide any control result showing that the effects detected on differentiation are not caused by the activity of the inhibitor on OP9-DL1 cells and not on thymocytes. This possibility is not excluded and if the inhibitor were acting on OP9 cells would invalidate completely the conclusions of the study.*

* *We now include data that ACY1215 does not impact upon OP9-DL1 cell number or acetylation of tubulin, and that ACY1215-treated OP9-DL1 cells can fully support adhesion and differentiation of thymocytes (new Supp Fig 2 A-C). We have added two additional authors who contributed to these data. We believe these data provide strong evidence that ACY1215 exerts its effects directly on the developing T cells.

* 2) The inhibitor is used at a single concentration (one has to search in the Methods section in order to find that it is 1 micromolar) and there is no evidence provided of dose-response effects. Furthermore, experiments are missing in which different doses of the inhibitor are tested on its potential targets and shown to have a selective impact on those targets at the concentration used in the study.*

We do not believe these analysis are within the scope of the manuscript, the focus of which is the novel differentiation characteristics revealed by ACY1215, rather than the impact of the drug itself.

3) The authors suggest that the inhibitor is a epigenetic regulator because it acts on the deacetylatio of histones but also that it acts on the formation of a potential immunological synapse by the pre-TCR expressing thymocytes with inhibition of the translocation of the microtubule organizing centre. By the end of the study, one does not know exactly how is the inhibitor acting on pre-T cell differentiation.

* *We completely agree, this manuscript provides a starting point for dissecting the molecular mechanism for ACY1215 effects, and we have taken care to discuss the several possibilities that are currently in play. However, we believe the identification of an effect is a critical finding in its own right and has already proven valuable in uncovering novel events in β-selection.

* 4) The authors seem to postulate a model in which the effect of the inhibitor on the immunological synapse and pre-TCR signaling affects the expression of Lef1 which itself modulates histone deacetylation. Therefore, the inhibition of HDAC6 would be acting on pre-TCR signaling upstream but also on the activity of Lef1 downstream. It seems that the approach is not sufficiently precise as to discriminate the site of action of the inhibitor*

We propose this as one possible model. Dissecting the impact via Lef1 vs HDAC6 vs tubulin is beyond the scope of this paper.

* 5) The authors use contour plots to display their data. This has the advantage of defining cell populations but on the other hand, hides the number of events that are defining the populations. This is for instance reflected in Figure 7 panel B where the CD5 vs surface TCRbeta plot of cultured DN3a thymocytes shows many different populations (in green) which are probably artifacts of the contour plot. Very likely such populations are formed by very few events

*

We have adjusted the contour densities. We also note that the histograms above and to the side of the contour plots are provide for ready comparison of proportions.

* 6) I do not see a big effect of the inhibitor on Lef 1 expression (Figure 6A) and if the inhibitor has an effect at the DN3b-Pre stage why it should not have it at the DN3b-Post stage.

*

The effect of ACY1215 on Lef1 expression is clear in FL-derived DN3bPre (Fig 6Ai) and in thymus-derived DN3a and DN3bPre cells (Fig 6Aii,7A). Given previous findings that Lef1/TCF are required for progression through β-selection (Xu et al, 09 from the manuscript), these data suggest that the failure to upregulate Lef1 in some DN3bPre cells might prevent their traversal to DN4, explaining why DN3bPost cells don’t exhibit a loss of Lef1.

* 7) Suppl. Fig. 11.-In DN3b-Post, expression of CD5 is higher than in DN3a but not so clearly higher than in DN3b-Pre. The effect of the inhibitor on DN3b-Post was that of reducing CD5 expression but not Lef1 expression. In this experiment, the effect of the inhibitor of Lef1 expression by DN3b-Pre is not seen. Quantitation? The inhibitor could be altering CD5 expression by inhibiting the synapse independent of Lef1 ?*

This is an understandable misconception, and we have clarified in the text and by including a plot of CD5 vs Lef1 in Sup Fig 11. The effect of drug on Lef1 expression in DN3bPre is readily apparent (see reduction in Lef1Hi in the red contour plot LHS). However, by separating Lef1 high and low populations (RHS), we see Lef1Hi cells in the pink contours. This does not indicate a high proportion of Lef1Hi cells, merely that we enriched for them in the gating, as a means to assess any correlation with CD5. The reviewer is absolutely correct that the inhibitor could be altering CD5 expression by inhibiting the synapse independent of Lef1. However, the clear correlation of expression of Lef1 and CD5 in untreated cells, and the loss of that correlation after ACY1215 treatment, supports the notion that ACY1215 disrupts a functional association between expression of Lef1 and CD5.

* 8) Figure 8.- The populations defined by CFSE staining are too broad in terms of fluorescence intensity as to determine number of cell divisions. It seems that there are only two populations: one that has not diluted CFSE and therefore has not divided and another that has diluted CFSE and has divided. How many times? we do not know. On the other hand, CD5 is increased in cells that have diluted CFSE. Have they expressed CD4, CD8, downregulated CD25, other markers indicating that the cells are not longer DN3a or DN3b? CD5 is upregulated after CFSE dilution not before dilution, so is CD5 expression cause or effect of differentiation..The effect of the inhibitor is not clear.*

We agree the CFSE staining does not indicate number of divisions. We don’t agree that there are two populations, rather, a spread of CFSE indicating heterogeneity in the extent of proliferation, and a inverse correlation between CFSE and CD5 indicating that proliferation is associated with increasing CD5 expression. At this stage, we do not believe there is sufficient information to predict a causal relationship between these two markers. However, to our knowledge, the association is novel and provides a strong basis for further exploration, particularly in light of recent published findings that CD5 can act to tune the TCR signal at later stages of T cell development.

* **Referees cross-commenting**

Totally in agreement! The effect of the drug could be on the OP9-DL1 cells and not on thymocytes. This is not proven

We hope you agree that our new data alleviates this concern, and supports a T cell autonomous impact of ACY1215.

Reviewer #1 (Significance (Required)):

With all the concerns about the method used by the authors to define subpopulations in DN3-DN4 transition and the involvement of HDAC6 activity I do not believe the paper will have a significant impact in the field. The authors will need to rethink their approaches in order to investigate the subject with sufficient guarantees. Perhaps using genetic approaches.*

As agreed by Reviewers 2 and 3, new findings in the manuscript represent a substantial contribution to the field irrespective of the molecular target of ACY1215. Genetic approaches have their own drawbacks (including issues of compensation in the non-acute setting of most genetic modifications), and the clinical use of inhibitors such as ACY1215 mean these findings are significant irrespective of the molecular target.*

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

While the authors appear to have initially set out to determine the role of HDAC6 at the beta-selection checkpoint of T cell development, they also came away with a new panel of markers that further delineate important stages of thymocyte differentiation, describing the sequential upregulation of CD28, the preTCR, Lef1 and CD5, and, subsequently, CD2 as cells pass the test verifying successful recombination of the T cell receptor (TCR) b chain. The authors used several approaches for this study; they took advantage of the well-characterized OP9-DL1 co-culture system to support differentiation of progenitor cells in the presence or absence of an HDAC6-specific inhibitor or they isolated progenitor populations of interest directly from a murine thymus for short term culture in the presence or absence of inhibitor. They identify an important role for HDAC6 at the b-selection checkpoint as evidenced by an accumulation of a subset of 'double negative 3' cells and attribute this, in part, to increased acetylation of a-tubulin at the preTCR synapse as well as dysregulated expression of and/or recruitment to the microtubule-organising centre of proteins essential for beta-selection signals. Possible disruption of preTCR signaling by an HDAC6 inhibitor appears to limit upregulation of regulatory molecules (e.g. CD5) and normal progression through this stage.

I find the data presented and conclusions made to be largely convincing and that this manuscript represents a substantial contribution to the field. I recognize many of the challenges associated with this study that include assessing protein levels on small populations of cells, the heterogeneity of the cell populations (even if sorting a discrete subset, the requirement for culturing the cells +/- inhibitor invites differentiation), and the pleiotropic effects of HDAC inhibitors (HDACi). With few exceptions, we can accept these issues as the authors were clearly careful in their approaches, and there are limited other techniques that can be used to address some of these questions.*

We thank the reviewer for their strong endorsement of the study. *

---

Major comments.

Given the effort already put into this paper, it might be worthwhile to ultimately show step-wise progression through the developmental intermediates described in this manuscript. A time course to assess differentiation of isolated DN3a cells in OP9-Dl1 coculture could be considered, for example. The authors clearly have the reagents and skills to carry out these experiments though the timing would be a factor in order to capture the appearance of discrete developmental intermediates. This would, in many ways, provide a straightforward summary of many of the reported results that would improve accessibility to a broader audience.

*We agree that this would be of ultimate value. Unfortunately, it is not in the scope of this manuscript.

The differences in protein levels stated are not always so obvious based on the contour plots and/or histograms; these are often subtle effects that can be obscured by the 'noise' that accompanies the analysis of protein levels on small populations of cells. Quantification of the data should be included when making conclusions about differences in expression levels of different markers. In addition, when quantification and statistics are provided, it is clear that at least three repeats were included, but without quantification, the reproducibility of the experiments are not known; the number of replicates for each experiment should be obviously stated.

We have added quantification to Fig 6, Fig 7 and Fig S11 and included numbers to indicate number of replicates for each experiments.*

Minor points.

The impact of the inhibitor seems to be inconsistent in Fig. 6A i and ii; there is not much of an impact of the inhibitor in ii as I understand. There also seem to be significantly different expression patterns of Lef in the DN3bpre stage in the two models (OP9 vs ex vivo) - what is the explanation for this?*

Lef1 does appear to be upregulated slightly earlier in ex vivo thymocytes compared to fetal liver derived cells, although most of the upregulation occurs in the DN3bPre stage in both systems. We are not sure of the explanation for this. Importantly both systems show clear reduction of Lef1 before, but not after, CD2 expression. * That the inhibitor leads to a 'loss of correlation' between Lef and CD5 levels is more obvious in Supp Fig 11 than as presented in Figure 7.*

Perhaps, although it is still evident in Figure 7. We believe the effect is most striking when thymocytes were sorted for DN3a, and then treated for 2 days (Fig 7B), but we also see the effect at 1 day on fetal liver-derived cells (Supp Fig 11) and at 1 day for thymocytes (Fig 7B) * Consider adding a CD25lo population (e.g. DN4) as a reference in Supp. Fig. 12.*

By definition DN3 and DN4 are delineated by expression of CD25, so all DN4 cells are lower for CD25 than any of the DN3 subsets. We have now made this clear with addition of DN4 in Supp Fig 12 as requested. * In reference to Fig. 5, the authors suggest the analysis of MTOC components in DN3a cells; are these Dn3a cells? DN3a cells were isolated and then cultured for a day +/- inhibitor. I presume there is some differentiation in these cultures that depends on the presence of the inhibitor. I am not suggesting that the authors need to redo this experiment but rather either acknowledge that these are not all DN3a cells (unless I am wrong here) by changing the wording, or add a marker to distinguish the subset (CD2?)*

You are correct, we have changed the wording to say: DN3a cells were cultured for 1 day with and without ACY1215 (so would be predominantly DN3a and DN3bPre and not yet past β-selection; see Supp Fig 9).*

Make note of the DN3b nomenclature used; I believe that 'pro' was used instead of 'post' at least once.*

We apologize, and have corrected.*

In Fig 1, the populations identified as CD4+ and CD8+ are likely immature populations; unless including TCRb staining to distinguish these, I suggest excluding them from the analysis. I think the DP population is sufficient here to get the point across.*

We appreciate the advice and have removed the SP data.*

In Supp Fig 2. the schematic does not appear to be consistent with legend (2 versus 4 d of culture).*

We have corrected to 2D.*

In Supp Fig 8a, the quantification of DN3a/b-pre/b-pro has a different experimental set up than in Fig 3bii but is written as if this is the quantification of the data as I understand it.*

No, the quantification is for Fig 3bi.*

In line 214/215, it is suggested that "Analysis of the cells immediately after extraction showed clearly distinct DN3a, DN3bPre and DN3bPost cells." but I did not find the data for this.*

We have now made more clear that this data is at the top right of Fig 4) * Please confirm the experimental set up in Supp. Fig. 9. Why treat with inhibitor prior to isolating the subsets and then culturing again without inhibitor?*

This is the correct set-up. The goal was to enrich sufficient DN3bPre cells to ensure a pure sort (taking advantage of the ACY1215 effect), and then to monitor their differentiation.*

Eliminate conclusions made without specific reference to figures or to 'future' figures.

*

We have tried to find such conlusions, but not been able to.

* In some histograms (e.g. 5), it was not obvious to me what the negative controls represented. Are these fluorescence minus one, isotype, other?

*

We have made more clear in the Figure Legends.

* In the abstract, it is suggested that increases in a number of markers provides for escalating TCR signaling strength; CD5 is among these. As a negative regulator of TCR signals, this statement seems to be counterintuitive.*

Apologies for this error, we have changed ‘escalating’ to ‘modulating’*

The authors state that, "These data together indicate that CD5 serves as a link between TCRb expression and proliferation, ...." (line 325/326); how CD5 'links' the two is not clear.*

We have changed the wording.*

-It is written that "...at Day 8-10 of the co-culture, when cells from mouse fetal liver were predominantly at the DN3 stage of T cell development (Supp Fig 1B)...". Reconsider wording this statement as it appears as if the majority of cells actually express CD4 and/or CD8. *

Thank you, we have done so.

* **Referees cross-commenting**

Reviewers 1 and 3 bring up important, obvious points that this reviewer missed in terms of the potential off-target effects of the HDACi on the stromal cell component of the co-culture system used for the experiments. It is difficult to determine the relevance of HDAC6 at this developmental checkpoint without additional controls*

We hope you agree that we have allayed this concern with new controls.*

Reviewer #2 (Significance (Required)):

As an immunologist with an interest in the molecular and cellular mechanisms that regulate T cell development, I find this manuscript interesting for several reasons.

One of the benefits of studying development and differentiation in the immune system is the ability to distinguish discrete developmental intermediates by flow cytometry using defined panels of cell surface and intracellular markers; this allows for the isolation of populations of cells for testing progenitor/progeny relationships, to identify the role of essential genes at various developmental stages and beyond. This manuscript adds important new markers that will allow researchers to more discretely tease apart important stages in T cell development during an important regulatory checkpoint.

Not only is beta-selection an essential first step in ensuring a functional antigen receptor repertoire during T cell development, but its tight regulation is absolutely necessary due to the double-strand DNA breaks that accompany antigen receptor gene rearrangement and the massive proliferation that ensues after successful pairing of a functionally rearranged TCRb chain with the preTCRa; indeed, dysregulation at the beta-selection checkpoint can give rise to leukemia. This study provides new insight into potential mechanisms of beta-selection regulation.

Thank you for this positive evaluation.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Chann et al employ a pharmacologic inhibitor (ACY1215) to assess the role of HDAC6 as a molecular effector of differentiation during traversal of the b-selection checkpoint. Using this inhibitor, they detect an accumulation of cells at the DN3b stage that have failed to upregulate CD2. Consequently, they propose the existence of a new intermediate stage between induction of CD28 and CD2 and term these stages as DN3b-pre and DN3b-post. The proposal is that the arrest of development between these two stages results from interference with the normal pattern of induction of CD5 and Lef1. The experiments are thoughtfully designed and interpreted. However, there are a number of significant issues.

1. HDAC6 ko mice have no thymic phenotype (Zhang MCB 08; Fig. 6) raising the possibility that all of the effects observed following ACY1215 treatment result from off-target activity. This calls the mechanistic analysis into question. One way to address this would be to treat HDAC6 deficient thymic progenitors with equivalent doses of drug to determine if the observed effects do not occur.*

We agree that HDAC6 might not be the primary target, and have gone to considerable lengths to make this clear in the manuscript. Rather than focus specifically on HDAC6, we believe identification of all possible molecular targets (HDAC6, Lef1/TCF1, perhaps other acetylases, each conferring transcriptional or cytoskeletal regulation) will require extensive efforts not within the scope of this manuscript.

* Equally important is that the analysis is essentially all descriptive with no interventions (gain or loss-of-function) to investigate the causal relationships of the correlations observed.

*

We don’t agree that the analysis is essentially all descriptive, since our findings derived from the application of ACY1215.

* Some of the data interpretation is puzzling. For example, drug treatment results in an increased proportion of DN3b cells, which is interpreted to mean that drug promotes the DN3a to DN3b transition; however, based on the absolute counts, a more likely explanation is the the drug is killing the DN3a cells (Fig2a).*

We certainly agree and state that DN3a cells are depleted by 1 day ACY1215, but do not believe this is due to death given the apoptisis analysis in Fig S4. Given that DN3 and DN4 cell numbers are equivalent even out to Day 4 when one would expect the DN3a depletion to have substantial effect, we suggest that this is ‘perhaps caused by precocious differentiation from DN3a to DN3b’. * **Referees cross-commenting**

Is there consensus that w/o clear evidence pointing to on-target action of the drug on the intended target that the significance of the study is limited?

We have confirmed that thymocytes are the cellular target. The molecular target will take much more work and is not the focus of this paper.

Reviewer #3 (Significance (Required)):

Because of the complete absence of a thymic phenotype of HDAC6-deficient mice, the significance ofe these findings is substantially in doubt.*

There are many examples of key biological processes that were not revealed by a phenotype in the knockout, due to compensatory effects (pertinent to this paper: Lef1 being a clear example).

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Chann et al employ a pharmacologic inhibitor (ACY1215) to assess the role of HDAC6 as a molecular effector of differentiation during traversal of the b-selection checkpoint. Using this inhibitor, they detect an accumulation of cells at the DN3b stage that have failed to upregulate CD2. Consequently, they propose the existence of a new intermediate stage between induction of CD28 and CD2 and term these stages as DN3b-pre and DN3b-post. The proposal is that the arrest of development between these two stages results from interference with the normal pattern of induction of CD5 and Lef1. The experiments are thoughtfully designed and interpreted. However, there are a number of significant issues.

1. HDAC6 ko mice have no thymic phenotype (Zhang MCB 08; Fig. 6) raising the possibility that all of the effects observed following ACY1215 treatment result from off-target activity. This calls the mechanistic analysis into question. One way to address this would be to treat HDAC6 deficient thymic progenitors with equivalent doses of drug to determine if the observed effects do not occur.
2. Equally important is that the analysis is essentially all descriptive with no interventions (gain or loss-of-function) to investigate the causal relationships of the correlations observed.
3. Some of the data interpretation is puzzling. For example, drug treatment results in an increased proportion of DN3b cells, which is interpreted to mean that drug promotes the DN3a to DN3b transition; however, based on the absolute counts, a more likely explanation is the the drug is killing the DN3a cells (Fig2a).

Referees cross-commenting

Is there consensus that w/o clear evidence pointing to on-target action of the drug on the intended target that the significance of the study is limited?

Significance

Because of the complete absence of a thymic phenotype of HDAC6-deficient mice, the significance ofe these findings is substantially in doubt.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

While the authors appear to have initially set out to determine the role of HDAC6 at the beta-selection checkpoint of T cell development, they also came away with a new panel of markers that further delineate important stages of thymocyte differentiation, describing the sequential upregulation of CD28, the preTCR, Lef1 and CD5, and, subsequently, CD2 as cells pass the test verifying successful recombination of the T cell receptor (TCR) b chain. The authors used several approaches for this study; they took advantage of the well-characterized OP9-DL1 co-culture system to support differentiation of progenitor cells in the presence or absence of an HDAC6-specific inhibitor or they isolated progenitor populations of interest directly from a murine thymus for short term culture in the presence or absence of inhibitor. They identify an important role for HDAC6 at the b-selection checkpoint as evidenced by an accumulation of a subset of 'double negative 3' cells and attribute this, in part, to increased acetylation of a-tubulin at the preTCR synapse as well as dysregulated expression of and/or recruitment to the microtubule-organising centre of proteins essential for beta-selection signals. Possible disruption of preTCR signaling by an HDAC6 inhibitor appears to limit upregulation of regulatory molecules (e.g. CD5) and normal progression through this stage.

I find the data presented and conclusions made to be largely convincing and that this manuscript represents a substantial contribution to the field. I recognize many of the challenges associated with this study that include assessing protein levels on small populations of cells, the heterogeneity of the cell populations (even if sorting a discrete subset, the requirement for culturing the cells +/- inhibitor invites differentiation), and the pleiotropic effects of HDAC inhibitors (HDACi). With few exceptions, we can accept these issues as the authors were clearly careful in their approaches, and there are limited other techniques that can be used to address some of these questions.

---

Major comments.

Given the effort already put into this paper, it might be worthwhile to ultimately show step-wise progression through the developmental intermediates described in this manuscript. A time course to assess differentiation of isolated DN3a cells in OP9-Dl1 coculture could be considered, for example. The authors clearly have the reagents and skills to carry out these experiments though the timing would be a factor in order to capture the appearance of discrete developmental intermediates. This would, in many ways, provide a straightforward summary of many of the reported results that would improve accessibility to a broader audience.

The differences in protein levels stated are not always so obvious based on the contour plots and/or histograms; these are often subtle effects that can be obscured by the 'noise' that accompanies the analysis of protein levels on small populations of cells. Quantification of the data should be included when making conclusions about differences in expression levels of different markers. In addition, when quantification and statistics are provided, it is clear that at least three repeats were included, but without quantification, the reproducibility of the experiments are not known; the number of replicates for each experiment should be obviously stated.

Minor points.

