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Referee #2

Evidence, reproducibility and clarity

Summary:

Voltage-gated proton channels are peculiar members of the voltage-gated ion channel family due to their absence of canonical pore. Instead, protons permeate through their voltage-sensing domain. The mechanisms of proton permeation in Hv1 channels are still unclear, with currently two competing hypotheses: (i) hopping through titrable residues within the protein; or (ii) via Grotthuss mechanism involving proton jumping through a continuous water wire. So far, these hypotheses were only tackled by computation. The authors therefore aimed to experimentally test the two hypotheses. To do so, the authors measured the transport rates of protons and water through wild-type and mutant D174A Hv1 reconstituted in lipid vesicles. Overall, the presented data are convincing and support their conclusion that proton conduction through the channel is not solely mediated by water transport. However, there are several aspects of the paper that I did not understand and would require clarification.

Major comments:

My major concern is about the relevance of using the D174A mutant. The authors explain at the beginning of the paper that Hv1-D174A is open at 0 mV, which allows measuring proton flux in systems in which voltage cannot be controlled. However, it seems from the proton flux experiments that wild-typet Hv1 can conduct protons perfectly well in the used experimental paradigm. So why test a mutant? It is actually not clear why wild-type Hv1 can conduct protons in the proton conduction assay. The authors should clearly state the trans-membrane potential created by the K+ gradient across the vesicle, as well as the pH inside and outside the vesicle, and related these conditions to their electrophysiology data to give us an idea of the open probability of wild-type Hv1 in the conditions used in the proton conduction assays. This is critical to be able to compare the relative rates of proton transport between the wild-type and the mutant. Similarly, the buffers and pH used for the water transport assay are not explicitly mentioned. Are they the same as for the proton transport assay or are the buffers inside and outside the vesicle symmetrical? Finally, in the introduction the authors base their assumptions about water transport on an X-ray structure of Hv1 in a closed conformation (3WKV). I do not think it is relevant to study permeation, which in theory should only happen in an open state. If the authors want to make assumptions about the number of hydrogen bonds in the pore and how many water molecules are in the pore (and I don't think they need to do it), they should rather base their assumptions on the computational models of Hv1 open state.

Minor comments:

1. Figure 6: the authors should precise that the model of proton conduction through Hv1 is just an assumption. The structural features of Hv1 open state are indeed unknown.
2. Page 9, lines 170-171 "Drastically prolonged tail current kinetics might reflect a decreased voltage-dependence of the deactivation in the D174 mutant". Or rather the prolonged kinetics reflect the stabilization of the open state by the mutation (as stated by the authors just after).
3. Supplementary figures are displayed in an odd fashion. Figure S3 should be placed before Figures S1 and S2.
4. In Figure 2, displaying the current trace corresponding to the 0 mV voltage step would improve readability of the figure, by showing that Hv1-D174A mutants conduct protons at 0 mV and not wt Hv1.
5. Figure 2 legend "Pronounced inward H+ currents activate negatively to the reversal potential (here -70 mV)". I think the authors mean "Here 0 mV", -70 mV is the threshold potential. Panel (c), I guess the EH vs Vrev plot is for D174A mutants but it is not mentioned in the legend
6. Page 4, line 89: the fact that D174A conducts protons at a lower rate is, at this point, based on a lot on assumption. I would just correct the last sentence by saying "Thus, D174A, while opening with less depolarization, seems to conduct protons at a lower rate"
7. Page 6, line 107. The word "therefore" is not necessary
8. Page 7, line 128: "of" in "measures of transport" is missing
9. Page 12, lines 261-262: "Figure M" ??

Referees cross-commenting

I agree with the two other reviewer's comments. I think our reviews more or less raise the same weaknesses in the study.

Significance

This paper addresses a single question with a clearly defined experimental paradigm. Once the issues addressed, the paper should bring important significance to the field of voltage-gated ion channels since the nature of proton conduction in Hv1 was not known. It could help explain ion conduction in some channelopathies involving ion conduction through the voltage-sensing domain.

The audience is mainly the voltage-gated ion channel community, as well as the community of membrane permeation mechanisms.

My field of expertise is in ion channel structure-function and pharmacology. I have little expertise in the described proton and water flow assays. Therefore I do not have sufficient expertise to evaluate the detailed experimental protocol that led to the measurements.

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Referee #1

Evidence, reproducibility and clarity

1. The authors state that: "the conductance density mediated by the expression of the mutant was 2.5 times smaller than the wild type, although we transfected the same amount of plasmid DNA (Fig. 2E). Assuming that protein expression is independent of the mutation, the observation suggested that the unitary proton flux ratio RC of wild type to mutant channel was equal to 2.5" (lines 82-85).

Macroscopic conductance (G) depends on channel number (N), microscopic or unitary conductance (), and open probability (PO) by G=NPO. The authors assume that the level of WT and D174A mutant protein expression on plasma membrane, which determines N, are equal; however, this critical assumption does not appear to have been tested. The fact that conductance density (nS/pF) is plotted in Fig. 2E does not alter this caveat because this procedure normalizes the data only for cell surface area (i.e., size).

The authors' conclude that "The conductance density relationship (Fig. 2E) compares the maximal conduction of both constructs; this is the fully open channel (open probability ≈ 1)"(lines 87-88). However, neither raw currents nor G-V data are shown. Typically, currents measured at large, near-saturating PO are used to compare the relative conductances of WT and mutant ion channels. The currents shown in Fig. 2A and 2B exhibit prominent 'droop' at even modest depolarizing potentials (+10 mV for D174A and +30 mV for WT), indicating that the proton gradient has been substantially perturbed by the flow of ge depolarizing voltages needed to drive channels to near-maximal PO. Furthermore, there is no evidence that maximal PO itself is also not different in WT and D174A channels. Indeed, maximal PO for native Hv1 channels measured using variance analysis is reported by significantly smaller than 1.0, and assuming that PO = 1.0 for either WT or D174A is therefore not well supported. Maximal could be altered by the D174A mutation, which has a clear and strong effect on channel gating evidenced by the large (-70 mV) negative shift in threshold potential reported both here and previously in the literature. Effects of mutations on maximal PO due to altered gating behavior could be separate and distinct from any change in plasma membrane channel number (N). Lastly, because D174A channels have a much higher PO than WT at 0 mV, the mutant will necessarily conduct inward proton currents at the physiological resting membrane potential (RMP) in tsa-201 cells (perhaps -30 mV?). Inwardly directed proton currents will therefore cause intracellular acidification under resting conditions. The constitutive acid load in cells expressing D174A, but not WT, is likely to have a variety of physiological consequences, including decreased protein expression or plasma membrane targeting of D174A. There is evidence that another-constitutively open Hv1 mutant (R205H) also generates smaller currents macroscopic conductance than WT, and this phenomenon is likely to result from decreased cell surface expression. To conclude that the microscopic conductances of WT and D174A are unequal, the authors must demonstrate that N is not different The authors' conclusion that D174A "conducts protons at a lower rate" (line 89) is therefore not well supported by the experimental data. 2. The authors indirectly measure apparent proton flux rates (D) in LUVs containing WT and D174A mutant Hv1 channels using a fluorescence-based approach, and conclude that D is 2.4 times smaller for D174A than WT. However, the method for estimating D is not performed under voltage clamp, and the driving force for proton current is neither known nor measured. The authors state that "Transmembrane voltage constituted the driving force for proton uptake into LUVs (Figure M). It resulted from facilitated K+ efflux out of the vesicles (30)", (lines 261-262), but this voltage is unknown and not likely to equal the Nernst equilibrium potential for K+ once Hv1 channels begin to open.

Once Hv1 channels begin to open, intra-lumenal pH (pHi) will necessarily occur during the experiment. Such changes are likely exacerbated by a) the low proton buffering capacity of the system (5 mM HEPES) and b) the absence of any counter-charge pathway to balance the effect of proton charge movement on the membrane potential. Given the small volume of LUVs, even a relatively modest difference in either membrane potential or pHi could substantially alter the driving force for proton movement. Together, these factors are highly likely to result in a rapid and potentially large change in the driving force for proton flux.

Driving force changes may also be different for WT and D174A because their relative PO may be different under the experimental conditions used here. Because D174A activates at much more negative voltages, it is likely to open more quickly and to a higher PO than WT at early times after depolarization is initiated by addition of valinomycin (Fig. 3A). This fact will likely result in a larger initial inward current being carried by D174A than WT channels. The result would be a more rapid acidification of LUVs by D174A.

The experimental data in Fig. 3A are consistent with the expectation that the proton gradient and driving force more rapidly approach equilibrium for D174A than WT channels: the apparent rate of AMCA fluorescence change is slower in D174A. Although the authors correctly interpret the experimental data to mean that the apparent D is slower for D174A, they do not rule out the artifactual explanation for the measured differences. Indeed, the observation in Fig. 3A that AMCA fluorescence change eventually reaches a plateau and is not affected by CCCP means that the proton gradient has become exhausted during the experiment, and directly demonstrates that the proton driving force is uncontrolled under the current experimental conditions.

In contrast to the authors' statement that "Our experiments with the purified and reconstituted channels corroborated the conclusion (Fig. 3A)", (lines 92-93) it is not clear that unitary proton flux rates/unitary conductances are actually different in WT and D174A. 3. The presumed differences in unitary conductances (i.e., 'transport rate') between WT and D174A are used to estimate Arrhenius activation energies (Ea): ("The difference in measures transport rates allows a rough estimation of the Arrhenius 128 activation energy Ea for HV1-mediated proton flow. It amounts to 40 kJ/mol for the wild type and 23 kJ for the mutant. Thus, Ea exceeds the corresponding 15 kJ/mol barrier measured for gramicidin A (32, 33)", (lines 128-130).

The method for determining Ea in the current work is not well-described. In Ref. 32, the authors estimate Arrhenius activation energy (Ea = 20 kJ/mol) for gramicidin D (not gramicidin A) from the slope of a line fit to measurements of currents at various temperatures. Here, the authors measure AMCA fluorescence decay rates at 4{degree sign}C and 23{degree sign}C and observe a similar temperature-dependent difference in WT and D174A (Fig. S2). Given that the data indicate that WT and D174A are similarly temperature-dependent, it is unclear how the authors arrive at different Ea values. The authors' conclusion that "The increment in Ea suggests that the transport mechanism may be different from a pure Grotthuss type, where the proton uses an uninterrupted water wire to cross the membrane", (lines 131-133) therefore does not appear to be well-supported. 4. The authors report no difference in water permeability in WT vs. D174A (Fig. 5 and S1) and interpret the results to mean that proton currents are not associated with measurable bulk water flow. A similar conclusion was reached for native Hv1 channels using deuterium substitution (DeCoursey & Cherny, 1997). However, the absence of bulk water flow does not itself rule out the possibility that 'trapped' waters within the Hv1 pore do not themselves carry the measured proton current. If intra-pore water molecules are tethered by hydrogen bonds with protein atoms, they may not move when Hv1 channels open. Proton transfer through a hydrogen-bonded network of waters requires only that the electronic structure of the network be rearranged during proton transfer; water is not required. As in the previous study (DeCoursey & Cherny, 1997), the lack of water flux reported here demonstrates seems to reinforce the notion that H+ moves separately from its waters of hydration (i.e., hydronium, H3O+, is not the permeant species) and does not necessarily imply information about the mechanism of proton transfer (i.e., side chain ionization vs. Grotthuss-type transfer in a water-wire).

The authors state that: 1) "every H-bond donating or receiving pore-lining residue would have contributed an increment ΔΔ𝐺‡ of 0.1 kcal/mol to the Gibbs free energy of activation Δ𝐺‡ (25)" (lines 145-147), and 2) calculating NH from this Δ𝐺‡ allows estimation of the channel's unitary water permeability (Eqn. 2). Although hydrogen bonding patterns will undoubtedly alter the free energy for channel activation, this is not the same free energy change as that for proton transfer. Hv1 gating involves conformational changes that are both voltage and pH-dependent, and the D174A mutation is known to alter the voltage dependence of gating (Fig. 2 and previous studies). The effect of D174A on Hv1 unitary conductance, however, is speculated but not unambiguous (see above). In the absence of definitive experimental data showing differences in the unitary conductance of WT vs. D174A, the authors' assumption that water permeability would be strongly temperature-dependent (lines 154-160) seems premature and their ensuing conclusion tenuous: "pore residues interrupt the HV1 spanning water wire, trapping the water molecules inside the HV1 channel. In contrast to water, protons cross the pore by hopping from one acidic residue to another through one or more bridging water molecules (Fig. 6)" (lines 161-164).

Furthermore, the authors calculate the number of hydrogen bonds (NH) that pore waters could form with pore-lining residues based on an X-ray structure of a chimeric proton channel protein (pdb: 3WKV) that is: a) manifests discontinuous transmembrane water density and is known to represent a non-conductive conformation, b) contains residues from Ci-VSP in the critical S2-S3 linker that form part of the proton transfer pathway, and c) exhibits structural features (i.e., highly conserved ionizable residues such as D185 and R205, which like D174 are reported to dramatically alter Hv1 gating, are packed into a solvent-free crevice) that are inconsistent with physiological function. Given that all Hv1 ionizable mutant combinations tested so far (the sole exception of D112V - other non-ionizable substitutions at D112 are tolerated) remain functional (Musset, Smith et al., 2011, Ramsey, Mokrab et al., 2010), the identities of water-interacting residues speculative. Interpreting differences in the calculated NH based on pdb: 3WKV therefore seems unlikely to reveal fundamentally important insights into Hv1 function. The author's conclusion that "The observation rules out the formation of an uninterrupted water chain spanning the open channel from the aqueous solution at one side of the membrane to the other. NH would have governed water mobility if such a water wire had formed (24)", (lines 143-145) therefore does not appear to be strongly supported.