The impact of the inhibitor seems to be inconsistent in Fig. 6A i and ii; there is not much of an impact of the inhibitor in ii as I understand. There also seem to be significantly different expression patterns of Lef in the DN3bpre stage in the two models (OP9 vs ex vivo) - what is the explanation for this?

That the inhibitor leads to a 'loss of correlation' between Lef and CD5 levels is more obvious in Supp Fig 11 than as presented in Figure 7.

Consider adding a CD25lo population (e.g. DN4) as a reference in Supp. Fig. 12.

In reference to Fig. 5, the authors suggest the analysis of MTOC components in DN3a cells; are these Dn3a cells? DN3a cells were isolated and then cultured for a day +/- inhibitor. I presume there is some differentiation in these cultures that depends on the presence of the inhibitor. I am not suggesting that the authors need to redo this experiment but rather either acknowledge that these are not all DN3a cells (unless I am wrong here) by changing the wording, or add a marker to distinguish the subset (CD2?)

Make note of the DN3b nomenclature used; I believe that 'pro' was used instead of 'post' at least once.

In Fig 1, the populations identified as CD4+ and CD8+ are likely immature populations; unless including TCRb staining to distinguish these, I suggest excluding them from the analysis. I think the DP population is sufficient here to get the point across.

In Supp Fig 2. the schematic does not appear to be consistent with legend (2 versus 4 d of culture).

In Supp Fig 8a, the quantification of DN3a/b-pre/b-pro has a different experimental set up than in Fig 3bii but is written as if this is the quantification of the data as I understand it.

In line 214/215, it is suggested that "Analysis of the cells immediately after extraction showed clearly distinct DN3a, DN3bPre and DN3bPost cells." but I did not find the data for this.

Please confirm the experimental set up in Supp. Fig. 9. Why treat with inhibitor prior to isolating the subsets and then culturing again without inhibitor?

Eliminate conclusions made without specific reference to figures or to 'future' figures.

In some histograms (e.g. 5), it was not obvious to me what the negative controls represented. Are these fluorescence minus one, isotype, other?

In the abstract, it is suggested that increases in a number of markers provides for escalating TCR signaling strength; CD5 is among these. As a negative regulator of TCR signals, this statement seems to be counterintuitive.

The authors state that, "These data together indicate that CD5 serves as a link between TCRb expression and proliferation, ...." (line 325/326); how CD5 'links' the two is not clear.

It is written that "...at Day 8-10 of the co-culture, when cells from mouse fetal liver were predominantly at the DN3 stage of T cell development (Supp Fig 1B)...". Reconsider wording this statement as it appears as if the majority of cells actually express CD4 and/or CD8.

Referees cross-commenting

Reviewers 1 and 3 bring up important, obvious points that this reviewer missed in terms of the potential off-target effects of the HDACi on the stromal cell component of the co-culture system used for the experiments. It is difficult to determine the relevance of HDAC6 at this developmental checkpoint without additional controls

Significance

As an immunologist with an interest in the molecular and cellular mechanisms that regulate T cell development, I find this manuscript interesting for several reasons.

One of the benefits of studying development and differentiation in the immune system is the ability to distinguish discrete developmental intermediates by flow cytometry using defined panels of cell surface and intracellular markers; this allows for the isolation of populations of cells for testing progenitor/progeny relationships, to identify the role of essential genes at various developmental stages and beyond. This manuscript adds important new markers that will allow researchers to more discretely tease apart important stages in T cell development during an important regulatory checkpoint.

Not only is beta-selection an essential first step in ensuring a functional antigen receptor repertoire during T cell development, but its tight regulation is absolutely necessary due to the double-strand DNA breaks that accompany antigen receptor gene rearrangement and the massive proliferation that ensues after successful pairing of a functionally rearranged TCRb chain with the preTCRa; indeed, dysregulation at the beta-selection checkpoint can give rise to leukemia. This study provides new insight into potential mechanisms of beta-selection regulation.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this work, Russell and colleagues study the differentiation steps of thymocytes around the time of expression and function of the pre-TCR. They use CD2 as a new marker of an intermediate population of differentiation between DN3a thymocytes and DN4 thymocytes. The CD2+ thymocytes would be and a later stage of differentiation than the CD2 negative ones. In this way, they define a DN3b-Pre and a DN3b-Post populations. The study also aims to study the role of histone deacetylase HDAC6 in thymocytes differentiation at the time of pre-TCR signaling by using as a tool the inhibitor ACY1215 and conclude that HDAC plays an important role during the DN3-DN4 transition. The method the authors use to study consist of the sorting of precursor cells from fetal or adult thymuses and studying the effect of the inhibitor during differentiation in vitro promoted by interaction of the thymocytes with the OP9-DL1 cell line, a well-characterized cell line that expresses a ligand of Notch and promotes DN3 differentiation up to the DP stage.

There are major concerns with the approach used by the researchers that make their conclusions unsustainable.

1. They use the inhibitor ACY1215 in the co-culture of thymocytes with OP9-DL1 cells to examine the effect of HDAC inhibition in thymocytes on their differentiation. However, the authors do not provide any control result showing that the effects detected on differentiation are not caused by the activity of the inhibitor on OP9-DL1 cells and not on thymocytes. This possibility is not excluded and if the inhibitor were acting on OP9 cells would invalidate completely the conclusions of the study.
2. The inhibitor is used at a single concentration (one has to search in the Methods section in order to find that it is 1 micromolar) and there is no evidence provided of dose-response effects. Furthermore, experiments are missing in which different doses of the inhibitor are tested on its potential targets and shown to have a selective impact on those targets at the concentration used in the study.
3. The authors suggest that the inhibitor is a epigenetic regulator because it acts on the deacetylatio of histones but also that it acts on the formation of a potential immunological synapse by the pre-TCR expressing thymocytes with inhibition of the translocation of the microtubule organizing centre. By the end of the study, one does not know exactly how is the inhibitor acting on pre-T cell differentiation.
4. The authors seem to postulate a model in which the effect of the inhibitor on the immunological synapse and pre-TCR signaling affects the expression of Lef1 which itself modulates histone deacetylation. Therefore, the inhibition of HDAC6 would be acting on pre-TCR signaling upstream but also on the activity of Lef1 downstream. It seems that the approach is not sufficiently precise as to discriminate the site of action of the inhibitor
5. The authors use contour plots to display their data. This has the advantage of defining cell populations but on the other hand, hides the number of events that are defining the populations. This is for instance reflected in Figure 7 panel B where the CD5 vs surface TCRbeta plot of cultured DN3a thymocytes shows many different populations (in green) which are probably artifacts of the contour plot. Very likely such populations are formed by very few events
6. I do not see a big effect of the inhibitor on Lef 1 expression (Figure 6A) and if the inhibitor has an effect at the DN3b-Pre stage why it should not have it at the DN3b-Post stage.
7. Suppl. Fig. 11.-In DN3b-Post, expression of CD5 is higher than in DN3a but not so clearly higher than in DN3b-Pre. The effect of the inhibitor on DN3b-Post was that of reducing CD5 expression but not Lef1 expression. In this experiment, the effect of the inhibitor of Lef1 expression by DN3b-Pre is not seen. Quantitation? The inhibitor could be altering CD5 expression by inhibiting the synapse independent of Lef1 ?
8. Figure 8. The populations defined by CFSE staining are too broad in terms of fluorescence intensity as to determine number of cell divisions. It seems that there are only two populations: one that has not diluted CFSE and therefore has not divided and another that has diluted CFSE and has divided. How many times? we do not know. On the other hand, CD5 is increased in cells that have diluted CFSE. Have they expressed CD4, CD8, downregulated CD25, other markers indicating that the cells are not longer DN3a or DN3b? CD5 is upregulated after CFSE dilution not before dilution, so is CD5 expression cause or effect of differentiation.The effect of the inhibitor is not clear.

Referees cross-commenting

Totally in agreement! The effect of the drug could be on the OP9-DL1 cells and not on thymocytes. This is not proven

Significance

With all the concerns about the method used by the authors to define subpopulations in DN3-DN4 transition and the involvement of HDAC6 activity I do not believe the paper will have a significant impact in the field. The authors will need to rethink their approaches in order to investigate the subject with sufficient guarantees. Perhaps using genetic approaches.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Autophagy of the endoplasmic reticulum (ER-phagy) is a fundamental process that is essential for maintaining cellular homeostasis and quality control. We recently identified a novel mechanism regulating ER-phagy in both plants and animals that is based on the ubiquitin-like protein modifiers ATG8 and UFM1, and the ER-associated protein, C53. Here, we use a combination of evolutionary, biochemical, and physiological experiments to investigate the evolution and regulation of this process. We reveal the dynamic evolution of UFM1 and the ubiquity of C53-mediated autophagy across eukaryotes. Leveraging these results, we then identify an ancestral molecular toggle switch, mediated by shuffled ATG8-interacting motifs (sAIMs), that controls C53-mediated autophagy through competitive binding between UFM1 and ATG8. These findings provide new insights into the evolution of UFM1, reveal a conserved mechanism for the regulation of ER-phagy, and raise new and exciting hypotheses about the diversity and function of the UFMylation pathway. We believe that this work will be of interest to those studying autophagy and cellular stress response but will also serve as an interesting example of the benefits of combining evolutionary analyses with biochemical and cellular experiments.

Our manuscript has been reviewed by three reviewers through ReviewCommons, whose comments, and our responses, can be found below. Two of the reviewers (Reviewer 1 and 3) were supportive of our work and its significance whereas Reviewer 2 questioned the novelty of our findings.

Each of the reviewers’ comments can be addressed through a few supporting experiments as well as an improved manuscript which clarifies the novelty and significance of our results. While being supportive of our work, Reviewer 1 requested minor additional experiments to support our mechanistic conclusions and Reviewer 3 suggested that we expand our characterizations of C53 function to additional eukaryotic supergroups. These experiments are straightforward to perform, the materials and protocols to accomplish them are already established, and our overall conclusions are robust to the resulting outcomes.

In contrast, Reviewer 2 did not suggest any additional experiments but rather challenged the novelty of our results as well as some of our interpretations. In particular, Reviewer 2 was uncertain of how our phylogenomic analyses built upon a previous study, published in 2014, which used comparative genomics to identify ubiquitin-related machinery across eukaryotes. Although it was an oversight to not reference this study (we cited a more recent article showing the same results), we were aware of their conclusions that UFMylation was present in the last eukaryotic common ancestor but absent in Fungi. We now clearly outline, both below and within the manuscript, our key phylogenomic results. These were acquired after implementing more advanced and comprehensive comparative genomic searches which allowed us to identify dynamic patterns in UFMylation evolution and permitted co-evolutionary analyses which were not only important for informing our experimental hypotheses but generated new functional questions. Our phylogenomic analyses are also linked to biochemical and physiological data, providing, for the first time, experimental support for our conclusions regarding UFMylation evolution. Similarly, Reviewer 2 suggested that our mechanistic results were an incremental extension of our previous work. Although our current work does of course build on our initial identification of C53-mediated autophagy, this manuscript provides novel insights into the importance and function of this process by revealing its ubiquity across eukaryotes and by characterizing the mechanistic details of its regulation. Ultimately, we disagree with Reviewer 2 but appreciate that this misunderstanding likely resulted from a lack of context and clarity in our manuscript which we have now resolved.

As outlined in detail below, we will address the reviewers concerns through additional experiments, analyses, and improvements to the text.

Thank you for considering our manuscript. We look forward to hearing from you.

Description of the planned revisions

We thank the reviewers for carefully evaluating our manuscript and for providing us with an opportunity to respond to their suggestions and criticisms. As you can see below in our pointby-point response, we address each of the points raised by the reviewers through the addition of supporting experiments, analyses, and an improved text. Altogether, we think these additional experiments and textual changes will significantly improve the manuscript. Therefore, we would like to thank all the reviewers and editors for their time and input.

Referee #1

Evidence, reproducibility and clarity

In this manuscript Picchianti et al. provide novel insights into the interaction of C53 with UFM1 and ATG8. Initially, the authors show that protein modification by UFM1 exists in the unicellular organism Chlamydomonas reinhardtii. To that end they demonstrated that pure Chlamydomonas UBA5, UFC1 and UFM1 proteins, can charge UFC1. Then, they showed that C53 interacts with ATG8 and UFM1. Specifically, they found that the sAIM are essential for the interaction with UFM1, while substituting this motif with canonical AIM prevents the binding of UFM1 but not of ATG8. Since binding of C53 to ATG8 recruits the autophagy machinery, the authors suggest that ufmylation of RPL26 releases UFM1 from C53 which allows the binding of ATG8. Overall, the authors demonstrate that C53 that forms a complex with UFL1 connects between protein ufmylation and autophagy by its ability to bind both UBLs. Here the authors revisited the assumption that only multicellular organisms have the UFM1 system. Using bioinformatic tools they show that it exists also in unicellular organism. Also, they show that in some organisms the E3 complex UFL1, UFBP1 and C53 exist but not UBA5, UFC1 or UFM1. This is a very interesting observation that suggests an additional role for this complex. In Fig 1C the authors show that in Chlamydomonas RPL26 undergoes ufmylation. Please use IP against RPL26 and then a blot with anti UFM1. From the current experiment it is not clear how the authors know that this is indeed RPL26 that undergoes ufmylation

RPL26 is highly conserved across eukaryotes, so by comparing our western blots with previous studies (Walczak et. al., 2019, Wang et al. 2020), we concluded that these bands corresponded to UFMylated RPL26. However, we agree with the reviewer that we need to confirm the identify of RPL26 with additional assays. Since the submission of the manuscript, we tested RPL26 antibodies in Chlamydomonas and showed that they work well. So, we will update our figure with the confirmation westerns.

In the second part of the manuscript the authors characterize the interaction of C53 with ATG8 and UFM1. This is a continuation of their previous published work (Stephani et al, 2020). Here the reviewer thinks that further data on the binding of these proteins to C53 is required. Specifically, defining the Kd of these interactions using ITC or other biophysical method can contribute to the study.

We agree with the reviewer. To obtain the KD values, we will perform ITC experiments with C53 wild type, a C53 sAIM mutant and a C53 cAIM variant titrated with ATG8 and UFM1.

Under normal condition the authors suggest that C53 binds UFM1 and this keeps it inactive. The reviewer thinks that this claim needs further support. Using IP (maybe with crosslinker) the author can show that C53, in normal conditions, bind more UFM1 than ATG8. Also, since the interaction of UFM1 to C53 is noncovalent, it will be nice to show how alternations in UFM1 expression levels can affect the activation of C53.

We thank the reviewer for this suggestion. Since the submission of the manuscript, we have obtained UFM1 overexpression lines. We will pull on C53 using our C53 antibody and check for ATG8 levels in wild type and UFM1 overexpressing lines under normal and stress conditions. We think this will show how alterations in UFM1 levels can affect C53 activation.

Finally, the authors suggest that ufmylation of RPL26 allows binding of ATG8 to C53 and this, in turn, leads to C53 activation. Can the authors show that in cells lacking UBA5, under normal condition or with Tunicamycin treatment, ATG8 does not activate C53 due to the fact that UFM1 does not leave C53.

In Stephani et al., we showed that C53-mediated autophagy requires the UFMylation machinery. In ufl1 and ddrgk1 mutants, C53 becomes insensitive to ER stress. However, to supplement these results, we will perform autophagic flux assays using the native C53 antibody to test autophagic degradation of C53 in a uba5 and ufc1 mutant under normal and tunicamycin stress conditions. The uba5 mutant that we have is a knockdown, so that’s why we will include the ufc1 mutant in our experiments.

Significance

This manuscript advances our understanding of the connection of ufmylation to autophagy which is mediated by C53.

Thank you!

Referee #2

Evidence, reproducibility and clarity

The manuscript from Picchianti et al. seeks to define the role of CDK5RAP3 (hereinafter referred as C53) during autophagy and its interplay with UFMylation. Together with UFL1 and DDRGK1, C53 is a component of a trimeric UFM1 E3 ligase complex that modifies the 60S ribosomal protein RPL26 at the endoplasmic reticulum (ER) surface upon ribosomal stalling (among other proposed functions that are not addressed). Several previous studies have implicated the UFMylation pathway in autophagy or ER-phagy although a non-autophagic fate for UFM1- tagged ribosomal subunits has also been reported. A previous study from the same authors (PMID: 32851973) identified an intrinsically disorder region (IDR) in C53 that is necessary and sufficient for interaction between C53 and autophagy receptor, ATG8. They reported that this IDR comprises four non canonical ATG8 interacting motifs (AIM), named shuffled AIMs (sAIMs) and showed that combinatorial mutagenesis of sAIM1, sAIM2, and sAIM3 abrogates ATG8 binding. A similar effect was observed for plant C53, though an additional canonical AIM (cAIM) in the C53 IDR had to be mutated to completely abolish C53 and ATG8 interaction. The earlier study reported that C53 IDR also interacts with UFM1, and this interaction can be disrupted in vitro by adding increasing concentration of ATG8, suggesting that ATG8 and UFM1 may compete with one another for C53 binding. The present paper attempts to build on this previous work by using phylogenomics to infer a coevolutionary relationship between UFMylation machinery and sAIMs in C53, which the authors argue, constitutes further evidence of the primary importance of a role for UFMylation in ER homeostasis. The manuscript includes a lot of biochemical data using variations of in vitro and in vivo pull-down experiments to define the roles of individual AIMs in mediating the binding of C53 to ATG8 and to UFM1. They also use NMR spectroscopy in an attempt to define the structural basis of the UFM1 and ATG8 binding to C53, concluding that plant C53 interacts with UFM1 mainly through sAIM1, while interaction with ATG8 requires cAIM as well as sAIM1 and sAIM2. Finally, the authors attempt to contextualize these findings by conducting studies on Arabidopsis mutants, showing that replacing sAIMs with cAIMs causes increases sensitivity to ER stress and apparently increases formation of C53 intracellular puncta that may colocalize with ATG8. From these data the authors concluded that the dual-ATG8 and UFM1 binding of C53 IDR regulates C53 recruitment to autophagosomes in response to ER stress. Major Issues: 1) The phylogenomics analysis conclusion that UFM1 is common in unicellular lineages and did not evolve in multicellular eukaryotes is not novel, as another comprehensive analysis of UFM1 phylogeny, published eight years ago - in 2014 - by Grau-Bové et al. (PMID: 25525215), also reported that UFM1, UBA5, UFC1, UFL1 and UFSP2 were likely present in LECA and lost in Fungi. Although the phylogenomic analysis by Picchianti et al. is also extended to DDRGK1 and C53 proteins, and some parasitic and algal lineages, their findings are incremental. Their proposed coevolution of sAIM and UFM1 is based on presence-absence correlation observed within five species (i.e., Albugo candida, Albuco laibachii, Piromyces finnis, Neocallimastix californiae, Anaeromyces robustus). However, this coevolutionary relationship must be further investigated by substantially increasing the taxonomic sampling within the UFM1-lacking group.

We were aware that previous studies had investigated the distribution of UFMylation proteins across eukaryotes and that these analyses had predicted the presence of UFMylation in LECA and subsequent loss in Fungi. We included a more recent citation noting this (Tsaban et al. 2021) but apologise for not citing Grau-Bové et al. (2014), which we have now included. We must emphasize that our results are not incremental. Although we had made a point of emphasizing the presence of UFM1 in LECA, this was to counter a recent and highly cited paper in the field which claimed that UFMylation evolved in plants and animals (Walczak et al. 2019). Below we note the novel and important results from our phylogenomic analyses: 1. We used improved taxonomic sampling and more advanced comparative genomics methods to identify UFMylation components sensitively and specifically across eukaryotes. This involved the inclusion of additional eukaryotic genomes, phylogenetic annotation of orthologs, and genomic searches to complement proteome predictions. These methods are essential for accurately identifying UFMylation components and yield more robust results than using sequence similarity clustering (Tsaban et al. 2021) or un-curated Pfam HMMER search results (Grau-Bové et al. 2014). 2. By placing our UFMylation reconstructions in a modern phylogenetic context we were not only able to support previous observations which noted the presence of UFM1 in LECA and its loss in Fungi (Grau-Bové et al. 2014) and Plasmodium (Tsaban et al. 2021), but also to identify novel patterns in the evolution of UFMylation. This included the observation of recurrent losses in diverse but trophically-related lineages (such as algae and parasites) and revealed the retention of certain UFMylation components in the absence of UFM1. We identified the frequent coretention of UFL1 and DDRGK1 following UFM1 loss in multiple eukaryotic groups, including Fungi, which were previously thought to be devoid of UFMylation machinery. These previously uncharacterized patterns, suggest that these proteins could have alternative functions and may be functionally associated with life history. These results therefore expand on and add complexity to our understanding of the evolution of UFMylation. 3. By conducting a comprehensive and accurate survey of UFMylation components we were able to use our data to examine co-evolutionary trends between C53 and UFM1, which would have been incomplete and inaccurate using previously curated datasets. As the reviewer noted, only five species were identified that encoded C53 but lacked UFM1. This is not a reflection of insufficient taxon sampling, but rather the strong co-evolution between C53 and UFM1 (i.e., when UFM1 is lost, C53 is almost always lost as well). We attempted to identify additional cases by searching hundreds of fungal and oomycete genomes as well as those from other eukaryotes, but no other species were found. We agree with the reviewer that additional taxa would have made our analyses stronger, but importantly, we do not rely on genomic correlations to infer function. Rather, we use these correlations to generate functional hypotheses which we then tested experimentally. In this way, we do not rely on the strength of our correlations. We have now revised the manuscript to include additional context (including citations) and have improved the clarity of the text to better convey the novelty of our findings.