References

Bennett AL, Ramsey IS (2017a) CrossTalk opposing view: proton transfer in Hv1 utilizes a water wire, and does not require transient protonation of a conserved aspartate in the S1 transmembrane helix. J Physiol

Bennett AL, Ramsey IS (2017b) Rebuttal from Ashley L. Bennett and Ian Scott Ramsey. J Physiol

De La Rosa V, Bennett AL, Ramsey IS (2018) Coupling between an electrostatic network and the Zn(2+) binding site modulates Hv1 activation. J Gen Physiol

De La Rosa V, Ramsey IS (2018) Gating Currents in the Hv1 Proton Channel. Biophys J 114: 2844-2854

DeCoursey TE (2017) CrossTalk proposal: Proton permeation through HV 1 requires transient protonation of a conserved aspartate in the S1 transmembrane helix. J Physiol 595: 6793-6795

DeCoursey TE, Cherny VV (1997) Deuterium isotope effects on permeation and gating of proton channels in rat alveolar epithelium. J Gen Physiol 109: 415-34

Musset B, Smith SM, Rajan S, Morgan D, Cherny VV, Decoursey TE (2011) Aspartate 112 is the selectivity filter of the human voltage-gated proton channel. Nature 480: 273-7

Ramsey IS, Mokrab Y, Carvacho I, Sands ZA, Sansom MS, Clapham DE (2010) An aqueous H+ permeation pathway in the voltage-gated proton channel Hv1. Nat Struct Mol Biol 17: 869-75

Ramsey IS, Moran MM, Chong JA, Clapham DE (2006) A voltage-gated proton-selective channel lacking the pore domain. Nature 440: 1213-6

Randolph AL, Mokrab Y, Bennett AL, Sansom MS, Ramsey IS (2016) Proton currents constrain structural models of voltage sensor activation. Elife 5: e18017

Significance

Here the authors attempt to ascertain whether water molecules may mediate proton transfer in the voltage-gated proton channel Hv1 using a combination of whole-cell voltage clamp electrophysiology, protein purification, reconstitution, and pH-dependent AMCA fluorescence measurement and estimates of water permeability, and hydrogen bond calculations based on an X-ray structure of a chimeric Hv1 proton channel model protein. The authors address an important question that is fundamental to the exquisitely proton-selective Hv1 channel and which may be applicable to other proton transporting proteins.

Although there is high potential for significance to a wide range of experimenters studying biologically fundamental mechanisms of proton transport, the experimental data fail to strongly support most of the authors main conclusions, and it is unclear whether the work represents a technial advance for the field. Previous work in the literature has described two main hypotheses for the proton transport mechanism in Hv1:

• A) an intra-protein transmembrane water wire that allows permeating H+ to move along a chain of hydrogen-bonded water molecules and does not require explicit ionization of any particular amino acid side chain (Bennett & Ramsey, 2017a, Bennett & Ramsey, 2017b, Ramsey et al., 2010), and
• B) Explicit ionization of a conserved side chain in the S1 helix (D112 in human Hv1) is required for proton transfer in Hv1 channels (DeCoursey, 2017, Musset et al., 2011). The Reviewer is an expert in the field, having originally identified and functionally characterized Hv1 channels in 2006 (Ramsey, Moran et al., 2006), contributed to the identification of key side chains and structural determinants of Hv1 function (De La Rosa, Bennett et al., 2018, Ramsey et al., 2010, Randolph, Mokrab et al., 2016), measured gating currents in Hv1 (De La Rosa & Ramsey, 2018), and authored the hypothesis that Hv1 utilizes a water-wire type mechanism for proton transfer (Ramsey et al., 2010).

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Reply to the reviewers

August 17, 2022

RE: Review Commons Refereed Preprint #RC-2022-01442

Dear Editor of the EMBO Journal,

Please find our updated manuscript and response to the reviewers’ comments. We appreciate the effort that the reviewers have put into the evaluation of our manuscript.

We are happy with the potential importance the reviewers realise in the study:

Reviewer 1: The finding that ubiquitination occurs inside mitochondria would be an important conceptual advance, which would open new perspectives both for ubiquitination and mitochondrial biology

Reviewer 2: This work would represent a significant/exceptional discovery if supported by compelling data.

Reviewer 3: the results are interesting and very important, as mentioned in the major comments section…

With regard to the major comments raised by the reviewers, you will find below our specific response point by point with explanations and suggested novel experiments (highlighted in yellow). In summary we suggest the following actions to fully support our model:

• We will perform a-complementation with ubiquitin (lacking the GG motif) fused at its C-terminus to the short fragment of b-galactosidase (a). Blue colonies with ωm will indicate import.
• As shown in Figure S2, now added to the manuscript, we show detection of ubiquitinated proteins and mono ubiquitin in extracts of mitochondria pre-treated with trypsin.
• A bio-archives address of our other manuscript will be provided.
• The use of a-complementation for protein localization was developed by us 15 years ago and since then has been used by us and other groups verifying its use as a screening tool. One point is clear, ωm or ωc do not leak into other subcellular compartments. Nevertheless, in the research of specific genes validation is important. Yes!!! ωm and ωc are exclusively located in mitochondria or the cytosol respectively.
• We will highly purify mitochondria on gradients and treat them with protease.
• We cannot be sure that we will be able to detect a protein with ubiquitin modifying activity which functions solely on certain proteins in mitochondria, so publication cannot rely on this.
• Repeat mass spectrometry with careful editing will be undertaken as suggested by the reviewer.
• We will attempt to perform protease protection assays in the presence of specific detergents.

Before tackling the very tough revision, we would like to know if EMBO Journal would positively consider acceptance of our manuscript based on the review and planned revision.

Prof. Ophry Pines Microbiology & Molecular Genetics Hebrew University of Jerusalem Jerusalem 91220 Israel

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

Summary:

In this manuscript, Zhang et al. investigate whether ubiquitination occurs inside mitochondria of the budding yeast S. cerevisiae. They first observe thanks to a sensitive complementation assay that several components of the yeast ubiquitination (and deubiquitination) machinery can localize inside mitochondria. To be able to specifically probe ubiquitin conjugates assembled inside mitochondria they fused HA-tagged ubiquitin to a mitochondrial targeting sequence. Using this construct, they demonstrate that ubiquitin conjugates can be assembled in mitochondria. A series of elegant experiments demonstrates that the pattern of ubiquitin conjugates depends on the mitochondrial localization and the activity of the ubiquitin conjugating enzyme Rad6. Altogether, these results convincingly demonstrate that ubiquitination can occur inside yeast mitochondria when ubiquitin is intentionally targeted inside this organelle. It however remains unclear whether mitochondrial ubiquitination occurs in endogenous conditions (without targeting ubiquitin into this compartment) and whether it affects mitochondrial functions.

Response: Regarding the question whether mitochondrial ubiquitination occurs in endogenous conditions, we feel that this is obvious based on our results. We detect numerous ubiquitination related enzymes (E1, E2, E3, DUB) eclipsed in mitochondria but none of the proteasome subunits. As pointed out by the reviewer “these results convincingly demonstrate that ubiquitination can occur inside yeast mitochondria”. With that said, additional data will be incorporated into the manuscript as suggested by the reviewer and can be seen below.

Major comments:

1) The materials and methods section is lacking important information (western blot protocol, details of antibodies, strains, plasmids...). It is thus difficult to evaluate how several experiments were performed and how their design (e.g. the promoters chosen to express tagged proteins) could impact the interpretation of the results. This is a major issue that needs to be corrected. The main text should also explicitly indicate whether tagged proteins used in the alpha-complementation assay are overexpressed or not.

Response: The materials and methods section will be updated accordingly.

2) Despite the previous comment, the data presented in the manuscript convincingly demonstrate that multiple components of the ubiquitination machinery can localize within mitochondria and that ubiquitin conjugates can be assembled in mitochondria when ubiquitin is modified to be intentionally targeted into this compartment. However, little data is shown to support the hypothesis that ubiquitin conjugates can be assembled in mitochondria when ubiquitin is not fused to a mitochondrial targeting sequence. Thus, in my opinion, the evidences presented in the current manuscript are not sufficient to conclude that ubiquitin conjugates are assembled in mitochondria in endogenous conditions (as this is done implicitly). Additional evidences are needed to draw this conclusion (see some experimental suggestions hereafter). Without further evidences, the speculative aspects of the claim that "ubiquitination occurs in the mitochondrial matrix" should be discussed explicitly.

Response: See the discussion above why we are confident that ubiquitination occurs in mitochondria. Our major problem with ubiquitin and the ubiquitination enzymes is that they are eclipsed in mitochondria. We propose as suggested by the reviewer (item 4 of his review) to perform a-complementation with ubiquitin fused at its C-terminus to the short fragment of b-galactosidase (a). Blue colonies with ωm will indicate import.

3) The authors used a mass spectrometry approach to identify mitochondrial ubiquitination substrates. However, they have not yet succeeded in identifying a substrate whose modification is specifically regulated by a given component of the mitochondrial ubiquitination machinery. They have also not identified a phenotype or process impacted by mitochondrial ubiquitination. Thus, at this stage, the biological consequences of mitochondrial ubiquitination remain elusive.

__Response: __We have not identified a substrate whose modification is dependent on a given component of the mitochondrial ubiquitination machinery, even though we have tried. Again, the problem is low levels of these proteins eclipsed in mitochondria. Even when we do find a protein that is ubiquitinated (e.g. Aco1) its ubiquitination is not exclusively dependent on Rad6. Thus, different ubiquitin enzymes may have the same substrates.

4) The authors have not directly investigated whether ubiquitin itself (without a mitochondrial targeting sequence) localizes in mitochondria. I encourage them to address this question since it would provide an important piece of evidence suggesting that mitochondrial ubiquitination can occur in endogenous conditions. This could be done using the alpha-complementation assay and the results could be presented within Figure 1. Ideally this experiment should be performed without overexpressing ubiquitin. Note that if the authors decide to use a C-terminally tagged form of ubiquitin for this experiment, the GG motif of ubiquitin should be mutated to avoid cleavage of the alpha tag by cellular DUBs. This form of ubiquitin will not be conjugatable, but this is not an issue for this experiment since its aim is to determine whether ubiquitin can be targeted to mitochondria, not to probe conjugates.

Response: We will perform experiments as suggested by the reviewer including ubiquitin fused at its C-terminus to the short fragment of b-galactosidase (a), see item 2. We have previously made a PreSu9-Ubi lacking a GG motif but now will look at a different combination of this and other constructs.

5) In the top panels of Figure 2 and S1, free ubiquitin is well detectable in the total and cytosolic fractions. It is however not clear to me whether it is also detectable in the concentrated mitochondrial fraction. If yes and if it would be resistant to trypsin digestion, it would provide additional evidence that endogenous ubiquitin can be targeted to the mitochondrial matrix (see previous comment).

Response: See Item 6.

6) The data shown in the top panel of Figure 2 and S1 also suggest that free ubiquitin is less concentrated in mitochondria than in the cytosol (since it is more difficult to detect in the concentrated mitochondrial fraction than in the cytosolic fraction, see previous comment). It is thus possible that the use of preSu9-HA-Ubi (or preFum1-HA-Ubi) lead to an artificially high intra-mitochondrial concentration of free ubiquitin. As the concentration of free ubiquitin is known to impact ubiquitination processes, I encourage the authors to compare the relative levels of free ubiquitin present in the mitochondrial fraction prepared from WT and preSu9-HA-Ubi (or preFum1-HA-Ubi) expressing cells. If free ubiquitin is detectable in mitochondrial fractions and resistant to trypsin (see previous comment), this could be done by repeating the experiment shown in Figure 3B and probing the blot with an antibody that recognizes free ubiquitin.

Response to 5 and 6: Detection of ubiquitin in mitochondria is extremely difficult even when mitochondria are 15-fold concentrated versus the cytosol and when HA-Ubi is overexpressed. Thus, ubiquitin is eclipsed in mitochondria. Nevertheless, as shown in the Figure below which was not part of the submitted manuscript yet was performed in parallel to experiments done early on, shows detection of very weak bands of free ubiquitin in extracts of mitochondria pre-treated with trypsin.

Endogenous ubiquitination pattern in mitochondria of _Δrad6 _cells is restored to normal by Rad6-α. __WT or Δrad6 cells containing a Rad6-α construct or an empty plasmid were subjected to subcellular fractionation. Mitochondrial fractions with or without trypsin treatment, were probed for ubiquitin by WB. Aco1 is a matrix mitochondrial protein, and Tom70 is a mitochondrial outer membrane protein (MOM) facing the cytosol.

7) I strongly encourage the authors to provide more data indicating that "ubiquitination occurs in mitochondria" by performing experiments that do not rely on the use of the preSu9-HA-Ubi or other forms of ubiquitin that are intentionally targeted to mitochondria. For instance, they could analyse the pattern of HA-Ubi conjugates of trypsin digested mitochondrial fractions prepared from wt, rad6-delta, and rad6-delta complemented with preSu9-Rad6-alpha-SL17. Note that if trypsin digested mitochondrial fractions are too contaminated by ubiquitinated proteins present outside mitochondria to perform this experiment, the authors may use the unspecific DUB Usp2 as an alternative protease to strip ubiquitinated proteins from the mitochondria periphery.

Response: Concentrated mitochondrial extracts from WT and Δrad6 cells untreated or treated with trypsin were probed with anti-ubiquitin antibodies (Figure above). A very weak band corresponding to free ubiquitin can be detected in extracts of mitochondria treated with trypsin but these are very weak and are on the limit of detection.

Minor comments:

1) Overall, the manuscript is well organized and easy to follow. The text is clearly written; the figures are well annotated.

2) The authors should provide full images of all the blots with anti-ubiquitin and anti-HA antibodies so that one can see the bands corresponding to free ubiquitin (or free HA-Ubi). For instance, in Figure 3B, it is not possible to see the presence (or absence) of the band corresponding to free HA-Ubi because the very bottom of the image is cut.

3) The authors should indicate whether the MTS of Su9 (and Fum1) are expected to be cleaved after import of preSu9-HA-Ubi (and preFum1-HA-Ubi) in mitochondria. They should also label on the corresponding immunoblots the presence (or absence) of the band corresponding to the free preSu9-HA-Ubi (and preFum1-HA-Ubi) (or HA-Ubi if the MTS is expected to be cleaved from these constructs).

4) In Figure 3B, the ubiquitin conjugates produced with preSu9-HA-Ubi and preFum1-HA-Ubi have different migration patterns. I think this should be explicitly mentioned and discussed. Could it be due to the presence of lysine residues in the Su9 or Fum1 MTS that could lead to the assembly of artificial ubiquitin chains?

5) The authors indicate that "endogenous Rad6 [...] is expressed at very low levels and can hardly be detected in the mitochondrial fraction by WB (Figure S5)". I did not manage to observe the band corresponding to endogenous Rad6 in the mitochondrial fraction in the pdf. The authors should provide a more contrasted or better quality image.

CROSS-CONSULTATION COMMENTS I agree with reviewer 2 that proper validation of the complementation assay is crucial for this manuscript. I was myself wondering whether it uses endogenously tagged proteins or whether it is based on an overexpression system. I imagine this information will be detailed in the manuscript in preparation mentioned by the authors. I am therefore wondering whether it would be possible to ask the authors to provide the draft of this manuscript (or at least the validation part).

Response: A bio-archives address of our other manuscript will be provided upon resubmission. See other issues referred to the response Reviewer 2.