2) The manuscript presents an overwhelming amount of biochemical and structural data obtained from a variety of protein binding techniques (i.e., NMR spectroscopy, in vitro GSTpulldown, fluorescence microscopy-based on-bead binding assays, and native massspectrometry). The results are poorly explained and not organized in a logical manner. Moreover, no attempt was made to explain the rationale behind using one technique over the other or how one method complements another to build a stronger conclusion than any individual approach. Given that none of the methods employed report quantitative measurement of binding affinities between C53 IDR and UFM1 or ATG8, it is not clear how the data presented in this manuscript contribute to our understanding of the proposed competition model for UFM1 and ATG8 binding to C53 IDR. To conclude that an interaction is "stronger" or "weaker" it is necessary to measure equilibrium binding constants. Fortunately, there are suitable techniques, including surface plasmon resonance (SPR), microscale thermophoresis (MST), fluorescence anisotropy, or calorimetry that are available to dissect these complex competitive binding interactions and to build models.

We thank the reviewer for their suggestion. Although we attempted to describe the rationale behind each experiment (please see the line 135-137; on-bead binding assays, line154-157; NMR, 177-181), we agree that the volume of data and variety of techniques warrants additional explanation. We will revise the manuscript to further explain our rationale for using each of the different approaches. As we noted above in our response to reviewer 1, we will also perform relevant ITC binding assays to quantify the interaction between C53, ATG8, and UFM1.

3) The NMR studies have the potential to dissect the types of dynamic binding inherent in unstructured proteins. However, the abundant NMR data presented combined with the aforementioned binding studies, remarkably, do not seem to significantly advance our understanding of how the system is organized or even how UFM1 and ATG8 bind C53, beyond the rather vague and somewhat circular conclusion stated in the abstract: "...we confirmed the interaction of UFM1 with the C53 sAIMs and found that UFM1 and ATG8 bound the sAIMs in a different mode." Or on line 165 "Altogether these results suggested that ATG8 and UFM1 bind the sAIMs withn C54 IDR, albeit in a different manner".

We agree that NMR has the potential to dissect the complex binding interactions between UFM1, ATG8, and C53, but disagree with the reviewer’s interpretation that our NMR data fail to achieve this. To sum up, our NMR data: 1. Revealed the structural basis of the interaction of C53-IDR with ATG8 and UFM1 at atomic resolution by showing that UFM1 binds preferentially to sAIM1 in the fast-intermediate exchange [Fig.4 and Fig. S7B], instead ATG8 binds cAIM in the slow-intermediate exchange, and once cAIM is occupied, it binds sAIM1,2 with lower affinity in the fast-intermediate exchange (Fig.4 and Fig.S7D). 2. Determined conformational changes in C53 IDR upon binding of ATG8, but not UFM1 (Fig.S7E), which lead to increased dynamics in distinct regions in C53 IDR. These data could explain how binding of first ATG8 would trigger C53-dependent recruitment of the tripartite complex to autophagosomes. 3. Identified how UFM1 binds to atypical hydrophobic patch in C53 sAIM, similar to what was shown for the UBA5 LIR/UFIM. To sum up, our results shed light on how both UBLs interact with C53, being sAIM1 the highest affinity binding site for UFM1 while ATG8 binds cAIM preferentially before occupying sAIM1,2. To provide more detailed information on the atomic details of the interaction between C53 and the UBLs, we will perform molecular docking studies by using the restraints obtained from the experimental NMR data.

4) The functional assays performed in Arabidopsis do not support the competitive model between UFM1 and ATG8 for binding to C53 during C53-mediated autophagy. The fluorescence microscopy images do not provide convincing evidence of colocalization between C53 and ATG8. In fact, in contrast to the claims made in the text or the quantification, mCherry-C53 fluorescence does not seem to localize in discrete puncta and its signal does not seem to overlap with ATG8A.

We disagree with the reviewer’s interpretation of these results although we acknowledge that there is some subtlety in interpreting the co-localization data. Importantly, Arabidopsis has 9 ATG8 isoforms and C53 can bind to most of them with varying affinities (see Stephani et al). Because of this, we do not expect C53 puncta to fully colocalize with ATG8A puncta. Additionally, the C53 puncta are smaller and more subtle than ATG8 puncta, which label the entire autophagosome. To reconcile this, we will quantify the effect by performing colocalization analyses under normal and stress conditions. We will also upload all the raw images as supporting material, so that anyone can independently assess our images.

Minor Issues: 1. The authors might choose to avoid teleological arguments such as (line 135): "As the phylogenomic analysis suggested that eh sAIMs have been retained to mediate C53-UFM1 interaction..."

We thank the reviewer for this suggestion and will modify the text accordingly.

1. The authors refer on multiple occasions to C53 "autoactivation" without defining what they mean by this. Do they propose that C53 UFMylates itself?.

We refer to C53 activity as the ability to recruit the autophagy machinery and initiate cargo sequestration and degradation in the vacuole. We attempted to explain this in lines 57-61 but we will reword it more clearly, as suggested by the reviewer.

1. The paper might want to avoid preachy philosophical statements like "Our evolutionary analysis also highlights why we should move beyond yeast and metazoans and instead consider the whole tree of life when using evolutionary arguments to guide biological research." (333- 335). While this is indeed a laudable goal, given the rather limited insights from this study, it is unclear how this paper exemplifies the notion.

We added this statement as we were intrigued by our evolutionary analyses’ ability to link C53 to UFM1 (an association which took years to identify experimentally) and generate useful functional hypotheses about the interaction between C53 sAIMs and UFM1. As we mentioned above, we also wanted to highlight this point in reference to a recent prominent study in the field which drew conclusions after only considering animals, plants, and fungi (Walczak et al., 2019). We believe this point is important and underappreciated by some cell biologists, but we will modify the text to make it more generic: “This work highlights the utility of using evolutionary analyses and eukaryotic diversity to generate mechanistic hypotheses for cellular processes”.

Significance

Overall, while the manuscript contains an abundance of new data, the overall conclusion of the work, stated in the title: "Shuffled ATG8 interacting motifs form an ancestral bridge between UFMylation and C53-mediated autophagy" does not constitute a significant advance beyond other published phylogenomic analysis (below) and the two previous papers by the same authors, including the 2020 paper "A cross-kingdom conserved ER-phagy receptor maintains endoplasmic reticulum homeostasis during stress (PMID: 32851973)" and the 2021 paper "C53 is a cross-kingdom conserved reticulophagy receptor that bridges the gap between selective autophagy and ribosome stalling at the endoplasmic reticulum PMID: 33164651)". While a regulatory interaction between UFMylation and autophagy is of potential importance, the data in this manuscript do not constitute a major advance and fail to provide new mechanistic insight to explain the role of C53 IDR in autophagy and its interplay with UFMylation

We disagree with the reviewer’s suggestion that our work does not constitute a significant advance. We outlined above in detail the novel insights that were obtained from our phylogenomic analysis which involved using improved methods to reveal a much more dynamic and informative picture of UFMylation evolution than has been described previously. Likewise, this manuscript builds substantially on our previous mechanistic work. In our 2020 paper (which is summarized in the mentioned 2021 review article), we identified C53 as an ER-associated protein that binds ATG8 through sAIMs and interacts with the phagophore after RPL26 UFMylation. This work linked C53 activity to ER-phagy and highlighted its importance in plant and animal stress response. However, key questions remained unanswered prior to our current work such as whether this mechanism is conserved across eukaryotes, especially in unicellular species, how C53 activity is regulated, and how UFM1 and ATG8 interact with C53. Our current manuscript builds on this work with the following key results: 1. We use a combination of phylogenomic and experimental analyses to demonstrate that C53 function is conserved across eukaryotes. 2. We reveal a mechanism whereby UFM1 and ATG8 compete for binding at the sAIMs in the C53 IDR and characterize how each of these ubiquitin-like proteins interacts in an alternative way (see the NMR results described above). 3. We show how the sAIMs are required for the regulation of C53-mediated autophagy and reveal the importance of UFM1-ATG8 competition in preventing C53 autoactivation, which causes unnecessary autophagic degradation and impairs cellular stress responses.

These insights are fundamental for understanding the mechanisms regulating C53-mediated autophagy which were unknown before this work. We will therefore adjust our manuscript to more clearly and explicitly explain how our data build on previous observations so that the novelty and significance of our results are clearer.

Referee #3

Evidence, reproducibility and clarity

Picchianti and colleagues have investigated a conserved molecular framework that orchestrates ER homeostasis via autophagy. For this, they have carried out phylogenomics and large-scale gene family analyses across eukaryote diversity as well as a barrage of molecular lab work. The amount of work carried out as well as the overall quality of the study is impressive.

Thank you!

I have only a few comments that should be very easy to tackle. (1) Maybe I missed it, but please upload all alignments used for phylogenetics and phylogenomics for reproducibility to e.g. Zenodo, Figshare or other suitable OA databases.

We included the alignments in the supplementary data, but as suggested, we will upload all the source data including the scripts and the alignments to Zenodo.

(2) "Why these non-canonical motifs were selected during evolution, instead of canonical ATG8 interacting motifs remains unknown" --> Maybe there is no "why" and these were not selected at all. Could be random... drift, non-adaptive constructive neutral evolution. I am not saying that asking "why" in evolutionary biology is wrong. It, however, often does not yield satisfactory answers--or any answer at all.

The reviewer is completely right that “why” is not the right way to frame an evolutionary question. Thank you for pointing this out. We will revise the text and make sure that we remove these kinds of deterministic statements.

(3) The authors make a case for UFMylation in LECA and I am fully sympathetic with this. However, getting rid of misfoled/problematic proteins and subcellular entities is something that prokaryotes also to a certain degree must have (and still do) master. Are inclusion bodies or export their only answers (I don't know)? Of course, in eukaryotes with all their intracellular complexity this is likely more of an issue. Given the scope of this manuscript (i.e. shedding light on that ancient framework, deep evolutionary roots in eukaryote evolution etc. etc.) it would be very interesting to read the authors thoughts on this and also pinpoint the prokaryote/eukaryote divide in light of the machinery discussed here.

Thank you for this suggestion. We did indeed check whether any of the UFMylation machinery were present in prokaryotes and only found homologs of UFSP2. These results are consistent with Grau-Bové et al. (2014) who conducted an equivalent analysis and concluded that UFMylation machinery were derived during eukaryogenesis. We will make reference to this in the revised manuscript.

Significance

This study not only impresses with the volume of experiments and data, but also the courage to show conservation of a molecular framework by working with such a range of distantly-related eukaryotes. The results and conclusions from this study should be interesting to anyone working in the broad fields of cellular stress and/or autophagy--both extremely timely topics.

We thank the reviewer for understanding our take-home message and the advances made. We especially thank the reviewer for understanding the challenge of connecting in silico genomic data with in vivo and in vitro experiments.

CROSS-CONSULTATION COMMENTS

Referee #2 The challenge in providing a fair review of this manuscript is to clearly define what contributions are novel, significant advances. It is difficult to tell the way the manuscript is written, as it is unclear how the new data - which are voluminous- actually advance the model already put forth by the same authors in two previous publications. It is also unfortunate that the authors overlooked the 2004 phylogenomics paper. There clearly are some new pieces of information here, but the overall increment in knowledge is rather minimal. Response from Referee #3 I agree that the authors somehow steamroll the reader with a wealth of data. But I think this can be addressed by the authors by requesting a lot more justification and by giving them the opportunity to put the significant advances into their own words. This is, in my opinion, quite doable in course of a revision. Overall I have to say that I am very sympathetic with the crosseukaryote reactivity approach that the authors have taken. It is quite intriguing.

We thank the reviewers for this useful exchange. We agree that our manuscript was not clear enough to emphasize the novelty of our results which likely resulted from the volume and diversity of the experiments and analyses that were presented. We have now revised the manuscript to improve the context and rationale for the study, the intent and hypotheses behind each experiment, and the novel results and insights obtained in each section.

Response from Referee #2 I agree that the cross-eukaryote approach is intriguing. Shouldn't we be concerned that the 2004 publication already made two of their key points (ie present in LECA, loss in Fungi). What is the incremental insight from this paper? I'd appreciate an opinion from an evolutionary biologist as to how strongly one can conclude functional co-evolution from such correlative data, especially given the rather small number of supporting examples. Is it also necessary to consider counter-examples- ie species that have sAIMs but no UFM1 (I believe that they found a few such cases)?

Importantly, we do not conclude functional co-evolution from our correlative data. Instead, we used these correlations to generate hypotheses that we tested with various experiments in different model systems. For example, the apparent correlation between C53 sAIMs and UFM1 prompted us to test whether or not UFM1 and sAIMs interact. Regardless of sample size or statistical significance, phylogenomic analyses can never demonstrate functional links, only correlations, which is why we combined these two approaches. Although only a few species encoded C53 without UFM1, each of these contained C53 cAIMs and lacked sAIMs (Figure 2c). There are species with UFM1 that lack C53 but this makes sense as UFM1 is used in other processes besides ER-phagy. We have revised the text to make our approach and reliance on certain data clearer.

Response from Referee #3 Well with these deep evolutionary questions this is always a challenge. Where does one stop to sample more homologs for one's analyses (one from each supergroup [which are no longer recognised by the community])? In that sense, the authors are right to make the parsimonious base assumption that if X and Y interact in species A and B (no matter how distant they are related) then X and Y interacted in the last common ancestor of A and B. That being said, if I would have designed this study, I would have sampled more broadly for my in vitro crosseukaryote approach. But also this, I think, could be carried out by the authors in a reasonable timeframe. Specifically, they have now sampled from Amorphea and Archaeplastida, they should add one from TSAR, one Haptista, one Cryptista, and one CRuM. If they synthesised the proteins via a company, they could have the constructs in a few weeks for about 1K Euro - I do not think that this would be an unreasonable request.

We agree that testing C53 function in additional species would strengthen our understanding of the conservation of this pathway across eukaryotes, as it cannot be assumed that orthologous proteins will function in the same way across all species. To our knowledge there is no other work showing experimentally that the UFMylation pathway is working in a single-celled organism. We focussed our efforts on the unicellular green alga, Chlamydomonas due to its relative experimental tractability. However, testing this was not trivial as it required us to establish expression and purification protocols, isolate Chlamydomonas mutants, optimize physiological stress assays, and perform the experiments.

Nevertheless, we agree that we could expand our in vitro assays with C53 orthologs from additional species. As suggested by reviewer 3, we will now synthesize 6 more C53 isoforms from two TSAR representatives (the alveolate, Tetrahymena thermophila, and the stramenopile, Phytophthora sojae), as well as a representative from Haptista (Emiliania), Cryptista (Guillardia), Diplomonada (Trypanosoma), and CRuMs (Rigifila). We will test their interaction with human and plant ATG8 and UFM1 proteins. We have also added two species from CRuMs into our phylogenomic analysis.

The list of experiments that we can do to address the reviewer’s concerns: 1. Repeat experiment in Figure 1C probing with �-RPL26. 2. To calculate KD values, perform ITC experiments with C53 wild-type, C53 sAIM mutant and C53 cAIM variant titrated with ATG8 and UFM1. 3. Perform CoIP experiments using C53 antibody in wild type and UFM1 overexpressing lines and detect for ATG8 association, under normal and stress conditions. 4. We will test autophagic degradation of C53 in uba5 and ufc1 mutants under normal and tunicamycin stress conditions by performing autophagic flux assays using the native C53 antibody 5. Molecular docking studies to see C53’s structural rearrangements leading to ATG8 and UFM1 binding. 6. Figures from co-localization experiments in Figure 5G will be revisited and we will perform additional co-localization analyses such as Pearson coefficient under normal and stress conditions. We will also upload all the raw images as supporting material, so that anyone can independently assess our images. 7. We will upload all the source data for phylogenomic analyses, including scripts and alignments to Zenodo. 8. Test the interaction of 6 newly synthesised C53 isoforms from: (1) an alveolate (tsAr, Ciliate), (2) a stramenopile (tSar, Phaeodactylum), (3) a haptophyte (Emiliania), (4) a cryptophyte (Guillardia), (5) a diplomonad (Trypanosoma) and (6) a CrRuM with human and plant ATG8 and UFM1 proteins.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Picchianti and colleagues have investigated a conserved molecular framework that orchestrates ER homeostasis via autophagy. For this, they have carried out phylogenomics and large-scale gene family analyses across eukaryote diversity as well as a barrage of molecular lab work. The amount of work carried out as well as the overall quality of the study is impressive. I have only a few comments that should be very easy to tackle.

1. Maybe I missed it, but please upload all alignments used for phylogenetics and phylogenomics for reproducibility to e.g. Zenodo, Figshare or other suitable OA databases.
2. "Why these non-canonical motifs were selected during evolution, instead of canonical ATG8 interacting motifs remains unknown" --> Maybe there is no "why" and these were not selected at all. Could be random... drift, non-adaptive constructive neutral evolution. I am not saying that asking "why" in evolutionary biology is wrong. It, however, often does not yield satisfactory answers--or any answer at all.
3. The authors make a case for UFMylation in LECA and I am fully sympathetic with this. However, getting rid of misfoled/problematic proteins and subcellular entities is something that prokaryotes also to a certain degree must have (and still do) master. Are inclusion bodies or export their only answers (I don't know)? Of course, in eukaryotes with all their intracellular complexity this is likely more of an issue. Given the scope of this manuscript (i.e. shedding light on that ancient framework, deep evolutionary roots in eukaryote evolution etc. etc.) it would be very interesting to read the authors thoughts on this and also pinpoint the prokaryote/eukaryote divide in light of the machinery discussed here.

Referees cross-commenting

Referee #2

The challenge in providing a fair review of this manuscript is to clearly define what contributions are novel, significant advances. It is difficult to tell the way the manuscript is written, as it is unclear how the new data - which are voluminous- actually advance the model already put forth by the same authors in two previous publications. It is also unfortunate that the authors overlooked the 2004 phylogenomics paper. There clearly are some new pieces of information here, but the overall increment in knowledge is rather minimal.

Response from Referee #3

I agree that the authors somehow steamroll the reader with a wealth of data. But I think this can be addressed by the authors by requesting a lot more justification and by giving them the opportunity to put the significant advances into their own words. This is, in my opinion, quite doable in course of a revision. Overall I have to say that I am very sympathetic with the cross-eukaryote reactivity approach that the authors have taken. It is quite intriguing.

Response from Referee #2

I agree that the cross-eukaryote approach is intriguing. Shouldn't we be concerned that the 2004 publication already made two of their key points (ie present in LECA, loss in Fungi). What is the incremental insight from this paper?

I'd appreciate an opinion from an evolutionary biologist as to how strongly one can conclude functional co-evolution from such correlative data, especially given the rather small number of supporting examples. Is it also necessary to consider counter-examples- ie species that have sAIMs but no UFM1 (I believe that they found a few such cases)?

Response from Referee #3

Well with these deep evolutionary questions this is always a challenge. Where does one stop to sample more homologs for one's analyses (one from each supergroup [which are no longer recognised by the community])? In that sense, the authors are right to make the parsimonious base assumption that if X and Y interact in species A and B (no matter how distant they are related) then X and Y interacted in the last common ancestor of A and B. That being said, if I would have designed this study, I would have sampled more broadly for my in vitro cross-eukaryote approach. But also this, I think, could be carried out by the authors in a reasonable timeframe. Specifically, they have now sampled from Amorphea and Archaeplastida, they should add one from TSAR, one Haptista, one Cryptista, and one CRuM. If they synthesised the proteins via a company, they could have the constructs in a few weeks for about 1K Euro - I do not think that this would be an unreasonable request.

Significance

This study not only impresses with the volume of experiments and data, but also the courage to show conservation of a molecular framework by working with such a range of distantly-related eukaryotes. The results and conclusions from this study should be interesting to anyone working in the broad fields of cellular stress and/or autophagy--both extremely timely topics.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The manuscript from Picchianti et al. seeks to define the role of CDK5RAP3 (hereinafter referred as C53) during autophagy and its interplay with UFMylation. Together with UFL1 and DDRGK1, C53 is a component of a trimeric UFM1 E3 ligase complex that modifies the 60S ribosomal protein RPL26 at the endoplasmic reticulum (ER) surface upon ribosomal stalling (among other proposed functions that are not addressed). Several previous studies have implicated the UFMylation pathway in autophagy or ER-phagy although a non-autophagic fate for UFM1-tagged ribosomal subunits has also been reported.

A previous study from the same authors (PMID: 32851973) identified an intrinsically disorder region (IDR) in C53 that is necessary and sufficient for interaction between C53 and autophagy receptor, ATG8. They reported that this IDR comprises four non canonical ATG8 interacting motifs (AIM), named shuffled AIMs (sAIMs) and showed that combinatorial mutagenesis of sAIM1, sAIM2, and sAIM3 abrogates ATG8 binding. A similar effect was observed for plant C53, though an additional canonical AIM (cAIM) in the C53 IDR had to be mutated to completely abolish C53 and ATG8 interaction. The earlier study reported that C53 IDR also interacts with UFM1, and this interaction can be disrupted in vitro by adding increasing concentration of ATG8, suggesting that ATG8 and UFM1 may compete with one another for C53 binding.

The present paper attempts to build on this previous work by using phylogenomics to infer a co-evolutionary relationship between UFMylation machinery and sAIMs in C53, which the authors argue, constitutes further evidence of the primary importance of a role for UFMylation in ER homeostasis. The manuscript includes a lot of biochemical data using variations of in vitro and in vivo pull-down experiments to define the roles of individual AIMs in mediating the binding of C53 to ATG8 and to UFM1. They also use NMR spectroscopy in an attempt to define the structural basis of the UFM1 and ATG8 binding to C53, concluding that plant C53 interacts with UFM1 mainly through sAIM1, while interaction with ATG8 requires cAIM as well as sAIM1 and sAIM2. Finally, the authors attempt to contextualize these findings by conducting studies on Arabidopsis mutants, showing that replacing sAIMs with cAIMs causes increases sensitivity to ER stress and apparently increases formation of C53 intracellular puncta that may colocalize with ATG8.

From these data the authors concluded that the dual-ATG8 and UFM1 binding of C53 IDR regulates C53 recruitment to autophagosomes in response to ER stress.

Major Issues:

1. The phylogenomics analysis conclusion that UFM1 is common in unicellular lineages and did not evolve in multicellular eukaryotes is not novel, as another comprehensive analysis of UFM1 phylogeny, published eight years ago - in 2014 - by Grau-Bové et al. (PMID: 25525215), also reported that UFM1, UBA5, UFC1, UFL1 and UFSP2 were likely present in LECA and lost in Fungi. Although the phylogenomic analysis by Picchianti et al. is also extended to DDRGK1 and C53 proteins, and some parasitic and algal lineages, their findings are incremental. Their proposed coevolution of sAIM and UFM1 is based on presence-absence correlation observed within five species (i.e., Albugo candida, Albuco laibachii, Piromyces finnis, Neocallimastix californiae, Anaeromyces robustus). However, this coevolutionary relationship must be further investigated by substantially increasing the taxonomic sampling within the UFM1-lacking group.
2. The manuscript presents an overwhelming amount of biochemical and structural data obtained from a variety of protein binding techniques (i.e., NMR spectroscopy, in vitro GST-pulldown, fluorescence microscopy-based on-bead binding assays, and native mass-spectrometry). The results are poorly explained and not organized in a logical manner. Moreover, no attempt was made to explain the rationale behind using one technique over the other or how one method complements another to build a stronger conclusion than any individual approach. Given that none of the methods employed report quantitative measurement of binding affinities between C53 IDR and UFM1 or ATG8, it is not clear how the data presented in this manuscript contribute to our understanding of the proposed competition model for UFM1 and ATG8 binding to C53 IDR. To conclude that an interaction is "stronger" or "weaker" it is necessary to measure equilibrium binding constants. Fortunately, there are suitable techniques, including surface plasmon resonance (SPR), microscale thermophoresis (MST), fluorescence anisotropy, or calorimetry that are available to dissect these complex competitive binding interactions and to build models.
3. The NMR studies have the potential to dissect the types of dynamic binding inherent in unstructured proteins. However, the abundant NMR data presented combined with the aforementioned binding studies, remarkably, do not seem to significantly advance our understanding of how the system is organized or even how UFM1 and ATG8 bind C53, beyond the rather vague and somewhat circular conclusion stated in the abstract: "...we confirmed the interaction of UFM1 with the C53 sAIMs and found that UFM1 and ATG8 bound the sAIMs in a different mode." Or on line 165 "Altogether these results suggested that ATG8 and UFM1 bbind the sAIMs withn C54 IDR, albeit in a different manner".
4. The functional assays performed in Arabidopsis do not support the competitive model between UFM1 and ATG8 for binding to C53 during C53-mediated autophagy. The fluorescence microscopy images do not provide convincing evidence of colocalization between C53 and ATG8. In fact, in contrast to the claims made in the text or the quantification, mCherry-C53 fluorescence does not seem to localize in discrete puncta and its signal does not seem to overlap with ATG8A.

Minor Issues:

1. The authors might choose to avoid teleological arguments such as (line 135): "As the phylogenomic analysis suggested that eh sAIMs have been retained to mediate C53-UFM1 interaction..."
2. The authors refer on multiple occasions to C53 "autoactivation" without defining what they mean by this. Do they propose that C53 UFMylates itself?.
3. The paper might want to avoid preachy philosophical statements like "Our evolutionary analysis also highlights why we should move beyond yeast and metazoans and instead consider the whole tree of life when using evolutionary arguments to guide biological research." (333-335). While this is indeed a laudable goal, given the rather limited insights from this study, it is unclear how this paper exemplifies the notion.

Referees cross-commenting

Referee #2

The challenge in providing a fair review of this manuscript is to clearly define what contributions are novel, significant advances. It is difficult to tell the way the manuscript is written, as it is unclear how the new data - which are voluminous- actually advance the model already put forth by the same authors in two previous publications. It is also unfortunate that the authors overlooked the 2004 phylogenomics paper. There clearly are some new pieces of information here, but the overall increment in knowledge is rather minimal.

Response from Referee #3

I agree that the authors somehow steamroll the reader with a wealth of data. But I think this can be addressed by the authors by requesting a lot more justification and by giving them the opportunity to put the significant advances into their own words. This is, in my opinion, quite doable in course of a revision. Overall I have to say that I am very sympathetic with the cross-eukaryote reactivity approach that the authors have taken. It is quite intriguing.

Response from Referee #2

I agree that the cross-eukaryote approach is intriguing. Shouldn't we be concerned that the 2004 publication already made two of their key points (ie present in LECA, loss in Fungi). What is the incremental insight from this paper?

I'd appreciate an opinion from an evolutionary biologist as to how strongly one can conclude functional co-evolution from such correlative data, especially given the rather small number of supporting examples. Is it also necessary to consider counter-examples- ie species that have sAIMs but no UFM1 (I believe that they found a few such cases)?

Response from Referee #3

Well with these deep evolutionary questions this is always a challenge. Where does one stop to sample more homologs for one's analyses (one from each supergroup [which are no longer recognised by the community])? In that sense, the authors are right to make the parsimonious base assumption that if X and Y interact in species A and B (no matter how distant they are related) then X and Y interacted in the last common ancestor of A and B. That being said, if I would have designed this study, I would have sampled more broadly for my in vitro cross-eukaryote approach. But also this, I think, could be carried out by the authors in a reasonable timeframe. Specifically, they have now sampled from Amorphea and Archaeplastida, they should add one from TSAR, one Haptista, one Cryptista, and one CRuM. If they synthesised the proteins via a company, they could have the constructs in a few weeks for about 1K Euro - I do not think that this would be an unreasonable request.

Significance

Overall, while the manuscript contains an abundance of new data, the overall conclusion of the work, stated in the title: "Shuffled ATG8 interacting motifs form an ancestral bridge between UFMylation and C53-mediated autophagy" does not constitute a significant advance beyond other published phylogenomic analysis (below) and the two previous papers by the same authors, including the 2020 paper "A cross-kingdom conserved ER-phagy receptor maintains endoplasmic reticulum homeostasis during stress (PMID: 32851973)" and the 2021 paper "C53 is a cross-kingdom conserved reticulophagy receptor that bridges the gap between selective autophagy and ribosome stalling at the endoplasmic reticulum PMID: 33164651)". While a regulatory interaction between UFMylation and autophagy is of potential importance, the data in this manuscript do not constitute a major advance and fail to provide new mechanistic insight to explain the role of C53 IDR in autophagy and its interplay with UFMylation

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this manuscript Picchianti et al. provide novel insights into the interaction of C53 with UFM1 and ATG8. Initially, the authors show that protein modification by UFM1 exists in the unicellular organism Chlamydomonas reinhardtii. To that end they demonstrated that pure Chlamydomonas UBA5, UFC1 and UFM1 proteins, can charge UFC1. Then, they showed that C53 interacts with ATG8 and UFM1. Specifically, they found that the sAIM are essential for the interaction with UFM1, while substituting this motif with canonical AIM prevents the binding of UFM1 but not of ATG8. Since binding of C53 to ATG8 recruits the autophagy machinery, the authors suggest that ufmylation of RPL26 releases UFM1 from C53 which allows the binding of ATG8. Overall, the authors demonstrate that C53 that forms a complex with UFL1 connects between protein ufmylation and autophagy by its ability to bind both UBLs.

Here the authors revisited the assumption that only multicellular organisms have the UFM1 system. Using bioinformatic tools they show that it exists also in unicellular organism. Also, they show that in some organisms the E3 complex UFL1, UFBP1 and C53 exist but not UBA5, UFC1 or UFM1. This is a very interesting observation that suggests an additional role for this complex. In Fig 1C the authors show that in Chlamydomonas RPL26 undergoes ufmylation. Please use IP against RPL26 and then a blot with anti UFM1. From the current experiment it is not clear how the authors know that this is indeed RPL26 that undergoes ufmylation

In the second part of the manuscript the authors characterize the interaction of C53 with ATG8 and UFM1. This is a continuation of their previous published work (Stephani et al, 2020) . Here the reviewer thinks that further data on the binding of these proteins to C53 is required. Specifically, defining the Kd of these interactions using ITC or other biophysical method can contribute to the study.

Under normal condition the authors suggest that C53 binds UFM1 and this keeps it inactive. The reviewer thinks that this claim needs further support. Using IP (maybe with crosslinker) the author can show that C53, in normal conditions, bind more UFM1 than ATG8. Also, since the interaction of UFM1 to C53 is noncovalent, it will be nice to show how alternations in UFM1 expression levels can affect the activation of C53. Finally, the authors suggest that ufmylation of RPL26 allows binding of ATG8 to C53 and this, in turn, leads to C53 activation. Can the authors show that in cells lacking UBA5, under normal condition or with Tunicamycin treatment, ATG8 does not activate C53 due to the fact that UFM1 does not leave C53.

Significance

This manuscript advances our understanding of the connection of ufmylation to autophagy which is mediated by C53.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reply to the reviewers

Referee #1

Evidence, reproducibility and clarity

1. This manuscript constructs a gene expression model with various factors. Specifically, the effect of cell size on gene expression is considered, which is often ignored by previous studies. One interesting finding is that the absolute number of the gene products and the concentration can have different distributions. Some predictions of the models are validated by experimental data on E. coli and yeast. This manuscript uses the mean-field approximation for cell volume, which has good accuracy when the number of stages is large. The usage of the power spectrum has a satisfactory effect on studying the concentration oscillation.

Response: Thank you for the positive comments.

1. Overall the paper was very difficult to follow and digest easily because of all the different factors and mechanisms invoked. It is mainly an issue of providing sufficient details for each of the factors and organizing them in a systematic and logical way. Although there is a supplementary appendix, it was hard to keep track of all the elements in the main manuscript. Perhaps something like Fig 1 of the Appendix can be presented in the main body to outline all the ingredients and how they affect each other.

Response: In the revised manuscript, we moved Supplementary Fig. S1 in the previous version into the main text to outline all the ingredients and how they affect each other (see page 8, Fig. 2). Moreover, we provided many details for each of the biological factors and tried to organize them in a more systematic and logical way (see pages 3-7).

1. It might be good to provide a more detailed description of the goal (studying gene product number and concentration under different parameters) after introducing the full and the reduced models. A table of symbols would also be helpful.

Response: In the revised manuscript, we added a table explaning the meaning of all model parameters (see page 4, Table 1). Moreover, we provided a detailed description of the goal of the present paper after introducing the full and reduced models (see page 7).

1. Some technical details in the Methods section are in fact helpful in understanding the conclusions. They can be moved to the Results section.

Response: In the revised manuscript, we moved many technical details in Methods and Supplementary Notes to the main text to help the readers better understand the conclusions (see pages 5-10).

1. One concern is that the central concept of this manuscript, “stage”, is not thoroughly discussed. This concept should have some significant biological meaning, not just be coined for mathematical convenience.

Response: In the revised manuscript, we explained in detail the biological meaning of the effective cell cycle stages (see page 4). Specifically, recent studies have revealed that in many cell types, the accumulation of some activator to a critical threshold is used to promote mitotic entry and trigger cell division, a strategy known as activator accumulation mechanism. In E. coli, the activator was shown to be FtsZ; in fission yeast, it is believed to be a protein upstream of Cdk1, the central mitotic regulator, such as Cdr2, Cdc25, and Cdc13. Biophysically, the N effective stages can be understood as different levels of the key activator. Moreover, we pointed out that the power law form for the rate of cell cycle progression may come from cooperativity of the key activator that triggers cell division.

1. Fig. 1(b) is a little strange. For the left panel, the x-axis (stage) is discrete, then the volume (y-axis) should be a step function, not a straight red line.

Response: In the revised manuscript, we added some red dots in the stage-volume plot to show the dependence of the mean cell volume vk on cell cycle stage k for the mean-field model (see page 3, Fig. 1). Moreover, we emphasized that the joining of these dots by a straight red line is simply a guide to the eye.

Significance

1. The main advance is a more complete model of gene expression under more realistic organism growth conditions.

Response: Thank you for acknowledging the results of the manuscript.

Referee #2

Evidence, reproducibility and clarity

1. Jia et al. introduce a modeling framework to represent stochastic gene expression, with an explicit representation of cell volume growth, cell cycle progression (and its dependency on cell volume) and gene dosage compensation. The model is very elegant and general in that it can represent a variety of situations, simply as a matter of parametrization. Under a simplifying assumption, the authors derive a number of metrics (include stationary distribution of gene product and power spectrum of gene product fluctuation dynamics), for both absolute number and concentration of gene product molecules. They use their model and derivations to examine under which conditions cell can achieve homeostasis in the concentration of the expressed gene product, despite changes in cell volume and gene copy number following replication. They also present and discuss the conditions giving rise to specific features (i.e. bimodality in stationary distribution, peak in power spectrum) and examine these features in experimental data to conclude to infer the underlying homeostasis strategies. The model is rather general and powerful. The simplifying assumption seems reasonable (and the authors investigate to some extent its limitations, i.e. Fig. 2). The conclusions are overall convincing.

Response: Thank you for the positive comments.

Major comments 1. My main concern is that the metrics that the authors use to assess concentration homeostasis (i.e. the γ parameter and the presence / absence of peak in power spectrum) do not seem quite appropriate to describe how much variability / fluctuations in concentration are driven by cell cycle effects. Indeed, the γ parameter measures how much the *average* concentration in each cell cycle stage varies throughout the cell cycle. However, this variability should be compared to the total variability due to both cell cycle effects and stochastic bursting dynamics. A given level of cell-cycle dependency (say γ = 0.2) could be very visible if gene expression is weakly noisy (e.g. B low and hni high) and completely invisible is gene expression is highly bursty (large B and small hni). In the latter situation, cell-cycle effects would be meaningless for the cell to minimize. In essence, reusing the authors notations, I think γ/φ1/2 , would be a more relevant metric to observe.

Response: In the revised manuscript, we showed that the total concentration noise φ can be decomposed as φ = φext + φint, where φext is the extrinsic noise which characterizes the fluctuations between different stages due to cell cycle effects and φint is the intrinsic noise which characterizes the fluctuations within each stage due to stochastic bursty synthesis and degradation of the gene product (see page 11). Based on the above decomposition, we introduced a new metric γ = φext/φ, which characterizes the accuracy of concentration homeostasis. Clearly, the new metric γ reflects the relation contribution of cell cycle effects in the total concentration variability. All discussions about concentration homeostasis are based on the new metric γ in the revised manuscript. Moreover, all figures have been updated by using this new metric.

1. Similarly, when inspecting the peak in the power spectrum, the weight of the Lorentzian function(s) creating the peak, should be compared to the stationary component (λN , uN in the authors’ notations).

Response: We cannot quite understand why the weights uk of the Lorentzian functions should be compared to the stationary component uN . In fact, all the weights uk except uN are actually complex numbers and we are not so sure about the meaning of uk/uN . However in the revised manuscript, we emphasized that the power spectrum G(ξ) is normalized so that G(0) = 1 throughout the paper (see page 13). To better understand concentration oscillations and its relation to homeostasis, we depicted both γ and H as a function of B and hni (see Supplementary Fig. S5). As expected, the off-zero peak becomes lower as B increases and as hni decreases since both of them correspond to an increase in concentration fluctuations which counteracts the regularity of oscillations; noise above a certain threshold can even completely destroy oscillations. Furthermore, we found that γ and H have similar dependence on B and hni. This again shows that the occurrence of concentration oscillations is intimately related to the visibility of cell cycle effects in concentration fluctuations.

A complementary analysis including these two points and a discussion the relative contribution of cell-cycle effects and bursting dynamics in the total variability/fluctuation of concentrations would be important to include.

Response: In the revised manuscript, we made some complementary analysis and discussion about the relative contribution of cell cycle effects and stochastic birth-death dynamics in the total variability of concentrations (see pages 11-14).

Minor comments 3. The dashed line on Fig. 3a is defined as κ = √ 2 1−β . First is this empirical or does it come from a derivation? Second, it seems incomplete since it should depend on w. Intuitively, this line should correspond to the value of κ that would best mimic balanced biosynthesis in the case where β 6= 1. In other words, κ should be so that hρB0 /V (t)iprereplication = hκρB0 /V (t)ipostreplication, which yields κ = 2w(1−β) ∗ (w − 1)/w ∗ [2w(β−1) − 1]/[2(1−w)(β−1) − 1]. This indeed simplifies into κ = √ 2 1−β when w = 0.5.

Response: Thank you for providing such a beautiful derivation. In the revised manuscript, we added this derivation into the main text (see pages 12-13). Moreover, we also made it clear that this relation can also be obtained from the perspective of power spectrum (see page 14).

1. η is used in the caption of Fig. 2, which is cited on page 4. But it is defined only 2 sections later, on page 6.

Response: In the revised manuscript, we gave the definition of η in both Table 1 and the caption of Fig. 3 (Fig. 2 in the old version). Please see page 4, Table 1 and page 9, Fig. 3.

1. w is used in the main text, but only defined in the caption of Fig. 3.

Response: In the revised manuscript, we gave the definition of w in both Table 1 (see page 4) and on page 7.

1. w is defined as “the proportion of cell cycle before replication”. Is this in terms of cell cycle stages (i.e. w = N0/N) or actual time?

Response: In the revised manuscript, we made it clear that w represents the proportion of cell cycle duration before replication, which should be distinguished from the proportion N0/N of cell cycle stages before replication (see page 7). This is because the transition rate between cell cycle stages is an increasing function of cell size, which means that earlier (later) stages have longer (shorter) durations.

1. Fig. 3 indicates that power spectra are normalized so that G(0) = 1, but G(0) = 10 on the first two graphs.

Response: Corrected as suggested (see page 12, Fig. 4). Thank you.

1. Page 11: “bimodality in the concentration distribution is significantly less apparent”. I would suggest rephrasing “bimodality in the concentration distribution is absent” since there should be no reference to “significance” and bimodality is either present or absent (binary), not less apparent.

Response: Corrected as suggested. Thank you.

Referees cross-commenting

1. Regarding the comment from reviewer 3 that ”a direct validity test should use data sets of at least two types (total, nascent RNA, etc)”. I almost made a related comment in my review, but then I held it off: This issue with using nascent RNA data is that their model does not allow an ON state. They assume that gene products are produced in instantaneous bursts, which is a fair assumption if the lifetime of gene products is large compared to the time the gene stays ON. This is ok if the considered ”gene products” are mRNA or proteins, but not nascent RNAs (for which the lifetime is the time to transcribe the gene). I did not make this comment in the end because I think the model is useful regardless. To comply with reviewer 3’s request, maybe the authors could use distributions of mRNA and protein products, but I’m not sure that such data exists (since they need cell-cycle-resolved data).

Response: It is not possible to validate our model with nascent mRNA data because the model in its present form cannot predict nascent mRNA fluctuations. This is because unlike mature mRNA, nascent mRNA cannot be assumed to decay via first-order kinetics. A detailed response is provided below to the original comment made by Referee 3. Regarding the comment on the use of cell-cycle-resolved data measuring mRNA and protein expression – while we agree it would make an excellent test of our model, we could not find such a dataset in the literature. We point out that our model, in its present form, is interesting as it is, as a detailed biological model of mature mRNA and protein number / concentration fluctuations in growing cells. Its predictions are yet to be fully confirmed and hence may stimulate the development of further experimental single-cell studies.

Significance

1. The advance of this paper is essentially technical. The authors present a model that incorporates and unifies previously studied effects (cell volume homeostasis, concentration homeostasis, bursting transcription). There is no major conceptual novelty, but the combination of these different aspects and the derivations that authors present are very valuable and might be applicable to interpret data in various species.

Response: Thank you for acknowledging the results of the manuscript.

Referee #3

Evidence, reproducibility and clarity

1. The manuscript analyses a phenomenological model of stochastic gene expression. The model couples bursty transcription with cell growth, division and DNA replication. The cell cycle is divided into a large number of stages whose exponential lifetimes depend on the cell volume. It is argued that concentrations of gene products are distributed according to mixed Gamma distributions, whereas the copy numbers follow mixed negative binomial distributions. The number of modes can be different for concentrations and copy numbers, for instance the copy numbers can be unimodal while concentrations are bimodal. The case when the mean concentration does not depend on the cell cycle stage is called perfect homeostasis. It is argued that perfect homeostasis leads to Gamma distribution of the gene product concentration and that deviations from a Gamma distributions result mainly from deviations of the concentration from perfect homeostasis. It is also proposed that concentration homeostasis is difficult to obtain. These qualitative predictions of the model are tested using two data sets, one for E.coli and another for fission yeast.

Response: Thank you for acknowledging the results of the manuscript.

Major comments 1. A huge number of states called “cell cycle stages” have exponential life times. On my opinion, this sequence of stages is just a technicality for keeping the model within a discrete Markovian framework. More natural choices are possible, such as piecewise deterministic Markov processes, age structured diffusions, etc. The biological significance (if there is any) of such states should be explained.