I agree with most comments of reviewer 3. Regarding the hypothesis that preSu9-HA-Ubi could form aggregates on the cytosolic surface of the mitochondria, I think that the results presented on Figure 7B rather argue against it (since they indicate that Rad6 localized inside mitochondria can restore the pattern of ubiquitin conjugates). That's why (in my opinion) the major question the author now need to adress is whether intra-mitochondrial ubiquitination occurs in endogenous conditions (ie without forcing ubiquitin into this compartment and without E2 or E3 overexpression).

Response: See response to the other reviewers

Reviewer #1 (Significance (Required)):

The finding that ubiquitination occurs inside mitochondria would be an important conceptual advance, which would open new perspectives both for ubiquitination and mitochondrial biology research. However, the significance of the current manuscript is limited because the presented evidences heavily rely on the use of artificial conditions (ubiquitin tagged with a mitochondrial-targeting sequence) that may trigger irrelevant ubiquitination events. The significance would be much higher if the authors would provide further evidences indicating that intra-mitochondrial ubiquitination occurs in endogenous conditions and/or if they had identified a mitochondrial process specifically impacted by mitochondrial ubiquitination.

Expertise of the reviewer: Ubiquitination, Yeast biology, protein-protein interactions. No specific expertise in mitochondrial biology

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

In the manuscript by Yu et al., the authors test the concept that certain proteins are unevenly distributed within distinct cell compartments. Due to this localization discrepancy, protein detection in some subcellular compartments can be "eclipsed" by a predominant subset of specific protein localizing in another cell compartment their actual distribution. Therefore, tiny amounts of physiologically relevant proteins could be biologically relevant. Still, their function in some locations can be overlooked (or eclipsed) because of the high expression level of the same protein in another subcellular compartment(s). Although, this concept is not particularly novel. For example, it is already known that many different proteins can localize to distinct cellular locations (e.g., permanent mitochondrial and peroxisomal localization of many proteins or transient localization of particular proteins to separate cell compartments). The authors apply a yeast system and an α-complementation assay to test further the role of such eclipsed proteins in mitochondrial biology. Specifically, they focus on the ubiquitin (Ub, or as abbreviated incorrectly in this manuscript; Ubi) conjugation pathway, components of which have never been convincingly shown to localize inside the mitochondria. This work proposes that certain ubiquitination events can occur inside yeast mitochondria. This work would represent a significant/exceptional discovery if supported by compelling data. However, the major problem with this work is that the conclusions are based on the ectopic expression of distinct proteins. This approach is not failproof in precise protein expression/delivery to the specific subcellular locations and is likely to result in a non-specific localization. Thus, the problem of eclipsed proteins is addressed by the methodology that may lead to the artificial generation of eclipsed overexpressed proteins. A more effective approach would be if the authors found a way to study this issue with endogenous proteins. The need for overexpression of mitochondria-targeted ubiquitin makes it challenging to reconcile the physiological role of these fundings. In addition, some critical technical issues and omissions further reduce the potential impact of this work (see Specific comments below). For example, strong evidence of mitochondria fraction purity and additional evidence that all the essential constructs used in this work are not misdirected to a different compartment are needed.

Response: “Although, this concept is not particularly novel” is a very disappointing remark by the reviewer!! While dual targeting of proteins has been known for many, many years, how widespread the phenomenon was unknown and thought to be negligible. We are leaders for the last 30 years in the field of dual targeting and distribution and in particular distribution of single translation products. We coined the terms “echoforms” and “eclipsed distribution” and developed methods to detect and screen for dual targeting. The concept of eclipsed distribution and in particular eclipsed targeting to mitochondria is very new, and is leading to a novel perception of the mitochondrial proteome (see MS submission). While the reviewer appears to be an expert on ubiquitination, we are experts on dual targeting.

• Ub was abbreviated incorrectly in this manuscript, Ubi. __Response: __This will be corrected.

Other comments will be referred to in the response to Specific comments.

Specific comments 1. The authors should demonstrate beyond doubt that the ω components of their assay (ω-C, which supposedly stays in the cytosol-ONLY and the ω-M component, which seemingly remains in the mitochondria-ONLY) are in the compartment that the authors claim. These two proteins are transfected into yeast cells and overexpressed. Therefore it is possible that they leak to other, not intended, subcellular compartments. The authors assume that ω-M and ω-C are exclusively located either in the mitochondria or the cytosol. However, this should be shown as validation of the assay. The indicated reference from 2005 (Ref.13) and others are irrelevant since assays have variations and are often researcher/lab dependent. This validation is very important since a misallocation of the overexpressed ω-M or ω-C, leaking into other subcellular compartments, may cause misdetection of the α-constructs.

Response: The use of a-complementation for protein localization was developed by us 15 years ago and since then has been used by us and other groups verifying its use as a screening tool. One point is clear, ωm or ωc do not leak into other subcellular compartments. Nevertheless, in the research of specific genes validation is important. Yes!!! ωm and ωc are exclusively located in mitochondria or the cytosol respectively.

It is not surprising that Ub conjugates are detected in mitochondrial fractions. It could be due to ubiquitination of the OMM (coming from the cytosol) or perhaps since the subcellular fractions were not pure mitochondria free from contamination (the likely culprit could be the ER). The mitochondrial fractions in this work were obtained by 10,000 g separation between cytosolic and mitochondrial crude fractions. Indeed, these 10,000 g crude fractions are highly impure with membranes from other compartments (i.e., microsomes, lysosomes, and so on). Therefore, more sophisticated purification methods should be used. In addition, the authors should also test these fractions for non-mitochondrial proteins from other membrane organelles.

Response: We agree with the reviewer and therefore will take the following approaches:

1. i) We will treat isolated mitochondria with protease in order to remove adhering proteins and digest OMM proteins…… see attached figure.
2. ii) We will highly purify mitochondria on gradients and this will be straight forward since we are now employing such methods in other projects in the lab. iii) Matrix protein enrichment (by mass spec) is associated with IP for preSu9-HA-Ub conjugates which is three-fold higher than for HA-Ub. In any case the fact that we identify conjugates of proteins not known to be mitochondrial, strongly supports our thesis.

Figure 2. Coomassie blue staining does not show any signal in the "M" fraction. It can be interpreted that the authors do not get any mitochondria there, and therefore the lack of Ub signal is due to the absence of the protein in the samples. Using the same amount of protein from each fraction would probably reduce the necessity of 15x enrichment.

Response: The Coomassie blue staining does show a signal in the "M" fraction which is weak yet when a 15x enrichment is run, the protein level by Coomassie blue staining is similar to the cytosolic fraction.

Figure 3. It is puzzling why the HA-UBQ presence is so strong in the crude mitochondrial fraction, but the preSu9-HA-Ub signal (mito-matrix) is comparatively weak. These data suggest that the crude mito-fraction could be highly contaminated with OTHER membranes. On the other hand, the preSu9-HA-UBQ signal is no more than 1-5% of the total mitochondrial signal. The high enrichment of the HA-Ubi in both cytosols and the mitochondria could indicate the OMM ubiquitination or (again) contamination by other compartments. The constructs with MTS are detected in the mitochondria. However, the localization of tagged MTS-Ubi in a non-targeted compartment (e.g., cytosol) should be excluded by additional exposure times. Because the manuscript talks about eclipsed proteins, this is important.

Response: The HA-Ub is strong in the mitochondrial fraction, in the absence of trypsin, but is very weak in the presence of the protease indicating that most of the ubiquitinated proteins are externally attached to mitochondria. In contrast, PreSu9-HA-Ub is imported into the mitochondrial matrix and is protected from trypsin. This manuscript refers to “eclipsed in mitochondria” (not the cytosol) and this is true for ubiquitination enzymes as well as for ubiquitin.