Response: In the revised manuscript, we explained in detail the biological meaning of the effective cell cycle stages (see page 4). Specifically, recent studies have revealed that in many cell types, the accumulation of some activator to a critical threshold is used to promote mitotic entry and trigger cell division, a strategy known as activator accumulation mechanism. In E. coli, the activator was shown to be FtsZ; in fission yeast, it is believed to be a protein upstream of Cdk1, the central mitotic regulator, such as Cdr2, Cdc25, and Cdc13. Biophysically, the N effective stages can be understood as different levels of the key activator. Moreover, we pointed out that the power law form for the rate of cell cycle progression may come from cooperativity of the key activator that triggers cell division.

1. The timescales of stochastic gene expression are not correctly taken into account. It is considered that during an exponential stage the bursting approximation describes gene expression in terms of Gamma distributions for concentrations and in terms of negative binomial distributions for copy numbers. This approximation is only valid if the lifetime of a stage is much larger than the time needed to generate a burst. For RNA, this condition cannot be fulfilled for a large number of states N and/or for two states promoters with a relatively long ON state. For the protein and/or in the case of translational bursting, the condition is even more difficult to fulfil. I agree with the Reviewer 2 that once the master equation accepted the results make sense. But my criticism is different and concerns the master equation itself. In this equation the burst is considered instantaneous, whereas it needs finite time in reality. Concerning nascent mRNA, ON/OFF etc. I disagree. The notion of instantaneous burst with well defined burst size and burst frequency on a stage has a meaning if the lifetime of this stage (which is not mRNA or protein lifetime) is short. The model validity should be clearly stated.

Response: Thank you for pointing out this important issue. When we talk about the validity of the model, we should stick to the full model, instead of the mean-field model. This is because once the full model makes sense, the mean-field model must work well when N ? 15, as we have shown in Fig. 3 and Supplementary Fig. S3. Hence our reply is based on the validity of the full model. We will reply to the above comments from the following three aspects. First, we agree with the referee that in our model, we assume that the gene product is produced in instantaneous bursts with the reaction scheme G ρpk (1−p) −−−−−−→ G + kM, k ≥ 1, M d −→ ∅, (1) where the mean burst size scales as V (t) β . Of course, in reality there is a finite time for the bursts to occur. A more general assumption is that within each cell cycle, the gene expression dynamics is characterized by the following three-stage model: G ρ −→ G ∗ , G∗ r −→ G, G∗ sV (t) β −−−−→ G ∗ + M, M u−→ M + P, M v −→ ∅, P d −→ ∅, (2) where the first two reactions describe the switching of the gene between an inactive state G and an active state G∗ the middle two reactions describe transcription and translation, and the last two reactions describe the degradation of the mRNA M and the protein P. Here the synthesis rate of mRNA depends on cell volume via a power law form with power β ∈ [0, 1]. Dosage compensation can be modeled by a decrease in the gene activation rate (for each gene copy) from ρ to κρ/2 upon replication. Previous studies have revealed that the bursting of mRNA and protein has different biophysical origins: transcriptional bursting is due to a gene that is mostly inactive, but transcribes a large number of mRNA when it is active (r ? ρ and s/r is finite), whereas translational bursting is due to rapid synthesis of protein from a single short-lived mRNA molecule (v ? d and u/v is finite). Under the above timescale separation assumptions, both mRNA and protein are produced in a bursty manner with the reaction scheme described by Eq. (1). The burst frequency for mRNA and protein are both ρ before replication and κρ after replication. The mean burst size for mRNA is (s/r)V (t) β and the mean burst size for protein is (su/rv)V (t) β , both of which have a power law dependence on cell volume (see pages 5-6). In Supplementary Figs. S1 and S2, we compare the mRNA and protein distributions for the bursty model with the reaction scheme given by Eq. (1) and the three-stage model with the reaction scheme given by Eq. (2), where both models under consideration have a cell cycle and cell volume description. It can be seen that the distributions for the two models are very close to each other under the above timescale separation assumptions with the bursty model being more accurate as r/ρ and v/d increase. Moreover, we find that the accuracy of the bursty model is insensitive to the value of the number of stages N. Here the values of N are chosen so that the ratio of the average time spent in each stage (T /N, where T ≈ (log 2)/g is the mean cell cycle duration) and the mean burst duration time (1/ρ) ranges from ∼ 0.5 − 2. This shows that the effectiveness of the bursty model does not require that the lifetime of a cell cycle stage is sufficient long. Due to mathematical complexity, we only focus on the bursty model in the present paper. The consistency between the gene product distributions for the two models justifies our bursty assumption. Second, while we assume bursty expression here, our model naturally covers non-bursty expression since the latter can be regarded as a limit of the former. Hence all the conclusions in the present paper are applicable to both bursty and non-bursty expression. In the revised manuscript, we emphasized this point (see page 4 for a detailed explanation). Last but not least, if the lifetime of the gene product is much shorter compared to the lifetime of each cell cycle stage, then the gene expression dynamics will rapidly relax to a quasi-steady state for each stage. In this case, the gene product fluctuations at each stage can be characterized by a gamma distribution in terms of concentrations and by a negative binomial distribution in terms of copy numbers, and hence the distribution of concentrations (copy numbers) for a population of cells is naturally a mixture of N gamma (negative binomial) distributions. However, the powerfulness of our analytical distribution (see page 10, Eq. (8)) is that it serves an accurate approximation when N ? 1 without making any timescale assumptions. The effectiveness of our analytical distributions is validated in Supplementary Fig. S3 for three different cases: (i) the degradation rate d of the gene product is much smaller than the cell cycle frequency f; (ii) d and f are comparable; (iii) d is much larger than f. In the revised manuscript, we also emphasized these points (see page 10).

1. DNA replication is a stochastic event and does not occur after a fixed number of exponential stages as it is considered in this model. Concerning replication: in the model this occurs after exactly N0 steps. In reality, replication occurs somewhere between the start of S and G2/M. N0 is in fact a random variable. Probably a new mean field assumption is needed here with some justification, but I have seen nothing in the paper.

Response: We agree with the referee that replication of the whole genome occurs in the S phase, which occupies a considerable portion of the cell cycle and thus cannot be assumed to occur after a fixed number of exponential stages. However, our model is for a single gene and since the replication time of a particular gene is much shorter than the total duration of the S phase, it is reasonable to consider it to be instantaneous. In addition, recent experiments have shown that the time elapsed from birth to replication for a particular gene occupies an approximately proportion of the cell cycle, which is called the stretched cell cycle model. This is also consistent with our assumption that replication of the gene of interest occurs after exactly N0 stages. While replication occurs after a fixed number of stages, nevertheless the time of replication is stochastic since each stage has a random lifetime. In the revised manuscript, we emphasized these points (see pages 4-5).

1. The results in the Methods were derived heuristically and their relation to the master equation (12) is not explicit (except for the part concerning moments and their power spectrum). Furthermore, one would like to have some estimates of the biases introduced by the mean field approximation. Concerning biases introduced by the mean field approximation: Figure 2 is a numerical simulation, some analytical estimates could be better. As Figure 2 looks rather convincing, I reclassify this as minor comment.

Response: We agree with the referee that the derivation of moments is rigorous, but the derivation of the analytical distribution given in Methods is not rigorous and cannot be directly obtained from the master equation. In the revised manuscript, we emphasized that the analytical distribution is not exact but it serves as a very good approximation (see pages 10 and 22). We showed that the analytical distribution agrees well with stochastic simulations when the number of cell cycle stages N ≥ 15 (see page 9, Fig. 3 and Supplementary Fig. S3). The logic behind our approximate distribution is that while the gene product may produce complex distribution of concentrations (copy numbers), when the number of cell cycle stages is large, the distribution must be relatively simple within each stage and thus can be well approximated by a simple gamma (negative binomial) distribution (see page 22). Due to the complexity of our model, it is very difficult to provide any analytical estimates on the bias introduced by the mean-field approximation. Often the bias of an approximation can be estimated when the approximation emerges from a systematic method such as van Kampen’s system-size expansion (see Ref. [21]). However, our mean-field model cannot be seen as the zero order term of some expansion and hence it is not possible to calculate the next-order correction which would be needed to estimate the error. However, we have tested very large swathes of parameter space and found that the mean-field approximation always works well when N ≥ 15 which is the physiologically relevant regime for most types of cells (see discussion on P. 7).

1. The model is not minimal and depends on a huge number of parameters. It is not clear how these parameters were found and if overfitting was avoided. One may have doubts about the identifiability of the parameter N. What difference is between N = 59 and N = 60 (the value of N for the cyanobacterium)?

Response: In the revised manuscript, we used synthetic data to show that all the model parameters involved in our model (except d and β which can be determined based on a priori knowledge) can be accurately estimated from cell-cycle resolved lineage data of cell volume and gene expression (see Supplementary Note 7). We provided details of the parameter inference method, compared the input parameters with the estimated ones and verify that they are identifiable (see Supplementary Table 1). We did not use real data to test our inference method because we could not find cell-cycle resolved lineage data for mRNA or proteins. As we noted, this is in principle possible via cell-cycle fluorescent markers. We also note that parameter inference for less detailed but similar models have been made in our previous papers — the parameters related to cell volume dynamics have been inferred in E. coli (see Ref. [51]) and fission yeast (see Ref. [52]) using the method of distribution matching, and the parameters related to gene expression dynamics have be estimated in E. coli (see Ref. [40]) using the method of power spectrum matching. Moreover, for our purpose, i.e. to investigate the effect of cell cycle and cell volume on gene expression, we do believe that our model is minimal. We captured cell growth with only one parameter g, the degree of balanced biosynthesis with one parameter β (β = 0 corresponds to the case where the synthesis rate is independent of cell volume and β = 1 corresponds to the case where the synthesis rate scales linearly with cell volume), the variability in cell cycle duration with only one parameter N, gene replication with only one parameter N0, gene dosage compensation with only one parameter κ (κ = 1 corresponds to perfect dosage compensation and κ = 2 corresponds to no dosage compensation), and the variation of size control strategy across the cell cycle with two parameters α0 and α1 (αi → 0 corresponds to timer, αi = 1 corresponds to adder, and αi → ∞ corresponds to sizer). The biological meaning of the cell cycle stages were clarified in the revised manuscript (see page 4). For our purpose, we believe that our model cannot be simpler.

1. The authors should make clear which cell biology aspects are important, which are less important, and which were neglected in the context of their problem. Thus, in their model, cell cycle acts on gene expression mainly by duplication of burst sources and thus by increase of burst frequency after replication. Another important source of gene expression variability during the cycle, the mitotic transcription repression, is neglected.

Response: In the revised manuscript, we clarified which cell biology aspects are important for gene expression dynamics (see page 17). Specifically, in our model, cell cycle and cell volume act on gene expression mainly by (i) the dependence of the burst size on cell volume; (ii) the increase in the burst frequency upon replication; (iii) the change in size control strategy upon replication; (iv) the partitioning of molecules at division. Point (iv) strongly affects copy number fluctuations, while it has little influence on concentration fluctuations. In addition, in the revised manuscript, we also elucidated the limitations of our model including mitotic transcription repression and others (see pages 19-20).

1. The validity test of the model is indirect. It was tested that the concentration distribution deviates from Gamma and that the deviation correlates positively to the lack of accuracy of the concentration homeostasis. However, many models can have this behaviour. A direct validity test should use data sets of at least two types (total, nascent RNA, etc.) allowing direct estimates of some model parameters (such as burst size and frequency using nascent RNA). Concerning parsimony, I think that the authors should test it. Are all the parameters identifiable? Is there any overfitting? They could use parameter uncertainty, comparison of training /testing errors, etc. Some details about the parameter fitting method should be provided.

Response: Regarding the parameter fitting and identifiability we have provided a detailed response to a previous comment above. However we emphasize that for the generation of Fig. 7, we did not need to estimate all model parameters from data. Hence in the previous version of the manuscript, no such estimation was done — we simply extracted the homeostasis accuracy γ, the height H of the off-zero peak of the power spectrum, and the Hellinger distance D of the concentration distribution from its gamma approximation directly from data. Finally, we point out that our model can be used to predict the dynamics of mature mRNAs, but it cannot be used to describe the dynamics of nascent mRNAs. This is because nascent mRNAs do not decay via a first-order reaction but their removal, i.e. their detachment from the gene which leads to mature mRNA, is better approximated by a reaction with a fixed decay time. This models the elongation time of nascent transcripts which does not suffer from much noise because the RNAP velocity is to a good approximation constant along the gene. See e.g. the following two papers for details: H. Xu, S. O. Skinner, A. M. Sokac, I. Golding, Stochastic kinetics of nascent RNA. Phys. Rev. Lett. 117, 128101 (2016). S. Braichenko, J. Holehouse, R. Grima. Distinguishing between models of mammalian gene expression: telegraph-like models versus mechanistic models. J. R. Soc. Interface 18, 20210510 (2021). Because of the fixed delay, the delay telegraph model (the telegraph model with a delayed degradation reaction) is non-Markovian and very different from the usual Markovian telegraph model which describes the dynamics of mature mRNA within each cell cycle. See e.g. the Supplementary Information of the following paper: X. Fu, et al. Accurate inference of stochastic gene expression from nascent transcript heterogeneity. bioRxiv (2021). Given the mathematical complexity introduced by a fixed delay, using it to describe the dynamics of nascent mRNA within each cell cycle leads to a non-Markovian model that is even more analytically intractable than the present one for mature mRNA. While an interesting research question, this is clearly far removed from the scope of our current manuscript.

Minor comments 8. The introduction could be more pedagogical. Right now it is just an accumulation of loosely related and sometimes abruptly introduced statements. For instance, we understand that the authors want to oppose their approach to other extant approaches. However, extant approaches should be better reviewed, some of them are aged structured and perfectly suited for analysing cell cycle data. It would be useful for the reader that an example of observation explained by their model and not explained by other models (age structured or not) is discussed in detail. The model of this work does not explain size control, it just assumes that this holds, and does not discuss cell population aspects. A more nuanced positioning of this approach with respect to the literature would be useful for judging its value.

Response: In the revised manuscript, we rewrote the introduction part to make it more pedagogical (see pages 1-2). In particular, we compared three popular models describing the cell size dynamics and the associated size homeostasis. The advantages and disadvantages of the three models were discussed.

1. The meaning of N should be discussed from the very start when the model is introduced.

Response: In the revised manuscript, we explained in detail the biological meaning of the effective cell cycle stages (see page 4). Specifically, recent studies have revealed that in many cell types, the accumulation of some activator to a critical threshold is used to promote mitotic entry and trigger cell division, a strategy known as activator accumulation mechanism. In E. coli, the activator was shown to be FtsZ; in fission yeast, it was believed to be a protein upstream of Cdk1, the central mitotic regulator, such as Cdr2, Cdc25, and Cdc13. Biophysically, the N effective stages can be understood as different levels of the key activator. Moreover, we pointed out that the power law form for the rate of cell cycle progression may come from cooperativity of the key activator that triggers cell division.

1. The authors call constitutive expression the situation when the mean copy number does not depend on the volume. This choice should be clarified as in general constitutive as opposed to specific, localised or transitory expression refers to non-regulated gene expression. It seems to me that in this context, expression is only partially constitutive (independent on the volume).

Response: In the present paper, constitutive expression means that the gene product is produced one at a time and is not produced in a bursty manner. It does not mean that the mean copy number does not depend on the volume. In the revised manuscript, we provided a more detailed discussion about how constitutive expression can be viewed as a limit of bursty expression (see page 4).

1. In figure 1b and for exponential growth the y axis should be log(volume) instead of volume. The mean field approximation is called both “of novel type” (Discussion) and “which has a long history of successful use in statistical physics” (p4). If something is novel, then one should clearly explain why.

Response: In fact, the y-axis in Fig. 1(b) should be volume instead of log(volume). This is because the x-axis represents the cell cycle stage instead of the real time. Note that for the adder strategy (α0 = α1 = 1), it follows from Eq. (3) on page 7 that the mean cell volume at stage k is vk = v1 + (k − 1)M0/N0, which linearly depends on k. This explains why the red curves in Fig. 1(b) are straight lines instead of exponential curves. In the revised manuscript, we also explained why the mean-field approximation used is novel (see page 7). Specifically, we pointed out that the mean-field approximation is not made for the whole cell cycle, rather we make the approximation for each stage and thus different stages have different mean cell volumes. This type of piecewise mean-field approximation, as far as we know, is novel and has not been used in the study of concentrating fluctuations before.

1. The word “cyclo-stationarity” is used with not much definition. If this means just stationary distribution of the gene products why not use just “stationarity” instead. What means “cyclo”? A number of properties were called “rare” but it is not clear on what grounds.

Response: In the revised manuscript, we removed the term “cyclo-stationarity” and simply assumed that the copy number and concentration distributions of the gene product at each cell cycle stage have reached the steady state (see page 8). In addition, for each property that was called “rare”, we explained the reasons in detail (see pages 14 and 17).

1. I did not find a proof that the copy number distribution has less modes than the concentration distribution.

Response: In fact, it is very difficult to prove that the concentration distribution has less modes than the copy number distribution. However, we have tested very large swathes of parameter space and found that the number of modes of the concentration distribution is always less than or equal to that of the copy number distribution. In the revised manuscript, we emphasized this point (see page 16).

Significance

1. The strength of this work is that it incorporates in a stochastic gene expression model a number of ideas on size control and dosage compensation that were discussed elsewhere from a cell population point of view. However, the proposed model is based on a number artificial choices that are difficult to justify biologically: a huge number of cell cycle discrete states and inappropriate handling of the timescales characterizing stochastic gene expression. Furthermore, the model is not minimal but depends instead on a huge number of parameters. I found the paper difficult to read and in the results presentation is not suitable for biologists that would need more details on the justification of the modelling choices and on the experimental validation of the model.

Response: All these points have been addressed in previous replies.

1. For mathematicians, the calculations are rather standard and may seem trivial.

Response: Our model is complex due to the coupling between gene expression dynamics, cell volume dynamics, and cell cycle events. It is far more complex than standard models of gene expression (see e.g. Refs. [2,84,85]) because of the large amount of biology encapsulated in it and we presented a first analytical- and simulation-based analysis of concentration fluctuations when concentration homeostasis is broken.

The computations of many quantities in the present paper are non-trivial. First, we showed that the generalized added volumes before and after replication both have an Erlang distribution. Using this property, we computed the mean cell volume in each cell cycle stage which is needed in the mean-field approximation. Furthermore, the computations of the power spectrum of concentration fluctuations are also highly non-trivial. The analytical expression of the power spectrum allows us to precisely determine the onset of concentration homeostasis. While the computations of moments of concentration fluctuations are standard, we used to the moments to construct an analytical concentration distribution which serves as an accurate approximation when N is large. Our concentration distribution is generally valid when concentration homeostasis is broken and goes far beyond recent models for growing cells which require concentration homeostasis and which do not take into account DNA replication, dosage compensation and size control mechanisms that vary with the cell cycle phase (e.g. Ref. [26] ).

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

The manuscript analyses a phenomenological model of stochastic gene expression. The model couples bursty transcription with cell growth, division and DNA replication. The cell cycle is divided into a large number of stages whose exponential lifetimes depend on the cell volume. It is argued that concentrations of gene products are distributed according to mixed Gamma distributions, whereas the copy numbers follow mixed negative binomial distributions. The number of modes can be different for concentrations and copy numbers, for instance the copy numbers can be unimodal while concentrations are bimodal. The case when the mean concentration does not depend on the cell cycle stage is called perfect homeostasis. It is argued that perfect homeostasis leads to Gamma distribution of the gene product concentration and that deviations from a Gamma distributions result mainly from deviations of the concentration from perfect homeostasis. It is also proposed that concentration homeostasis is difficult to obtain. These qualitative predictions of the model are tested using two datasets, one for E.coli and another for fission yeast.

Major comments:

The model encompasses a number of artificial choices:

• A huge number of states called "cell cycle stages" have exponential life times. On my opinion, this sequence of stages is just a technicality for keeping the model within a discrete Markovian framework. More natural choices are possible, such as piecewise deterministic Markov processes, age structured diffusions, etc. The biological significance (if there is any) of such states should be explained.
• The timescales of stochastic gene expression are not correctly taken into account. It is considered that during an exponential stage the bursting approximation describes gene expression in terms of Gamma distributions for concentrations and in terms of negative binomial distributions for copy numbers. This approximation is only valid if the lifetime of a stage is much larger than the time needed to generate a burst. For RNA, this condition cannot be fulfilled for a large number of states N and/or for two states promoters with a relatively long ON state. For the protein and/or in the case of translational bursting, the condition is even more difficult to fulfil.
• DNA replication is a stochastic event and does not occur after a fixed number of exponential stages as it is considered in this model. The results in the Methods were derived heuristically and their relation to the master equation (12) is not explicit (except for the part concerning moments and their power spectrum). Furthermore, one would like to have some estimates of the biases introduced by the mean field approximation. The model is not minimal and depends on a huge number of parameters. It is not clear how these parameters were found and if overfitting was avoided. One may have doubts about the identifiability of the parameter N. What difference is between N=59 and N=60 (the value of N for the cyanobacterium)? The authors should make clear which cell biology aspects are important, which are less important, and which were neglected in the context of their problem. Thus, in their model, cell cycle acts on gene expression mainly by duplication of burst sources and thus by increase of burst frequency after replication. Another important source of gene expression variability during the cycle, the mitotic transcription repression, is neglected.<br /> The validity test of the model is indirect. It was tested that the concentration distribution deviates from Gamma and that the deviation correlates positively to the lack of accuracy of the concentration homeostasis. However, many models can have this behaviour. A direct validity test should use datasets of at least two types (total, nascent RNA, etc.) allowing direct estimates of some model parameters (such as burst size and frequency using nascent RNA).