Figure 3C-E. These data indeed suggest that the Ub-conjugates could be formed inside the mitochondria. However, the above-discussed possibility that other than mitochondria compartments co-sediment in the 10,000g fractions makes the data interpretation highly challenging.

__Response: __We will highly purify mitochondria on gradients and this will be straight forward since we are now employing such methods in other projects in the lab.

Figure 4. Unsurprisingly, mitochondrial targeting of Ub leads to detecting some co-immunoprecipitating mitochondrial proteins. However, these data do not support the notion that Ub conjugation machinery acts inside the mitochondria and that the target proteins are indeed conjugated with Ub (the interaction with Ub is not equal to being conjugated). At the minimum, the authors should provide a validation that some of the detected mitochondrial matrix proteins are indeed ubiquitinated. To this end, purified mitochondria could be used for the candidate protein IP under denaturing conditions and then blotted for the candidate protein and Ub.

__Response: __As shown in Table S2 and figure S7, forms of Ilv5, a mitochondrial protein, are ubiquitinated in WT and Drad6 cells. These modified forms of Ilv5 can be eluted from mitochondrial extracts of WT and Drad6 cells. However, the ubiquitination of ilv5 is not dependent or effected by the Drad6 mutation. We cannot be sure that we will be able to detect a protein with ubiquitin modifying activity which functions solely on certain proteins in mitochondria.

Figure 5. The knock-out of the E2 Rad6 causes a change in the mitochondria ubiquitination pattern. This is an interesting observation, but again it does not prove that the change in the mitochondrial ubiquitination is due to the activity of Rad6 inside of the mitochondria, as opposed to ubiquitination of the OMM proteins or contaminating fractions. One also wonders why overexpression of mitochondria-targeted Ub would be necessary to detect the ubiquitination if this process was physiologically relevant, especially given that detecting endogenous Ub is not challenging. Furthermore, the apparent increase in ubiquitination in E2 mutant cells (Fig. 5) should also be addressed in more detail. Finally, data from one WB is shown, and quantification of several independent experiments should also be provided.

__Response: __We show in the MS that RAD6 is exclusively targeted to mitochondria (Su9MTS) while unimported molecules are degraded (SL17; degron). This hybrid Rad6 can restore the WT ubiquitin pattern, while a rad6 active site mutant cannot.

Figure 6. Can the authors provide Western blot data showing the expression of Rad6? Furthermore, quantifying these rescue experiments is necessary to make this conclusion more solid.

Response: Even though we did not succeed in making good Rad6 antisera, we can clearly detect Rad6-a fusion proteins (Figure 7B).

Figure 7. The authors found that preSu9-Rad6-α have problems being imported into the mitochondria matrix; therefore, they rebuild it as a preSu9-Rad6-α-SL17 protein. SL17 is a degron that targets the cytosolic protein (not imported into the mitochondria) to the proteasome and degraded (Figs. 7A-B-C). These issues could be a red flag for the rest of the manuscript, suggesting that other constructs (that were not critically evaluated for their localization in this work) could leak to different cellular compartments.

Response: The wording used by the reviewer is particularly disturbing since current understanding in cell biology of eukaryotic cells does not accept “leaking” of proteins to different cellular compartments. One wouldn’t want DNAses, RNAses, Proteases etc leaking from one compartment to another. The localization of proteins to different cellular compartments involves very precise signals on the proteins, and specific cellular components, such as translocases, are required to target proteins to their exact destination. This is true for Rad6; it contains an MTS like sequence which when removed blocks import of the protein into mitochondria. Rad6 according to our analysis is an eclipsed dual targeted protein, so it no surprise that it is in two compartments and the trick with the SL17 degron solves the problem.

The manuscript needs to be carefully edited, some references are in the not correct format, and there are issues with figure labels.

Response: Careful editing will be undertaken as suggested by the reviewer.

CROSS-CONSULTATION COMMENTS I agree with a great summary by reviewer 1. This discovery should be validated by top-quality data.

Reviewer #2 (Significance (Required)):

In the manuscript by Yu et al., the authors test the concept that certain proteins are unevenly distributed within distinct cell compartments. Due to this localization discrepancy, protein detection in some subcellular compartments can be "eclipsed" by a predominant subset of specific protein localizing in another cell compartment their actual distribution. Therefore, tiny amounts of physiologically relevant proteins could be biologically relevant. Still, their function in some locations can be overlooked (or eclipsed) because of the high expression level of the same protein in another subcellular compartment(s). Although, this concept is not particularly novel. For example, it is already known that many different proteins can localize to distinct cellular locations (e.g., permanent mitochondrial and peroxisomal localization of many proteins or transient localization of particular proteins to separate cell compartments). The authors apply a yeast system and an α-complementation assay to test further the role of such eclipsed proteins in mitochondrial biology. Specifically, they focus on the ubiquitin (Ub, or as abbreviated incorrectly in this manuscript; Ubi) conjugation pathway, components of which have never been convincingly shown to localize inside the mitochondria. This work proposes that certain ubiquitination events can occur inside yeast mitochondria. This work would represent a significant/exceptional discovery if supported by compelling data. However, the major problem with this work is that the conclusions are based on the ectopic expression of distinct proteins. This approach is not failproof in precise protein expression/delivery to the specific subcellular locations and is likely to result in a non-specific localization. Thus, the problem of eclipsed proteins is addressed by the methodology that may lead to the artificial generation of eclipsed overexpressed proteins. A more effective approach would be if the authors found a way to study this issue with endogenous proteins. The need for overexpression of mitochondria-targeted ubiquitin makes it challenging to reconcile the physiological role of these fundings. In addition, some critical technical issues and omissions further reduce the potential impact of this work (see Specific comments above). For example, strong evidence of mitochondria fraction purity and additional evidence that all the essential constructs used in this work are not misdirected to a different compartment are needed.

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

Summary: In this study, the authors detected a set of components of a ubiquitination system in the mitochondrial matrix in budding yeast using the subcellular compartment-dependent α-complementation assay. The authors detected the conjugates of mitochondrial targeting signal sequence-directed HA-Ub (preSu9-HA-Ub) in the mitochondrial matrix. The immunoprecipitates of the preSu9-HA-Ubi conjugates were highly enriched for the mitochondrial matrix proteins. Subsequently, the authors focused on the Rad6 E2 ubiquitin conjugating enzyme in the mitochondrial matrix and evaluated its inactivation-altered ubiquitination pattern in the organelle. The authors conclude that ubiquitination occurs in the mitochondrial matrix because of the eclipsed targeted components of the ubiquitination machinery.

Major comments: The authors argued that the proteins that were modified with preSu9-HA-Ubi, which was forced to be imported into the mitochondria, are present in the mitochondrial matrix, because these species are resistant to trypsin digestion. However, it was possible that they formed severe aggregates on the cytosolic surface of the mitochondria, and hence, were resistant to the proteinase. In other words, a small amount of proteins that were not imported into the mitochondria could be deposited on the cytosolic surface of the mitochondria, where they were modified with preSu9-HA-Ubi by cytosolic Rad6. To confirm if the preSu9-HA-Ubi-modified proteins were really present in the mitochondrial matrix, they should perform the protease protection assay in the presence of an appropriate detergent (Figure 3D). In addition, subcellular fractionation of the organelle by density gradient centrifugation, indirect immunofluorescence microscopic analysis of the preSu9-HA-Ubi conjugates, and/or experiments on the in vitro import of preSu9-HA-Ubi and Rad6 into the mitochondria would strongly support the authors conclusion. Other experiments that might support the authors conclusion would be to test whether the band pattern for the preSu9-HA-Ubi conjugates changes when the mitochondrial import is impaired.