Minor comments:

The introduction could be more pedagogical. Right now it is just an accumulation of loosely related and sometimes abruptly introduced statements. For instance, we understand that the authors want to oppose their approach to other extant approaches. However, extant approaches should be better reviewed, some of them are aged structured and perfectly suited for analysing cell cycle data. It would be useful for the reader that an example of observation explained by their model and not explained by other models (age structured or not) is discussed in detail. The model of this work does not explain size control, it just assumes that this holds, and does not discuss cell population aspects. A more nuanced positioning of this approach with respect to the literature would be useful for judging its value.

The meaning of N should be discussed from the very start when the model is introduced.

The authors call constitutive expression the situation when the mean copy number does not depend on the volume. This choice should be clarified as in general constitutive as opposed to specific, localised or transitory expression refers to non-regulated gene expression. It seems to me that in this context, expression is only partially constitutive (independent on the volume).

In figure 1b and for exponential growth the y axis should be log(volume) instead of volume.

The mean field approximation is called both "of novel type" (Discussion) and "which has a long history of successful use in statistical physics" (p4). If something is novel, then one should clearly explain why.<br /> The word "cyclo-stationarity" is used with not much definition. If this means just stationary distribution of the gene products why not use just "stationarity" instead. What means "cyclo"?

A number of properties were called "rare" but it is not clear on what grounds.

I did not find a proof that the copy number distribution has less modes than the concentration distribution.

Referees cross-commenting

Part 1

I agree with the Reviewer 2 that once the master equation accepted the results make sense. But my criticism is different and concerns the master equation itself. In this equation the burst is considered instantaneous, whereas it needs finite time in reality.

Part 2 (response to Part 2 of Rev2)

• concerning replication: in the model this occurs after exactly N_o steps. In reality, replication occurs somewhere between the start of S and G2/M. N_o is in fact a random variable. Probably a new mean field assumption is needed here with some justification, but I have seen nothing in the paper
• concerning biases introduced by the mean field approximation: Figure 2 is a numerical simulation, some analytical estimates could be better. As Figure 2 looks rather convincing, I reclassify this as minor comment.
• concerning nascent mRNA, ON/OFF etc. I disagree. The notion of instantaneous burst with well defined burst size and burst frequency on a stage has a meaning if the lifetime of this stage (which is not mRNA or protein lifetime) is short. The model validity should be clearly stated.
• concerning parsimony, I think that the authors should test it. Are all the parameters identifiable? Is there any overfitting? They could use parameter uncertainty, comparison of training /testing errors, etc. Some details about the parameter fitting method should be provided.

Significance

The strength of this work is that it incorporates in a stochastic gene expression model a number of ideas on size control and dosage compensation that were discussed elsewhere from a cell population point of view. However, the proposed model is based on a number artificial choices that are difficult to justify biologically: a huge number of cell cycle discrete states and inappropriate handling of the timescales characterizing stochastic gene expression. Furthermore, the model is not minimal but depends instead on a huge number of parameters.

I found the paper difficult to read and in the results presentation is not suitable for biologists that would need more details on the justification of the modelling choices and on the experimental validation of the model. For mathematicians, the calculations are rather standard and may seem trivial. I am a systems biologist with a background in mathematics and theoretical physics.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

Jia et al. introduce a modeling framework to represent stochastic gene expression, with an explicit representation of cell volume growth, cell cycle progression (and its dependency on cell volume) and gene dosage compensation. The model is very elegant and general in that it can represent a variety of situations, simply as a matter of paramterization. Under a simplifying assumption, the authors derive a number of metrics (include stationary distribution of gene product and power spectrum of gene product fluctuation dynamics), for both absolute number and concentration of gene product molecules. They use their model and derivations to examine under which conditions cell can achieve homeostasis in the concentration of the expressed gene product, despite changes in cell volume and gene copy number following replication. They also present and discuss the conditions giving rise to specific features (i.e. bimodality in stationary distribution, peak in power spectrum) and examine these features in experimental data to conclude to infer the underlying homeostasis strategies.

Major comments:

The model is rather general and powerful. The simplifying assumption seems reasonable (and the authors investigate to some extent its limitations, i.e. Fig. 2). The conclusions are overall convincing.

1. My main concern is that the metrics that the authors use to assess concentration homeostasis (i.e. the γ parameter and the presence/absence of peak in power spectrum) do not seem quite appropriate to describe how much variability/fluctuations in concentration are driven by cell cycle effects. Indeed, the γ parameter measures how much the average concentration in each cell cycle stage varies throughout the cell cycle. However, this variability should be compared to the total variability due to both cell cycle effects and stochastic bursting dynamics. A given level of cell-cycle dependency (say γ=0.2) could be very visible if gene expression is weakly noisy (e.g. B low and <n> high) and completely invisible is gene expression is highly bursty (large B and small <n>). In the latter situation, cell-cycle effects would be meaningless for the cell to minimize. In essence, re-using the authors notations, I think γ / ϕ^1/2, would be a more relevant metric to observe.
2. Similarly, when inspecting the peak in the power spectrum, the weight of the Lorenztian function(s) creating the peak, should be compared to the stationary component (λ_N, u_N in thhe authors' notations).

A complementary analysis including these two points and a discussion the relative contribution of cell-cycle effects and bursting dynamics in the total variability/fluctuation of concentrations would be important to include.

Minor comments:

1. The dashed line on Fig. 3a is defined as κ = sqrt(2)^(1-β). First is this empirical or does it come from a derivation? Second, it seems incomplete since it should depend on ω. Intuitively, this line should correspond to the value of κ that would best mimic balanced biosynthesis in the case where β≠1. In other words, κ should be so that <ρB' / V(t)>_prereplication = <κρB' / V(t)>_postreplication which yields κ = 2^(ω(1-β)) * (ω-1)/ω * [2^(ω(β-1))-1]/[2^((1-ω)(β-1))-1] This indeed simplifies into κ = sqrt(2)^(1-β) when ω=0.5.
2. η is used in the caption of Fig. 2, which is cited on page 4. But it is defined only 2 sections later, on page 6.
3. ω is used in the main text, but only defined in the caption of Fig. 3.
4. ω is defined as "the proportion of cell cycle before replication". Is this in terms of cell cycle stages (i.e. ω=N_0/N) or actual time?
5. Fig. 3 indicates that power spectra are normalized so that G(0)=1, but G(0)=10 on the first two graphs.
6. Page 11: "bimodality in the concentration distribution is significantly less apparent". I would suggest rephrasing "bimodality in the concentration distribution is absent" since there should be no reference to "significance" and bimodality is either present or absent (binary), not less apparent.

Referees cross-commenting

Part 1.

I agree with reviewer 1 that a table of symbols would be helpful. On reviewer 3's second Major Comment, I don't think that the "the lifetime of a stage [has to be] much larger than the time needed to generate a burst". From how the authors write and solve the master equation, I don't think that such a separation of timescale is necessary. The authors should indeed clarify this and if reviewer 3 is correct, then that's indeed a major limitation. On reviewer 3's second Major Comment, I don't think that the "the lifetime of a stage [has to be] much larger than the time needed to generate a burst". From how the authors write and solve the master equation, I don't think that such a separation of timescale is necessary. The authors should indeed clarify this and if reviewer 3 is correct, then that's indeed a major limitation. On reviewer 3's comment "DNA replication [...] does not occur after a fixed number of exponential stages", I don't think I agree with this statement. Cell cycle progression relies on an ensemble of biochemical reactions. Representing this as a set of exponential waiting-time distributions with different means is probably amongst the most general and agnostic ways of representing this. Whether these exponential waiting-times only depend on cell volume is another question. This actually links back to reviewer 3's first Major comment and reviewer 1's comment that the concept of "stage" should be better discussed.

Regarding the need for "estimates of the biases introduced by the mean field approximation" (reviewer 3), I guess that's the goal of figure 2. Maybe reviewer 3 should make more explicit what she/he would like to see.

Regarding the comment from reviewer 3 that "a direct validity test should use datasets of at least two types (total, nascent RNA, etc)". I almost made a related comment in my review, but then I held it off: This issue with using nascent RNA data is that their model does not allow an ON state. They assume that gene products are produced in instantaneous bursts, which is a fair assumption if the lifetime of gene products is large compared to the time the gene stays ON. This is ok if the considered "gene products" are mRNA or proteins, but not nascent RNAs (for which the lifetime is the time to transcribe the gene). I did not make this comment in the end because I think the model is useful regardless. To comply with reviewer 3's request, maybe the authors could use distributions of mRNA and protein products, but I'm not sure that such data exists (since they need cell-cycle-resolved data).

I disagree with the statements that "the proposed model is based on a number artificial choices that are difficult to justify biologically" and that "the model is not minimal but depends instead on a huge number of parameters." In my opinion, the model is elegantly simple to capture the mechanisms under study (i.e. the effect of cell cycle and cell volume on stochastic gene expression). It is expressed so that the model captures a broad range of situations (i.e. it reduces to simpler models as a matter of choosing parameter values, e.g. \Beta=0 => transcription independent of cell cycle; \alpha => \infty cell cycle depends only on size ...). I do not think that a series of exponential distributions for cell cycle progression is inappropriate, it is the most agnostic and general way of representing an ensemble of biochemical reactions that would be meaningless to describe explicitly. Instead, only their dependency on cell volume is taken into account (and in a very general way, i.e. parameters 'a' and \alpha). It is fair to ask the authors to clarify the concept of "stage", but I see this model as being as simple as possible, but not simpler, for the authors' purpose.

Finally, I agree that the paper is probably "not suitable for biologists" but disagree that "for mathematicians, the calculations are rather standard and may seem trivial."

Part 2. Resp. to reviewer 3 on the master equation (Part 1 of Rev3):

Ok, I understand better your comment. What you mean by "the time needed to generate a burst" is the time that the gene produces RNAs, not the lifetime of the gene product (which is 1/d). That's true. It is essentially the same ifdea as what I write in my previous comment about nascent RNA data not being well captured by the model. Again, I think this is fine for "gene products" that are somewhat stable (not the case for nascent RNAs, but ok for mRNAs and proteins). This is fine by me as long as the authors explicit better this limitation of their model.

Part 3. Response to Reviewer 3 (Part 2 of Rev 3)

• concerning replication: Note that the mean field approximation is on cell volume, not on stage progression ("To simplify this model, [...] we ignore volume fluctuations at each stage but retain fluctuations in the time elapsed between two stages", p3). So the time at which replication occurs is already a random variable in the model. It is the sum of all the exponentially distributed random variables corresponding to stages 1 to N_0. The resulting distribution of replication time from the start of cell cycle is a random variable, which can be anything from very deterministic (N_0 very high) to very variable (N_0 very low).
• concerning nascent mRNA, ON/OFF etc. : I'm not sure I get your objection, but the best is probably to let the authors respond to your original comment.
• concerning parsimony: Ok, you're right. The authors should test it.

Significance

The advance of this paper is essentially technical. The authors present a model that incorporates and unifies previously studied effects (cell volume homeostasis, concentration homeostasis, bursting transcription). There is no major conceptual novelty, but the combination of these different aspects and the derivations that authors present are very valuable and might be applicable to interpret data in various species.

The paper is suitable for a physics/mathematics/computational audience. It is rather technical and would not be understood by readers with only a biology background.

Field of expertise of the reviewer: Gene regulation, single-molecule imaging, stochastic modeling.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

This is a report on "Concentration fluctuations due to size-dependent gene expression and cell-size control mechanisms," by jia, Singh, and Grima. This manuscript constructs a gene expression model with various factors. Specifically, the effect of cell size on gene expression is considered, which is often ignored by previous studies.

One interesting finding is that the absolute number of the gene products and the concentration can have different distributions. Some predictions of the models are validated by experimental data on E. coli and yeast.

This manuscript uses the mean-field approximation for cell volume, which has good accuracy when the number of stages is large. The usage of the power spectrum has a satisfactory effect on studying the concentration oscillation. Overall the paper was very difficult to follow and digest easily because of all the different factors and mechanisms invoked. It is mainly an issue of providing sufficient details for each of the factors and organizing them in a systematic and logical way. Although there is a supplementary appendix, it was hard to keep track of all the elements in the main mauscript. Perhaps something like Fig 1 of the Appendix can be presented in the main body to outline all the ingredients and how they affect each other.

It might be good to provide a more detailed description of the goal (studying gene product number and concentration under different parameters) after introducing the full and the reduced models. A table of symbols would also be helpful.

Some technical details in the Methods section are in fact helpful in understanding the conclusions. They can be moved to the Results section.

One concern is that the central concept of this manuscript, "stage", is not thoroughly discussed. This concept should have some significant biological meaning, not just be coined for mathematical convenience.

Fig. 1(b) is a little strange. For the left panel, the x-axis (stage) is discrete, then the volume (y-axis) should be a step function, not a straight red line.

Significance

The main advance is a more complete model of gene expression under more realistic organism growth conditions.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reply to the reviewers

We wish to thank all three reviewers for their thorough examination of our manuscript and their constructive criticism that allowed us to increase its quality. You will see that, following their recommendations, we have included a good amount of new data in the manuscript. Specifically, we added a new figure with experiments proposed by the reviewers (now Fig. 4), as well as Figs. S3 and S4. In addition, we expanded one paragraph of our Discussion to comment on a very recent article published by Huang et al in Nature Structural and Molecular Biology with conclusions pertaining the interplay of Rpd3 and Gcn5 in PHO5 gene regulation. Below we include the point-by-point response (in blue) with the changes we have implemented to address their specific points. All the additions and changes in the manuscript are made in red.

Referee #1

Evidence, reproducibility and clarity

In this manuscript, Novačić et al., investigate into a mechanisms of the non-coding transcriptiondriven regulation of the phosphate-responsive PHO5 gene. The authors employ CRSPRi system to discern direct contribution of the antisense non-coding transcription (CUT025) expressed during phosphate -rich conditions to transcriptional repression of the yeast PHO5 gene and therefore challenging previous study from the Svejstrup's lab that proposed a positive role for non-coding transcription in control of PHO5 gene. They propose a model where non-coding transcription represses PHO5 by mediating recruitment of Rpd3 histone deacetylase leading to altered chromatin structure at PHO5 promoter due to reduced recruitment of the RSC chromatin remodelling complex. Overall, the data presented in the manuscript are of a good quality, experiments are well controlled and nicely presented. Manuscript is well written. My specific comments are below: 1. I am somewhat confused by the data presented in Figure 5. While there is similar impact on the chromatin structure seen in rrp6D and air1Dair2D strains (Fig 5C) that corresponds to more "closed" configuration of chromatin , it is not consistent with H3 ChIP data that show higher nucleosome occupancy across PHO5 UAS in rrp6D but loss of nucleosomes in the double mutant (or there is a mistake perhaps while plotting the data?)

We now realize that the data was plotted confusingly, and we apologize for it. While doing the H3 ChIP experiment we only prepared the +Pi samples for the air1Δ air2Δ double mutant. In the figure we only included this one data point for the double mutant, which could lead to the false conclusion that at other timepoints there are no histones at its PHO5 promoter region. We decide to remove this data point from the figure to avoid the confusion and only keep the air1Δ air2Δ data for the ClaI assay. We believe that this should not be an issue as this data point is not critical for the conclusions we are making.

1. To further explore direct link between nc transcription, Rpd3 and rrp6 mediated effect, I suggest to test the effect on PHO5 induction upon rpd3 and rrp6 deletions in CRISPRi CUT025 background.

We performed this experiment and now include it as Fig. S3 in the manuscript. As expected, expressing the CRISPRi system only made difference when Rpd3 was present.

1. It seems that most noticeable effect of blocking nc transcription by an elegant approach that utilizes CRISPRi system on the phosphatase activity is seen between 0-1.5h of induction. I suggest taking additional time points at 30-45 min.

We took additional timepoints and the results were incorporated as the new Fig. 5E. The CRISPRi effect resulting in higher acid phosphatase activity was still most noticeable after 1,5 h of induction. This was mostly in line with the fact that the difference in PHO5 mRNA levels was most pronounced after 30 min of induction (Fig. 5D), as the time needed to achieve measurable protein level after induction can lag significantly for secretory proteins, such as acid phosphatase. Secretory proteins are cotranslationally translocated into the ER, after which they traverse the secretory pathway and undergo modifications before being finally exported to the periplasm where their activity can be measured. Consequently, the increase in acid phosphatase activity upon induction is only measurable after at least an hour.

1. How do authors explain that the effect of the exosome mutations are reversed and phosphatase activity is increased at later time point (20 h, Fig 2A)? I suggest using more distinct colour for dis3 mutants.

That effect is indeed somewhat surprising. We hypothesize that the effects we are seeing after 20 h reflect the specific conditions of prolonged induction, i.e. keeping the chromatin open or semi-open for a very long period of time, which do not necessarily reflect the early gene induction period that we are using as a read-out of the effect of different mutations on acid phosphatase expression kinetics. We previously noticed a similar effect with chromatin remodeler-related mutants (e.g. rsc2Δ, unpublished result from S. Barbarić group), which speak in favour of the prolonged induction conditions resulting in a chromatin state with its own specialized cofactor requirements. We therefore consider the chromatin state after prolonged induction a topic for another study, however, we now comment on this effect in the manuscript. The dis3 mutants are now shown in more distinct colours.

1. Figure 5A -label "H3 ChIP"

The label was added.

1. Error bars are quite high in Fig 1C, perhaps it is worth repeating the experiment

Since significant differences in PHO5 mRNA levels can be seen between wt and rrp6Δ mutant cells at 0,75 and 3 h of induction, we feel that the higher error bars at 5 h of induction are not worth repeating the experiment – especially since the values are bound to converge to a similar one after a longer induction period, as demonstrated in Fig. 1D.

Significance

significant of interest for general audience

Referee #2

Evidence, reproducibility and clarity

The authors study the PHO5 locus, which is known to a have antisense transcript and that has previously been shown the be important for activation of Pho5 sense transcription. The authors challenge the idea by an extensive analyses. They show the Pho5-AS represses sense transcription, and thus fits in the category as AS repressors instead of activators. They show a correlative data that when antisense goes down and sense goes up. They show that increase antisense levels leads to decrease sense levels. They use mutants of decay pathways to increase the levels antisense transcription. Moreover, they used crispri to repress the antisense transcript. Lastly, they show that histone deacetylation represses Pho5 sense. The data in the manuscript is convincing, and well presented. One thing that needs further clarification is the strategy to increase anti-sense levels by deletion mutants of decay or depletion of decay pathways. While it is clear that this stabilizes the pho5-AS and decrease pho5-sense, it is not clear that this causes an increase in transcription. Perhaps, it is possible that antisense transcript itself has a repressive effect. If one really wanted to increase antisense transcription than the antisense promoter should be increased in strength. On the other the CriprI experiment is very convincing. I am surprised how well the crisprI system works, it is thought to be not so efficient at blocking elongating polymerase and good at blocking initiation.

We thank the reviewer for this feedback. We performed additional experiments which you will find described below. Based on the results, we would like to keep the point about AS transcription causing the effect.

Major comments: - Are the key conclusions convincing? Perhaps, the conclusion that increased transcription leads to repression is not completely convincing. The authors use mutants in rrp6, exosome, and nrd1 to increase Pho5-AS transcription elongation. However, I am always under impression that these mutants stabilize the transcript. And the authors acknowledge this in their manuscript. So how do you discriminate between increased stability versus increased elongation? I support the conclusion that inhibition of Pho5-AS leads to increase Pho5-S. However, increase in elongation is not directly demonstrated. While still possible, it is equally possible that a more stable pho5-AS transcript has a repressive an effect on Pho5-AS. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? See above. Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. If the authors want to keep the message that increased transcription of Pho5-AS leads to more repression that may need to consider additional experiments. For example, increasing transcription from the antisense promoter.

We performed the proposed experiment and now include it in the manuscript as Fig. 4AB. Briefly, we inserted the strong constitutive TEF1 promoter in the antisense configuration downstream of the PHO5 gene ORF, so that it drives AS transcription. The results of this experiment very clearly show the inverse relationship between PHO5 mRNA and AS transcripts levels at +Pi conditions. Importantly, this strong constitutive AS transcription had an even more pronounced effect on PHO5 gene expression than deletion mutant backgrounds (in which, like in wt cells, the AS promoter is presumably weak), and did not allow for full level of PHO5 gene expression to be reached. To verify that the AS RNA itself does not have a regulatory role, but rather the act of its transcription represses the corresponding gene, we performed an additional experiment with appropriate diploid strains. The design of this experiment is standardly used to test whether an AS transcript can work in trans (for example see Nevers et al. 2018 NAR Fig. 6). This experiment is now included as Fig. 4C. Together, the results of these experiments paint a clear picture of AS transcription, and not AS level/stability itself, driving the repression of the PHO5 gene.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. To me this is an optional experiment, but it would benefit the manuscript
• Are the data and the methods presented in such a way that they can be reproduced? yes - Are the experiments adequately replicated and statistical analysis adequate? yes

Minor comments: - Specific experimental issues that are easily addressable. - Are prior studies referenced appropriately? yes - Are the text and figures clear and accurate? Yes - Do you have suggestions that would help the authors improve the presentation of their data and conclusions? no

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The manuscript challenges previous work where it was claimed that Pho5-AS is important for activation of Pho5-S. As such, it is important work. In the field of noncoding the transcription the Pho5-AS fits in a class of AS transcript that has been well described.
• Place the work in the context of the existing literature (provide references, where appropriate). See above.
• State what audience might be interested in and influenced by the reported findings. In researchers in field of transcription, chromatin, and more specifically in yeast gene regulation.
• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. Chromatin, transcription, yeast.