Response: We will attempt to perform 1) Protease protection assay in the presence of a detergent (Figure 3D). 2) Subcellular fractionation of the organelle by density gradient centrifugation. 3) In vitro import of Rad6 into the mitochondria.

Minor comments: In Figure 3B, the molecular weight distributions of the preSu9-HA-Ubi conjugates and those of the preFum-HA-Ubi conjugates are different. Is there any reason for this difference?

In Figure 3E, the position of "-" (MG132) for lane 1 is not correct.

In Figure 6A: The band pattern for preSu9-HA-Ubi (lane 13) in the rad6-delta cells expressing Ubc8-alpha is different from that of the wild-type cells expressing Ubc8-alpha (lane 12) as well as that obtained from the rad6-delta cells harboring empty plasmids (lane 9). Is there any explanation for this observation?

In Figure 7B and S6: The level of preSu9-Rad6-alpha-SL17 in the rad6-delta cells is always lower than that in the wild-type cells (compare lanes 13 and 10 in Figure 7B, and lanes 13 and 12 in Figure S6). Is there any explanation for this observation? The protease protection assay (with detergent control) is needed to fully confirm that preSu9-Rad6-alpha-SL17 is present in the mitochondria.

In Figure S7, the authors presented the matrix proteins, Ilv5 and Aco1, detected in the preSu9-HA-Ubi IPed samples and described this observation in the main text. However, the authors also showed the blots for Idh1 and Fum1, which were also pulled down with preSu9-HA-Ubi from the WT cells more than from the rad6-delta cells. Is this correct? If so, please elucidate this observation in the main text.

Figure 8D and 8E are not cited in the main text. Although there are no explanations for these figures in the main text, it looks like Rad6-deltaN11-alpha resides in the mitochondrial fraction. However, the alpha-complementation assay suggests that it resides in the cytosol. Please explain this discrepancy.

First page of the discussion section, item 6): E2 Rad6, but not E3 Rad6?

Figure S7: HA-Ub (cytosolic form) control is needed in addition to the empty vector control.

Figure S7, left panel: There is an unnecessary line break in "Hsp60" and "Ilv5."

Figure S7, right panel: There is an unnecessary line break in "Hsp60."

CROSS-CONSULTATION COMMENTS I agree with comments of reviewer 1 and 2. -Validation of the complementation assay. -I also think that it is important to address whether intra-mitochondrial ubiquitination can be observed with endogenous level of ubiquitin. If even a small amount of preSu9-HA-Ub is mistargeted to the cytosol, proteins at the cytosolic side of mitochondrial outer membrane could be ubiquitinated and detected in the mitochondrial fraction. -Preparation of mitochondria with more sophisticated purification methods (i.e. high resolution density gradient) would be needed to separate mitochondria from ER and other organelles. -More information is needed in the materials and methods section.

Reviewer #3 (Significance (Required)): Significance Although the results are interesting and very important, as mentioned in the major comments section, additional experiments are needed to support their model. However, researchers working on the mitochondrial biology and ubiquitin systems might be interested in and influenced by the reported findings.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this study, the authors detected a set of components of a ubiquitination system in the mitochondrial matrix in budding yeast using the subcellular compartment-dependent α-complementation assay. The authors detected the conjugates of mitochondrial targeting signal sequence-directed HA-Ub (preSu9-HA-Ub) in the mitochondrial matrix. The immunoprecipitates of the preSu9-HA-Ubi conjugates were highly enriched for the mitochondrial matrix proteins. Subsequently, the authors focused on the Rad6 E2 ubiquitin conjugating enzyme in the mitochondrial matrix and evaluated its inactivation-altered ubiquitination pattern in the organelle. The authors conclude that ubiquitination occurs in the mitochondrial matrix because of the eclipsed targeted components of the ubiquitination machinery.

Major comments:

The authors argued that the proteins that were modified with preSu9-HA-Ubi, which was forced to be imported into the mitochondria, are present in the mitochondrial matrix, because these species are resistant to trypsin digestion. However, it was possible that they formed severe aggregates on the cytosolic surface of the mitochondria, and hence, were resistant to the proteinase. In other words, a small amount of proteins that were not imported into the mitochondria could be deposited on the cytosolic surface of the mitochondria, where they were modified with preSu9-HA-Ubi by cytosolic Rad6. To confirm if the preSu9-HA-Ubi-modified proteins were really present in the mitochondrial matrix, they should perform the protease protection assay in the presence of an appropriate detergent (Figure 3D). In addition, subcellular fractionation of the organelle by density gradient centrifugation, indirect immunofluorescence microscopic analysis of the preSu9-HA-Ubi conjugates, and/or experiments on the in vitro import of preSu9-HA-Ubi and Rad6 into the mitochondria would strongly support the authors conclusion. Other experiments that might support the authors conclusion would be to test whether the band pattern for the preSu9-HA-Ubi conjugates changes when the mitochondrial import is impaired.

Minor comments:

• In Figure 3B, the molecular weight distributions of the preSu9-HA-Ubi conjugates and those of the preFum-HA-Ubi conjugates are different. Is there any reason for this difference?

• In Figure 3E, the position of "-" (MG132) for lane 1 is not correct.

• In Figure 6A: The band pattern for preSu9-HA-Ubi (lane 13) in the rad6-delta cells expressing Ubc8-alpha is different from that of the wild-type cells expressing Ubc8-alpha (lane 12) as well as that obtained from the rad6-delta cells harboring empty plasmids (lane 9). Is there any explanation for this observation?

• In Figure 7B and S6: The level of preSu9-Rad6-alpha-SL17 in the rad6-delta cells is always lower than that in the wild-type cells (compare lanes 13 and 10 in Figure 7B, and lanes 13 and 12 in Figure S6). Is there any explanation for this observation? The protease protection assay (with detergent control) is needed to fully confirm that preSu9-Rad6-alpha-SL17 is present in the mitochondria.

• In Figure S7, the authors presented the matrix proteins, Ilv5 and Aco1, detected in the preSu9-HA-Ubi IPed samples and described this observation in the main text. However, the authors also showed the blots for Idh1 and Fum1, which were also pulled down with preSu9-HA-Ubi from the WT cells more than from the rad6-delta cells. Is this correct? If so, please elucidate this observation in the main text.

• Figure 8D and 8E are not cited in the main text. Although there are no explanations for these figures in the main text, it looks like Rad6-deltaN11-alpha resides in the mitochondrial fraction. However, the alpha-complementation assay suggests that it resides in the cytosol. Please explain this discrepancy.

• First page of the discussion section, item 6): E2 Rad6, but not E3 Rad6?

• Figure S7: HA-Ub (cytosolic form) control is needed in addition to the empty vector control.

• Figure S7, left panel: There is an unnecessary line break in "Hsp60" and "Ilv5."

• Figure S7, right panel: There is an unnecessary line break in "Hsp60."

CROSS-CONSULTATION COMMENTS

I agree with comments of reviewer 1 and 2.