Referee #3

Evidence, reproducibility and clarity

Novačić et al present a manuscript entitled "Antisense non-coding transcription represses the PHO5 model gene via remodeling of promoter chromatin structure" which is a locus-specific follow up to previous studies from Soudet and Stutz groups on genome-wide analysis of transcription interference mediated by antisense transcripts in S cerevisiae. Critically, the authors here employ a CRISPRi approach to reduce antisense transcription from reaching the PHO5 promoter and in doing so show that kinetics of PHO5 induction are increased as would be predicted from their previous model. Additionally, they show predicted epistasis between rpd3 and rrp6 on PHO5 expression and gcn5 and rrp6 that are consistent with their model. Comments are relatively minor but should be addressed. Introduction p3. "This mechanism was subsequently explored genome-wide in yeast, which revealed a group of genes that in the absence of Rrp6 accumulate AS RNAs and are silenced in an HDACdependent manner (14)." This sentence appears awkward- perhaps move "in the absence of Rrp6" to after "AS RNAs"?

Corrected as proposed.

p3 "Under a high phosphate concentration Pho4 undergoes phosphorylation by the cyclindependent-kinase (Pho80-Pho85)" Since "the" is used, don't use parentheses around Pho80-Pho85

Corrected as proposed.

Methods Give amount/concentration of glycine used in quenching formaldehyde for ChIP. Give the exact wash conditions and buffers not "extensively"

All of those details are now provided in the manuscript. Figure 4C.

Describe schematic in legend

It is now described.

Figure 4D. Indicate time of induction in legend.

This was lacking for Figs. 4B-C (now 5B-C) so we added it there.

Figure 5A. air∆ data are missing from later time points?

Please see our first response to Reviewer 1. We removed the air1Δ air2Δ double mutant data, as we only had one data point for it in this assay.

Figure 6. Legend needs to indicate what Pi conditions are. Since PHO5 expressed, appears to be low Pi. An issue that needs to be discussed is that rpd3∆ appears to decrease expression of PHO5 AS. Is this simply because of increased PHO5 expression? Does rpd3∆ have any effects on AS in high Pi? This is important to interpret if effects of rrp6 and rpd3 are epistatic or additive.

We thank the Reviewer for bringing this to our attention. To explore the effect of rpd3Δ on PHO5 AS level, we quantified the PHO5 AS transcript by RT-qPCR with cells grown in (chemically defined) high Pi medium, which we now include in Fig. 7A. We find that rpd3Δ mutation has practically no effect on PHO5 AS transcript level both in the wt and the rrp6Δ mutant background. This result speaks in favor of rrp6Δ and rpd3Δ being epistatic rather than additive.

Figure 7. Sth1-CHEC data are hard to interpret. Some sort of quantification might be required as effects are not clear from the browser track nor is it clear from browser track that the results are reproducible. Examination of Sth1-AA effects in gcn5∆ background might be more compelling that the effect on RSC is via acetylation. Otherwise it is a bit hard to say as RSC could be functioning in parallel to the acetylation-dependent pathways implicated.

We agree that the presumption that histone acetylation recruits RSC to the PHO5 gene promoter had to be tested. We therefore include the experiment involving Sth1-AA depletion in the gcn5Δ background as Fig. 8A. This experiment was complicated by the fact that RSC is highly abundant (and at the same time essential for cell viability), but we resolved this by starting to deplete RSC two hours before gene induction. These results position RSC and Gcn5 in the same pathway. In contrast, more complete Sth1 depletion severely impaired viability of the rrp6Δ mutant, making it hard to interpret the effect, so we now include this result as Fig. S4.

To show the effect of AS transcription on RSC recruitment to the PHO5 promoter more quantitatively, we re-analyzed the Sth1-CHEC data (for two independent biological replicates) and now include the log2 values for the changes in Sth1 binding in the text of the manuscript.

Significance

The work is focused and narrower in impact but important because direct tests of locus-specific effects are performed, validating models from previous genomic analyses. **Referees cross-commenting**

I think the other reviews are very reasonable. I would just suggest to the authors that they think carefully about the reviews and decide what they think is most valuable to improving the work/presentation

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Novačić et al present a manuscript entitled "Antisense non-coding transcription represses the PHO5 model gene via remodeling of promoter chromatin structure" which is a locus-specific follow up to previous studies from Soudet and Stutz groups on genome-wide analysis of transcription interference mediated by antisense transcripts in S cerevisiae. Critically, the authors here employ a CRISPRi approach to reduce antisense transcription from reaching the PHO5 promoter and in doing so show that kinetics of PHO5 induction are increased as would be predicted from their previous model. Additionally, they show predicted epistasis between rpd3 and rrp6 on PHO5 expression and gcn5 and rrp6 that are consistent with their model. Comments are relatively minor but should be addressed.

Introduction

p3. "This mechanism was subsequently explored genome-wide in yeast, which revealed a group of genes that in the absence of Rrp6 accumulate AS RNAs and are silenced in an HDAC-dependent manner (14)."

This sentence appears awkward- perhaps move "in the absence of Rrp6" to after "AS RNAs"?

p3 "Under a high phosphate concentration Pho4 undergoes phosphorylation by the cyclin-dependent-kinase (Pho80-Pho85)"

Since "the" is used, don't use parentheses around Pho80-Pho85

Methods

Give amount/concentration of glycine used in quenching formaldehyde for ChIP. Give the exact wash conditions and buffers not "extensively"

Figure 4C. Describe schematic in legend

Figure 4D. Indicate time of induction in legend.

Figure 5A. air∆ data are missing from later time points?

Figure 6. Legend needs to indicate what Pi conditions are. Since PHO5 expressed, appears to be low Pi. An issue that needs to be discussed is that rpd3∆ appears to decrease expression of PHO5 AS. Is this simply because of increased PHO5 expression? Does rpd3∆ have any effects on AS in high Pi? This is important to interpret if effects of rrp6 and rpd3 are epistatic or additive.

Figure 7. Sth1-CHEC data are hard to interpret. Some sort of quantification might be required as effects are not clear from the browser track nor is it clear from browser track that the results are reproducible. Examination of Sth1-AA effects in gcn5∆ background might be more compelling that the effect on RSC is via acetylation. Otherwise it is a bit hard to say as RSC could be functioning in parallel to the acetylation-dependent pathways implicated.

Significance

The work is focused and narrower in impact but important because direct tests of locus-specific effects are performed, validating models from previous genomic analyses.

Referees cross-commenting

I think the other reviews are very reasonable. I would just suggest to the authors that they think carefully about the reviews and decide what they think is most valuable to improving the work/presentation

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors study the PHO5 locus, which is known to a have antisense transcript and that has previously been shown the be important for activation of Pho5 sense transcription. The authors challenge the idea by an extensive analyses. They show the Pho5-AS represses sense transcription, and thus fits in the category as AS repressors instead of activators. They show a correlative data that when antisense goes down and sense goes up. They show that increase antisense levels leads to decrease sense levels. They use mutants of decay pathways to increase the levels antisense transcription. Moreover, they used crispri to repress the antisense transcript. Lastly, they show that histone deacetylation represses Pho5 sense.

The data in the manuscript is convincing, and well presented. One thing that needs further clarification is the strategy to increase anti-sense levels by deletion mutants of decay or depletion of decay pathways. While it is clear that this stabilizes the pho5-AS and decrease pho5-sense, it is not clear that this causes an increase in transcription. Perhaps, it is possible that antisense transcript itself has a repressive effect. If one really wanted to increase antisense transcription than the antisense promoter should be increased in strength. On the other the CriprI experiment is very convincing. I am surprised how well the crisprI system works, it is thought to be not so efficient at blocking elongating polymerase and good at blocking initiation.

Major comments:

• Are the key conclusions convincing?

Perhaps, the conclusion that increased transcription leads to repression is not completely convincing. The authors use mutants in rrp6, exosome, and nrd1 to increase Pho5-AS transcription elongation. However, I am always under impression that these mutants stabilize the transcript. And the authors acknowledge this in their manuscript. So how do you discriminate between increased stability versus increased elongation? I support the conclusion that inhibition of Pho5-AS leads to increase Pho5-S. However, increase in elongation is not directly demonstrated. While still possible, it is equally possible that a more stable pho5-AS transcript has a repressive an effect on Pho5-AS.<br /> - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

See above. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

If the authors want to keep the message that increased transcription of Pho5-AS leads to more repression that may need to consider additional experiments. For example, increasing transcription from the antisense promoter. - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

To me this is an optional experiment, but it would benefit the manuscript - Are the data and the methods presented in such a way that they can be reproduced?

yes - Are the experiments adequately replicated and statistical analysis adequate?

yes

Minor comments:

• Specific experimental issues that are easily addressable.
• Are prior studies referenced appropriately?

yes - Are the text and figures clear and accurate?

Yes - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

no

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

The manuscript challenges previous work where it was claimed that Pho5-AS is important for activation of Pho5-S. As such, it is important work. In the field of noncoding the transcription the Pho5-AS fits in a class of AS transcript that has been well described. - Place the work in the context of the existing literature (provide references, where appropriate).

See above. - State what audience might be interested in and influenced by the reported findings.

In researchers in field of transcription, chromatin, and more specifically in yeast gene regulation. - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Chromatin, transcription, yeast.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this manuscript, Novačić et al., investigate into a mechanisms of the non-coding transcription-driven regulation of the phosphate-responsive PHO5 gene. The authors employ CRSPRi system to discern direct contribution of the antisense non-coding transcription (CUT025) expressed during phosphate -rich conditions to transcriptional repression of the yeast PHO5 gene and therefore challenging previous study from the Svejstrup's lab that proposed a positive role for non-coding transcription in control of PHO5 gene. They propose a model where non-coding transcription represses PHO5 by mediating recruitment of Rpd3 histone deacetylase leading to altered chromatin structure at PHO5 promoter due to reduced recruitment of the RSC chromatin remodelling complex.

Overall, the data presented in the manuscript are of a good quality, experiments are well controlled and nicely presented. Manuscript is well written. My specific comments are below:

1. I am somewhat confused by the data presented in Figure 5. While there is similar impact on the chromatin structure seen in rrp6D and air1Dair2D strains (Fig 5C) that corresponds to more "closed" configuration of chromatin , it is not consistent with H3 ChIP data that show higher nucleosome occupancy across PHO5 UAS in rrp6D but loss of nucleosomes in the double mutant (or there is a mistake perhaps while plotting the data?)
2. To further explore direct link between nc transcription, Rpd3 and rrp6 mediated effect, I suggest to test the effect on PHO5 induction upon rpd3 and rrp6 deletions in CRISPRi CUT025 background.
3. It seems that most noticeable effect of blocking nc transcription by an elegant approach that utilizes CRISPRi system on the phosphatase activity is seen between 0-1.5h of induction. I suggest taking additional time points at 30-45 min.
4. How do authors explain that the effect of the exosome mutations are reversed and phosphatase activity is increased at later time point (20 h, Fig 2A)? I suggest using more distinct colour for dis3 mutants.
5. Figure 5A -label "H3 ChIP"
6. Error bars are quite high in Fig 1C, perhaps it is worth repeating the experiment

Significance

significant

of interest for general audience

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Revision Plan

1. General Statements

We really appreciate the positive comments and suggestions of the reviewers on our submitted manuscript. We think we will be able to solve the issues inquired by reviewers by adding new data and revising the phrases as detailed below.

2. Description of the planned revisions

Reviewer #1:

Major comments

Localization analysis of a transiently expressed MAP70 transgene with inactivating phosphosite mutations would be important to see whether the identified conserved phosphosites are relevant for MAP70 interaction with MTs. This experiment could be performed rapidly using transient expression in BY-2 cells.

We agree on the importance of this analysis. Therefore we are currently preparing fluorescent markers of Nt-MAP70-2-like and its phospho-blocked (Ala) version to coexpress with MT and nuclear markers in BY-2 cells. We estimate that we need three more months to complete this experimsnt.

The authors propose that PP2 blocks phragmoplast formation by preventing phosphorylation of class II Kinesin-12 proteins. In support, authors show that PP2 treatment correlates with a decrease in KIN12A phosphopeptide count (not fully abolished) and its failure to localize to emerging phragmoplasts in BY-2 cells and Physcomitrium. As class II Kinesis-12 proteins have been previously implicated in phragmoplast assembly this is a fairly reasonable hypothesis, but would benefit from the analysis of transgenic KIN12A variants carrying inactivating (A) or potentially activating (D/E) phosphosite mutations. Is loss of phosphorylation sufficient to prevent phragmoplast localization? Can an activated variant rescue PP2-induced KIN12A localization and cell division defects? As above, using transient expression in BY-2 cells would be a fast approach to tackle these questions.

We are currently preparing fluorescent markers of phospho-blocked (Ala) and phospho-mimic (Asp) versions of KIN12A (PAKRP1) to coexpress with MT and nuclear markers in BY-2 cells. We will check whether they localize to phragmoplast and also test PP2 effects. We would need three more months to complete these analyses.

Reviewer #2:

Major comments

• The manuscript would strongly benefit from being revised by a native english speaker. There are many unusual or awkward formulation, in particular in the abstract.

We apologize for unnatural sentences. After adding new data and correcting the manuscript, we will ask a native english speaker to revise it.

Reviewer #3:

Major comments

The major concern is lack of evidence to connect MAP70 and MT disruption upon treatment with PD-180970, in contrast to PP2, which was shown to affect localization of Kinesin-12. I wonder if authors could use taxol to stabilize MTs, then observe the localization of MAP70 with application of PD-180970?

As we responded to reviewer 1, we are preparing the fluorescent marker of Nt-MAP70-2-like to coexpress with MT and nuclear markers in BY-2 cells. By using this multi-color marker, we will test whether PD-180970 affects the localization of MAP70 on MTs, also using taxol. However, in our experiene, taxol is not a very effective inhibitor and may not work in our transient expression system in BY-2 cells. In that case, we will analyze whether phospho-mimic (Asp) version can prevent MT disruption in the presence of PD-180970 to assess the relation of PD-180970, MAP70 and MT disruption.

I have another concern on the action of PD-180970. PD-180970 appears to affect ubiquitously indispensable proteins for MTs. If PD-180970 disrupt MT by inhibiting phosphorylation of some MAPs, it must need time for turnover of proteins phosphorylated before PD-180970 was applied. In the proteomics experiment, author treated the cells with the compounds for 8-9 hr. On the other hand, in BY-2 cells, PD-18970 disrupted MTs only 30 min after application of PD-180970. I wonder if proteins were replaced during the 30 min. Could authors examine how long it takes to affect interphase MTs? If PD-180970 disrupts MTs in a 5-10 min like oryzalin, it is unlikely that inhibition of phosphorylation of proteins like MAP70 caused MT disruption. Rather, it may inhibit some proteins that have activity to disrupt microtubules but are usually inactivated by phosphorylation or inhibit something directly without phosphorylation.

We agree that there is no evidence that PD-180970 disrupts MTs by inhibiting phosphorylation of MAP70. In our live-imaging system, in which reagents are added to liquid cultivation medium, the time from the reagent application to the arrival to each cell varies. Therefore, in order to accurately measure the time required for the inhibitor to take effect, it is necessary to design a new assay system, such as using fluorescent dyes to monitor the reagent's diffusion. In addition, since some reactions mediated by protein phosphorylation occur rapidly, minute-order observations might not be sufficient. Therefore, as an alternative strategy to assess the direct involvement of MAP70 phosphorylation on MT stabilization, we will examine whether PD-180970 induces MT disruption using strains expressing the phospho-blocked (Ala) and phospho-mimic (Asp) versions of MAP70 described above.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Reviewer #1:

Minor comments

The authors identified the analogs PD-166326 and PP1 as potent inhibitors of cell division. For completeness, it would be interesting to include a description of these arrest phenotypes and how they compare with that of PD180870 or PP2.

We have added the effects of all tested compounds on Arabidopsis embryos in Fig. S3C and Table S1. Based on this data and the results of tobacco BY-2 cells, we have compared the effects of PD-166326 and PD180870, and PP1 and PP2 in Results.

Although there are two more obvious candidates in the phosphoproteome datasets on which the authors focus on, there is very little discussion on whether the other top hits and whether they might be involved in cell division. On a related note, there is no discussion on the specificity of these compounds and the likelihood of phenotypes unrelated to cell division.

We have added the information of “Similar proteins in Arabidopsis” and “Description and putative functions” for all identified candidates for PD-180970 and PP2 in Table S2 and S3, respectively. With referring this information, we have added the sections to describe the possible contributions of these candidates on MT organization and phragmoplast formation in Results. In addition, we have described the specificity of these compounds and the phenotypes unrelated to cell division in the section for the results of Arabidopsis roots (Fig. S2A).

1st results section:

"...developed into the globular stage without causing morphological defects..."

Should omit the word "causing" or replace with "any/detectable"

We have omitted the word "causing".

Reviewer #2:

Even if the identification of the kinase(s) targeted by these two compounds is missing, the characterisation of at least two downstream effectors of these elusive kinase(s) inhibited by PD-180970 and PP2 is an important step forward. I would recommend to this point make very clear in the writing (e.g. already in the abstract). Upon a superficial reading, the reader could assume that MAP70s and PAKRP1s are the direct molecular targets of these compounds.

We appreciate the very positive comments. To clarify this point, in addition to the following responses to each suggestion, we have changed the last sentense of the abstract to “These properties make PD-180970 and PP2 useful tools for transiently controlling plant cell division at key manipulation nodes that are conserved in diverse plant species”.

Major comments

• I would modify the title to shift the emphasis from the methodology to the biological targets identified.

We have changed the title to “Identification of novel compounds inhibiting microtubule organization and phragmoplast formation in diverse plant species”.

• Concerning MAP70s the authors claim that there is little functional data about this family. Yet, a recent paper (https://www.science.org/doi/10.1126/sciadv.abm4974) identifies MAP70-5 as necessary for the proper organisation of CMTs in the endodermis and its ability to actively remodel to accommodate emergence of the lateral root primordium in Arabidopsis thaliana. This could provide a functional context to test several of the predictions that the authors list in the discussion.

We have referred this paper in Results and Discussion, as “MAP70-5 was reported to increase MT length in vitro and to reorganize cortical MTs to alter the endodermal cell shape for lateral root initiation, suggesting that MAP70-5 mediates dynamic change of MT arrays”.

Minor comments

• The narrative would be improved by moving the section "PD-180970 and PP2 do not irreversibly damage viability" before the phosphoproteomic section.

We have moved the “irreversibly” section to before the “phosphoproteomics” section.

Reviewer #3:

Minor comments

In supplemental data, authors show only 12 or 14 candidates of the target. It is interesting how other MAPs including homologues of MAP70 and Kiesnin-12 in BY-2 cells were scored in the phospho-proteomics assay. I suggest authors show longer lists of proteomics including other MAPs. It would be valuable information for the research community.

We apologize for not providing the complete dataset. We have added Dataset S1 of total protein sequences that we predicted from published RNA-sea data of BY-2 cells, and all identified proteins of phosphoproteomics assay for PD-180970 and PP2 in Datasets S2 and S3, respectively. We have moved the lists of top candidates to Tables S2 and S3.

In Abstract, authors should mention that the two compounds reduced phosphorylation level of diverse proteins including MAP70 and Kinesin-12. This is very important results and, otherwise, it may cause misunderstanding of the activity of the compounds. In addition to this, it is better to rephrase the following sentence. "presumably by inhibiting MT-associated proteins (MAP70)" with "presumably by inhibiting phosphorylation of MT-associated proteins (MAP70)."

To avoid such a misunderstanding, we have changed the descriptions in Abstract to “Phosphoproteomic analysis showed that these compounds reduced phosphorylation level of diverse proteins. In particular, PD-180970 inhibited phosphorylation of the conserved serine residues in MT-associated proteins (MAP70). PP2 significantly reduced the phosphorylation of class II Kinesin-12, and impaired its localization at the phragmoplast emerging site”. Due to this change, the suggested sentence was eliminated. Also in Discussion, we have mentioned the reduction of phosphorylation of various proteins by stating, "we found that PD-180970 and PP2 reduced the phosphorylation levels of diverse proteins. These parts may be further modified depending on the results of the phospho-blocked (Ala) and phospho-mimic (Asp) analyses.

Page7 line 1st. it would be better to insert "of MAP70 family" after "in the conserved MT-binding domain" because the MT binding domains are unique to the MAP70 family. I could not understand why this is " (2nd line) consistent with PD-18970 severely disrupting all the tested MT structure". At current stage, there is no evidence that dephosphorylation of MAP70 caused the microtubule disruption. I suggest authors remove the sentence (", which was~MT structures").

We agreed on both points and have corrected them as the reviewer suggested.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

This manuscript by Kimata and colleagues describes identification of compounds that inhibit microtubule organization and cell division in plants. In this manuscript, authors screened two chemical libraries and successfully found two compounds, PD-180970 and PP2", as potent inhibitors of cell division. Because the two compounds act as kinase inhibitor in animal cells, authors analyzed their effects on phosphorylation by using BY-2 suspension cells. Among the affected proteins, authors focused on two microtubule-related proteins, MAP70 and Kinesin-12. Authors showed that PD-180970 disrupt all structures of microtubules in BY-2 cells. All members of Arabidopsis MAP70 shared the target residues, although Arabidopsis map70 mutants grew normally. PP2 abolished the localization of Kinesin-12 to phragmoplasts, and inhibit the cell plate formation. Both compounds worked in other plant species including moss. I think highly of the unique screening system using Arabidopsis zygote and BY-2 cells developed by the authors. Although the direct targets and specificity of the compounds are still to be determined, I think the two compounds should become powerful tools in plant cell biology in future. Generally, the manuscript is well written, and the data are of high quality. I have, however, several suggestions as below.

Major

The major concern is lack of evidence to connect MAP70 and MT disruption upon treatment with PD-180970, in contrast to PP2, which was shown to affect localization of Kinesin-12. I wonder if authors could use taxol to stabilize MTs, then observe the localization of MAP70 with application of PD-180970?

I have another concern on the action of PD-180970. PD-180970 appears to affect ubiquitously indispensable proteins for MTs. If PD-180970 disrupt MT by inhibiting phosphorylation of some MAPs, it must need time for turnover of proteins phosphorylated before PD-180970 was applied. In the proteomics experiment, author treated the cells with the compounds for 8-9 hr. On the other hand, in BY-2 cells, PD-18970 disrupted MTs only 30 min after application of PD-180970. I wonder if proteins were replaced during the 30 min. Could authors examine how long it takes to affect interphase MTs? If PD-180970 disrupts MTs in a 5-10 min like oryzalin, it is unlikely that inhibition of phosphorylation of proteins like MAP70 caused MT disruption. Rather, it may inhibit some proteins that have activity to disrupt microtubules but are usually inactivated by phosphorylation or inhibit something directly without phosphorylation.

Minor

In supplemental data, authors show only 12 or 14 candidates of the target. It is interesting how other MAPs including homologues of MAP70 and Kiesnin-12 in BY-2 cells were scored in the phospho-proteomics assay. I suggest authors show longer lists of proteomics including other MAPs. It would be valuable information for the research community.

In Abstract, authors should mention that the two compounds reduced phosphorylation level of diverse proteins including MAP70 and Kinesin-12. This is very important results and, otherwise, it may cause misunderstanding of the activity of the compounds. In addition to this, it is better to rephrase the following sentence. "presumably by inhibiting MT-associated proteins (MAP70)" with "presumably by inhibiting phosphorylation of MT-associated proteins (MAP70)."

Page7 line 1st. it would be better to insert "of MAP70 family" after "in the conserved MT-binding domain" because the MT binding domains are unique to the MAP70 family. I could not understand why this is " (2nd line) consistent with PD-18970 severely disrupting all the tested MT structure". At current stage, there is no evidence that dephosphorylation of MAP70 caused the microtubule disruption. I suggest authors remove the sentence (", which was~MT structures").

Significance

Redundancy of genes prevent researchers from exploring the genetic mechanisms of cell division. Time-specific manipulation of plant cell division by optogenetics or pharmacology has not been established. Identification of compounds that can specifically affect cell division is desired for further investigation of plat cell division. Although the direct targets and specificity of the compounds are still to be determined, I think the screening system and the two compounds identified by the authors should become powerful tools in plant cell biology in future. This work will influence not only plant biologists but also broad readership including cell/developmental biologists and chemical biologists.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

Kimata et al. report on the identification and characterisation of two compounds inhibiting cell division in plants. Motivated by the need to circumvent genes function redundancy to study cell division in plants, the authors screened 170 biologically active compounds for inhibitors of the first highly stereotypical division of the Arabidopsis zygote. They identify two compounds PD-180970 and PP2 that very potently block this division. Monitoring the effect of these compounds on microtubules dynamics and using high resolution imaging on BY-2 cell cultures, they conclude that PD-180970 inhibits MT organization while PP2 inhibits phragmoplast formation. These two compounds have reversible effects and are active in several plants species ( Arabidopsis, Tobacco, Cucumber and Physcomitrella). Both compounds targets kinases in animal cells. To shed light on the molecular mechanism perturbed by these compounds, the authors performed a phospho-proteomic profiling of synchronised BY-2 cells upon treatment by either of this compounds, controlled by inactive analogs. They identify two proteins which phosphorylation is severely reduced by the compounds. PD-180970 reduces the phosphorylation of members of the MAP70 at three conserved S residues, two mapping in the microtubule binding domains. PP2 reduces phosphorylation of PAKRP1/KIN12A and PAKRP1L//KIN12B a pair of phragmoplasts-associated kinesins. The authors show that PP2 disrupts the phragmoplast-localisation of the both kinesins, phenocopying the effects of the double mutant pakrp1/pakrp1l and thus providing a likely molecular mechanisms for the effects of PP2.

Overall the manuscript is solid, the experiments well executed and controlled and the results precisely. The conclusions are supported by the data and the manuscript is clearly structured.

Even if the identification of the kinase(s) targeted by these two compounds is missing, the characterisation of at least two downstream effectors of these elusive kinase(s) inhibited by PD-180970 and PP2 is an important step forward. I would recommend to this point make very clear in the writing (e.g. already in the abstract). Upon a superficial reading, the reader could assume that MAP70s and PAKRP1s are the direct molecular targets of these compounds.

Major comments:

• I would modify the title to shift the emphasis from the methodology to the biological targets identified.
• Concerning MAP70s the authors claim that there is little functional data about this family. Yet, a recent paper (https://www.science.org/doi/10.1126/sciadv.abm4974) identifies MAP70-5 as necessary for the proper organisation of CMTs in the endodermis and its ability to actively remodel to accommodate emergence of the lateral root primordium in Arabidopsis thaliana. This could provide a functional context to test several of the predictions that the authors list in the discussion.
• The manuscript would strongly benefit from being revised by a native english speaker. There are many unusual or awkward formulation, in particular in the abstract.

Minor comments:

• The narrative would be improved by moving the section "PD-180970 and PP2 do not irreversibly damage viability" before the phosphoproteomic section.

Significance

Plant cell biologists interested in cell division and microtubules will find this pre-print enticing. The compounds identified will reveal useful tools to analyse cell division in plants and the manuscript provides a significant technical advance. Although my expertise does not lay in the field of chemical inhibitors of cell division, there are to my knowledge, no compounds that selectively inhibit phragmoplast growth like PP2. The manuscript paves the way for further studies such as genetic suppressor screens to identify the plant kinase(s) targeted by these compounds.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this manuscript, Kimata and colleagues describe the identification of two reversibly acting compounds that affect specific stages of cell division through a chemical screen in in vitro cultured Arabidopsis zygotes. They further characterize the effects of these compounds on cell division using advanced imaging techniques, and demonstrate that they perturb cell cycle progression in multiple plant species and systems, thus acting on conserved pathways. Finally, using phosphoproteomics and transgenic approaches in cultured plant cells the authors identified potential indirect targets of these compounds. The work described is very thorough and well presented, with conclusions supported by the data. In addition it provides information on two compounds that can be broadly applied in plant molecular research and demonstrate the feasibility of an in vitro ovule culture system for chemical screening in plants.

Major comments

Localization analysis of a transiently expressed MAP70 transgene with inactivating phosphosite mutations would be important to see whether the identified conserved phosphosites are relevant for MAP70 interaction with MTs. This experiment could be performed rapidly using transient expression in BY-2 cells.

The authors propose that PP2 blocks phragmoplast formation by preventing phosphorylation of class II Kinesin-12 proteins. In support, authors show that PP2 treatment correlates with a decrease in KIN12A phosphopeptide count (not fully abolished) and its failure to localize to emerging phragmoplasts in BY-2 cells and Physcomitrium. As class II Kinesis-12 proteins have been previously implicated in phragmoplast assembly this is a fairly reasonable hypothesis, but would benefit from the analysis of transgenic KIN12A variants carrying inactivating (A) or potentially activating (D/E) phosphosite mutations. Is loss of phosphorylation sufficient to prevent phragmoplast localization? Can an activated variant rescue PP2-induced KIN12A localization and cell division defects? As above, using transient expression in BY-2 cells would be a fast approach to tackle these questions.

Minor comments

The authors identified the analogs PD-166326 and PP1 as potent inhibitors of cell division. For completeness, it would be interesting to include a description of these arrest phenotypes and how they compare with that of PD180870 or PP2.

Although there are two more obvious candidates in the phosphoproteome datasets on which the authors focus on, there is very little discussion on whether the other top hits and whether they might be involved in cell division. On a related note, there is no discussion on the specificity of these compounds and the likelihood of phenotypes unrelated to cell division.

1st results section: "...developed into the globular stage without causing morphological defects..." Should omit the word "causing" or replace with "any/detectable"

Significance

The work described in this manuscript identified and characterized two compounds that affect specific processes important for cell division in plant cells. Furthermore, the authors demonstrate the feasibility of an in vitro ovule culture system for chemical screening of specific processes in early plant embryos. The identified compounds are effective in multiple tissues in phylogenetically distant land plants and their effects are reversible. These compounds can be useful to, for example, manipulate the microtubule cytoskeleton, cell cycle, or ploidy in different plant models and different contexts, and more specifically to cell biologists studying the molecular mechanisms of cell division.

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

REVIEWER #1

__Summary: __Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

In virtue of the classical cancer stem cells (CSC) marker ALDH1A1 and SMAD Response Element (SRE) promoter, the authors engineered CSC-derived extracellular vesicles (EVs). By performing the second sortase (SrtA)-based proximity labeling, the authors detected the immune cells that specifically interacted with the CSC-EVs and demonstrated that CSC-EVs preferentially target MHC-II- macrophages and PD-1+ T cells.

---

Major comments: - Are the key conclusions convincing? No. CD63 is accepted as the exosome marker, but cannot represent the whole population of EVs. Especially, we do have the information on the percentage of CD63+ EVs among the total population derived by CSCs. However, it seems impossible to estimate the total population derived by CSCs. It is the inherent flaw of the strategy, which limits the accuracy of the labeling. One possible method is to label CD81+ and CD9+ EVs, together with CD63+ EVs, to study the immune cells interacting with CSC-EVs in vitro and in vivo.

We would like to thank this Reviewer for the time spent reading our manuscript and for highlighting the fact that other EVs markers could have been used to track EVs. We would like to point out that the Sortase-A experimental strategy is independent from any assumptions on EV markers since SrtA is fused to a commonly-used transmembrane domain (from PDGFR, see Hamilton et al. Adv Biosys 2020). Nonetheless, we followed up on the Reviewer suggestion and performed additional experiments to assess the overlap between this generic membrane marker, CD63 and CD81. To this end, we have performed multicolor nano-flow cytometry and stained EVs for SrtA (via its flag peptide) and CD63 or CD81 (new suppl. Fig. S2B-C). We used Flag staining to detect the PDGFR transmembrane domain as a generic membrane marker (__new suppl. Fig. S1C __and ref. 50). We observed that Flag staining colocalized with both CD63+ and CD81+ EVs, indicating not only that the use of a general-purpose transmembrane domain transcends classical EV biomarkers, but also that CD63 and CD81 label largely overlapping EV subpopulations, as previously reported (Jeppesen DK et al. Cell 2019). Accordingly, SrtA- and CD63-GFP-based strategies yielded very similar results (Fig. 2 and 4).

Compared with the normal cancer cells, cancer stem cells are a very small population. It is reasonable to consider that the CSC-EVs is also a small population among total EVs. Therefore, it is quite questionable to compare the interaction of normal cancer cells-derived EVs and CSC-EVs with immune cells.

We fully agree with this reasoning, and it is exactly because of this contrast that our observations of the specific behavior of CSC-EVs are very relevant for CSC biology. Our experimental design includes proper control groups and is based on validated approaches (Hamilton et al. Adv Biosys 2020).

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Yes. The authors stated "such EV-mediated intercellular communication between CSC and these immune cells contributed to the observed spatial interactions and niche sharing." Not enough evidence supported the statement.

We have removed these claims from the text.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. As mentioned before, if the authors could perform the labeling CD81+ and CD9+ CSC-EVs and study the interaction with immune cells, the conclusion may be more convincing.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. The suggested experiments are time-consuming.

We appreciate the Reviewer acknowledging that repeating the CD63-GFP experiments in the manuscript using CD81-GFP and CD9-GFP fusion reporters is very time-consuming. Nonetheless, we have provided proof that the SrtA approach labels both CD63+ and CD81+ EVs (new suppl. Fig. S2B-C), which, together with the fact that both CD63-GFP- and SrtA-based approaches yielded very similar results (Fig. 2 and 4), strongly indicates that repeating these experiments with additional reporters will add limited value to already sound conclusions.

• Are the data and the methods presented in such a way that they can be reproduced? Yes.

• Are the experiments adequately replicated and statistical analysis adequate? Yes.

Minor comments: - Specific experimental issues that are easily addressable. Yes

• Are prior studies referenced appropriately? The references related SrtA-mediated labeling were not sufficiently referenced.

The full characterization of SrtA-based strategy was cited in reference 50 (Hamilton et al. Adv Biosys 2020). We would be happy to include any reference this Reviewer thinks is missing.

• Are the text and figures clear and accurate? Yes

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? No

Significance: - Describe the nature and significance of the advance (e.g., conceptual, technical, clinical) for the field.

Cancer cells are heterogeneous. It is natural to believe that EVs are heterogeneous due to their different origin. Considering the important role of cancer stem cells during tumor development and treatment resistance acquisition, it is important to understand the function of CSC-EVs in the tumor microenvironment. However, considering the methodology is questionable, I am not sure the conclusions are convincing. For Figure 3, there are many pieces of literature on this topic and showing the data that macrophages in CSCs niches are good for the maintenance of CSC. So, it is not novel.

We thank the Reviewer to point out the importance of understanding the function of CSC-EVs in the tumor microenvironment. We hope we have addressed the methodology issues raised by this Reviewer. Although recent students outline the relationship between CSC and macrophages biology, very little is known about the role of EVs in this interaction. The novelty of our work stems from the use of advanced genetic engineering approaches that allow us to demonstrate directly in vivo, without any in vitro manipulation of CSC-EVs, that CSC-EVs come in contact with macrophages (and other specific immune subsets).

• Place the work in the context of the existing literature (provide references, where appropriate).

• State what audience might be interested in and influenced by the reported findings. Cancer stem cells or extracellular vesicles are timely topics and would be interesting to people in the cancer and EV fields.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate., EVs biology, with no special focus on CSCs.

REVIEWER #2

__Summary: __In this work Dr. Pucci and colleagues use flowcytometry and in vivo approaches to define the potential role of EVs originating from cancer stem cells to mediate intercellular communication with cells of immune origin in the cancer microenvironment. The work is interesting, the team used specific promoters to drive the expression of EV markers specifically in cancer stem cells. Another interesting approach is the use of sortase to label neighbour cells in the cancer microenvironment.

Overall the reviewer has the impression the work is quite superficial and the conclusions cannot be claimed by the results presented in the paper for the following reasons:

1. Cancer stem cells are a relatively small fraction when compared to the entire cancer cell population, therefore it is possible that the EV released tend to accumulate in macrophages because those are cells competent for specialized internalization and clearance of EV (e.g. PMID: 30745143). Second accumulation in macrophages does not mean any kind of signaling, it may just be that the EVs are degraded.

We thank the Reviewer for understanding and appreciating our work. We would like to point out that the novelty of our work is the identification of a specific macrophage subset (MHC-II– macrophages) that is mainly targeted by CSC-EVs (Fig.2). We observed a selective enrichment of these macrophage subset when tracking CSC-EVs, which argues against passive uptake, as the Reviewer seems to suggest. Moreover, these class-II negative macrophages were also found at increased frequency within the CSC niche (Fig.4), further suggesting an active process. This information is not trivial and cannot be inferred from the literature.

We are not claiming any signaling mechanism, which will be the focus of future work, including the role of CSC-EVs on maintaining MHC-II– immunosuppressive macrophage populations. We have amended the main text to clarify these points.

The sortase experiment is very interesting, however key controls are missing. For example, a thorough in vitro characterization of the system is needed: a. No clear description of the vectors used is provided (how is the labelling fluorescent protein released by the cells? How far can the protein diffuse?); b. The sortase's labelling efficiency is not characterized. c. Which proteins are targeted by sortase in the acceptor cells? There is any protein that can specifically be labelled by sortase on the cell surface of acceptor cells? This is not explained or validated. d. The authors claim that the labelling is provided by EVs harboring sortase on their surface, however also the plasma membrane of the cells may efficiently label cells. This should be explored and discussed. Which is the enzymatic sortase activity present on the EVs? How the authors can exclude that the red fluorescent protein is simply internalized by the neighbor cells? This should also be evaluated.

We thank the Reviewer for the interest in the SrtA-based approach, which we have thoroughly described and validated in Hamilton et al. Adv Biosys 2020 (ref. 50). We apologize if we did not reference that work properly. In that publication, we characterized SrtA labelling efficiency under various conditions and with different substrates, we mentioned which proteins can be targeted by SrtA on the surface of cells (that is, any protein with an N-terminal glycine, such as MHC-I, VE-Cadherin, CD19, integrins, …). We have clarified the above details in the new version of the manuscript.

We apologize for not including a schematic of the lentiviral vectors used, that we have now added (new suppl. Fig. S1). These schematics show that the red fluorescent protein is released from cells because it is fused to a signal sequence. In order to control for internalization of the red fluorescent protein by neighboring cells, we have used a control group in which CSC do not express SrtA while the bulk of tumor cells (including CSC) still secrete the red fluorescent protein. The values for SrtA activity are calculated by subtracting baseline internalization of red fluorescent protein by each individual immune subset. We have amended the Methods section to clarify this.

We are glad to hear that the Reviewer fully understood how the SrtA-based approach works. As this Reviewer mentions, it is not possible to discriminate between CSC and CSC-EVs since SrtA is present on both. This is a limitation of current EV technology in general. Although we were careful in wording our results and conclusions, we have revised the manuscript to take this into further consideration. The manuscript now claims that the SrtA approach unveils short-range interactions between CSC, CSC-EVs and immune cells due to their proximity.

Method section should be expanded, map of vectors provided and possibly deposited.

We apologize for not including a schematic of the lentiviral vectors used, that we have now added (new suppl. Fig. 1). We have expanded description of the Methods. We will promptly deposit the lentiviral transfer plasmids employed in this work with Addgene upon publication.

__Minors: __The paper should be expanded, and experiments better described.

We have expanded the paper and the description of the experiments, as requested.

CROSS-CONSULTATION COMMENTS I find the comments of Reviewer 1 important to be addressed. I might have under-estimated the amount of time necessary to revise the work. I still believe the material and method section is insufficient.

We thank the Reviewer for acknowledging that major revision of our work is very time-consuming. We hope to have addressed both Reviewer 1 and 2 comments.

Significance: The paper present technological innovation that can result of interest for the large audience of EV enthusiasts. The scientific advancement is limited since the conclusion: These results suggest that combination therapies targeting CSC, tumor macrophages and PD1 may synergize, is known and the work presented does not really support it since there is no evidence the EVs have any signaling role. Perhaps the authors should work more on tightening their result to a cell biology perspective of cancer niche interaction.

We thank the Reviewer for understanding the technological innovation. We will remove the statement on combination therapy and refocus on a cell biology perspective.

REVIEWER #3

In this paper, the authors used genetically engineered CSC-derived EVs to perform sortase-mediated in vivo proximity labeling and interrogate interactions of these vesicles with immune cells in the TME. The authors show that these EVs mediate intra-tumoral recruitment of immune cells, MHC class II(-) macrophages and PD1+ T cells, to the CSC niche and define EV-mediated special interactions of these immune cells within this niche. The manuscript is timely and novel, as it introduces a new experimental platform for identification, characterization and monitoring of CSC-derived EVs within the TME. Much has been recently learned about tumor cell-derived "tEVs", while almost nothing is known about CSC-derived tEVsCSC. Here, using genetic engineering, the authors have created specifically labeled fluorescent (GFP) tEVsCSC and studied interactions of these vesicles with immune cells in the TME. Two different HNSCC mouse models, MOC2 (carcinogenesis-dependent) and mEER (Ras dependent), were used. CSC populations were identified as cells with the brightest GFP fluorescence (~5%). These cells also expressed the known stem cell markers and formed oospheres in vitro. The authors then show that tEVcsc preferentially targeted MHC II (-) macrophages, which avidly uptake these EVs. tEVcsc also showed preferential tropism towards PD1+ T cells. Further, the authors demonstrate that location-dependent labeling indicates the presence and "clustering" of MHC II (-) macrophages and PD1+ T cells in the same niche within the TME. The generation of genetically modified labeled fluorescent tEVcsc and tEVs and in vitro as well as in vivo analyses of their interactions with immune cells in the TME were technically demanding. These studies were expertly performed, and the results are convincing. The data presentation is adequate, but the figure legends are sparce, and the text is densely narrated and somewhat difficult to read. Some more clarity in Results and more explicitly documented correlative data would clarify and enhance the message the authors convey.

We thank the Reviewer for fully understanding the novelty of our work. We agree that the description of results and figures can be improved. We have now clarified the narration of results and figure legends so they can be better understood.

The Discussion is rationally written, but the comments in Abstract and in conclusions about combination therapies and targeting CSC, tumor macrophages and PD1 to lower HNSCC recurrence are not appropriate. There is nothing in this manuscript about immunotherapy and these comments should be deleted.

We agree with the Reviewer and we have removed these statements from the text.

Overall, this is an interesting, timely and novel manuscript using genetically modified, fluorescently labeled EVs to explore their interactions with immune cells in the TME of HNSS. Technical and experimental approaches are complex, but appear to be well done, providing an experimental model for probing cellular interactions in the TME at a single-cell level. I recommend acceptance after modifications as suggested above

Significance: Significance is high, as it advances our understanding of the interactive role of CSC-derived EVs with macrophages and T cells in the tumor microenvironment.

We thank the Reviewer for appreciating the significance of our work.