• Validation of the complementation assay.
• I also think that it is important to address whether intra-mitochondrial ubiquitination can be observed with endogenous level of ubiquitin. If even a small amount of preSu9-HA-Ub is mistargeted to the cytosol, proteins at the cytosolic side of mitochondrial outer membrane could be ubiquitinated and detected in the mitochondrial fraction.
• Preparation of mitochondria with more sophisticated purification methods (i.e. high resolution density gradient) would be needed to separate mitochondria from ER and other organelles.
• More information is needed in the materials and methods section.

Significance

Significance

Although the results are interesting and very important, as mentioned in the major comments section, additional experiments are needed to support their model. However, researchers working on the mitochondrial biology and ubiquitin systems might be interested in and influenced by the reported findings.

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 by Yu et al., the authors test the concept that certain proteins are unevenly distributed within distinct cell compartments. Due to this localization discrepancy, protein detection in some subcellular compartments can be "eclipsed" by a predominant subset of specific protein localizing in another cell compartment their actual distribution. Therefore, tiny amounts of physiologically relevant proteins could be biologically relevant. Still, their function in some locations can be overlooked (or eclipsed) because of the high expression level of the same protein in another subcellular compartment(s). Although, this concept is not particularly novel. For example, it is already known that many different proteins can localize to distinct cellular locations (e.g., permanent mitochondrial and peroxisomal localization of many proteins or transient localization of particular proteins to separate cell compartments). The authors apply a yeast system and an α-complementation assay to test further the role of such eclipsed proteins in mitochondrial biology. Specifically, they focus on the ubiquitin (Ub, or as abbreviated incorrectly in this manuscript; Ubi) conjugation pathway, components of which have never been convincingly shown to localize inside the mitochondria. This work proposes that certain ubiquitination events can occur inside yeast mitochondria. This work would represent a significant/exceptional discovery if supported by compelling data. However, the major problem with this work is that the conclusions are based on the ectopic expression of distinct proteins. This approach is not failproof in precise protein expression/delivery to the specific subcellular locations and is likely to result in a non-specific localization. Thus, the problem of eclipsed proteins is addressed by the methodology that may lead to the artificial generation of eclipsed overexpressed proteins. A more effective approach would be if the authors found a way to study this issue with endogenous proteins. The need for overexpression of mitochondria-targeted ubiquitin makes it challenging to reconcile the physiological role of these fundings. In addition, some critical technical issues and omissions further reduce the potential impact of this work (see Specific comments below). For example, strong evidence of mitochondria fraction purity and additional evidence that all the essential constructs used in this work are not misdirected to a different compartment are needed.

Specific comments

1. The authors should demonstrate beyond doubt that the ω components of their assay (ω-C, which supposedly stays in the cytosol-ONLY and the ω-M component, which seemingly remains in the mitochondria-ONLY) are in the compartment that the authors claim. These two proteins are transfected into yeast cells and overexpressed. Therefore it is possible that they leak to other, not intended, subcellular compartments. The authors assume that ω-M and ω-C are exclusively located either in the mitochondria or the cytosol. However, this should be shown as validation of the assay. The indicated reference from 2005 (Ref.13) and others are irrelevant since assays have variations and are often researcher/lab dependent. This validation is very important since a misallocation of the overexpressed ω-M or ω-C, leaking into other subcellular compartments, may cause misdetection of the α-constructs.
2. It is not surprising that Ub conjugates are detected in mitochondrial fractions. It could be due to ubiquitination of the OMM (coming from the cytosol) or perhaps since the subcellular fractions were not pure mitochondria free from contamination (the likely culprit could be the ER). The mitochondrial fractions in this work were obtained by 10,000 g separation between cytosolic and mitochondrial crude fractions. Indeed, these 10,000 g crude fractions are highly impure with membranes from other compartments (i.e., microsomes, lysosomes, and so on). Therefore, more sophisticated purification methods should be used. In addition, the authors should also test these fractions for non-mitochondrial proteins from other membrane organelles.
3. Figure 2. Coomassie blue staining does not show any signal in the "M" fraction. It can be interpreted that the authors do not get any mitochondria there, and therefore the lack of Ub signal is due to the absence of the protein in the samples. Using the same amount of protein from each fraction would probably reduce the necessity of 15x enrichment.
4. Figure 3. It is puzzling why the HA-UBQ presence is so strong in the crude mitochondrial fraction, but the preSu9-HA-Ub signal (mito-matrix) is comparatively weak. These data suggest that the crude mito-fraction could be highly contaminated with OTHER membranes. On the other hand, the preSu9-HA-UBQ signal is no more than 1-5% of the total mitochondrial signal. The high enrichment of the HA-Ubi in both cytosols and the mitochondria could indicate the OMM ubiquitination or (again) contamination by other compartments. The constructs with MTS are detected in the mitochondria. However, the localization of tagged MTS-Ubi in a non-targeted compartment (e.g., cytosol) should be excluded by additional exposure times. Because the manuscript talks about eclipsed proteins, this is important.
5. Figure 3C-E. These data indeed suggest that the Ub-conjugates could be formed inside the mitochondria. However, the above-discussed possibility that other than mitochondria compartments co-sediment in the 10,000g fractions makes the data interpretation highly challenging.
6. Figure 4. Unsurprisingly, mitochondrial targeting of Ub leads to detecting some co-immunoprecipitating mitochondrial proteins. However, these data do not support the notion that Ub conjugation machinery acts inside the mitochondria and that the target proteins are indeed conjugated with Ub (the interaction with Ub is not equal to being conjugated). At the minimum, the authors should provide a validation that some of the detected mitochondrial matrix proteins are indeed ubiquitinated. To this end, purified mitochondria could be used for the candidate protein IP under denaturing conditions and then blotted for the candidate protein and Ub.
7. Figure 5. The knock-out of the E2 Rad6 causes a change in the mitochondria ubiquitination pattern. This is an interesting observation, but again it does not prove that the change in the mitochondrial ubiquitination is due to the activity of Rad6 inside of the mitochondria, as opposed to ubiquitination of the OMM proteins or contaminating fractions. One also wonders why overexpression of mitochondria-targeted Ub would be necessary to detect the ubiquitination if this process was physiologically relevant, especially given that detecting endogenous Ub is not challenging. Furthermore, the apparent increase in ubiquitination in E2 mutant cells (Fig. 5) should also be addressed in more detail. Finally, data from one WB is shown, and quantification of several independent experiments should also be provided.
8. Figure 6. Can the authors provide Western blot data showing the expression of Rad6? Furthermore, quantifying these rescue experiments is necessary to make this conclusion more solid.
9. Figure 7. The authors found that preSu9-Rad6-α have problems being imported into the mitochondria matrix; therefore, they rebuild it as a preSu9-Rad6-α-SL17 protein. SL17 is a degron that targets the cytosolic protein (not imported into the mitochondria) to the proteasome and degraded (Figs. 7A-B-C). These issues could be a red flag for the rest of the manuscript, suggesting that other constructs (that were not critically evaluated for their localization in this work) could leak to different cellular compartments.
10. The manuscript needs to be carefully edited, some references are in the not correct format, and there are issues with figure labels.

CROSS-CONSULTATION COMMENTS

I agree with a great summary by reviewer 1. This discovery should be validated by top-quality data.

Significance

In the manuscript by Yu et al., the authors test the concept that certain proteins are unevenly distributed within distinct cell compartments. Due to this localization discrepancy, protein detection in some subcellular compartments can be "eclipsed" by a predominant subset of specific protein localizing in another cell compartment their actual distribution. Therefore, tiny amounts of physiologically relevant proteins could be biologically relevant. Still, their function in some locations can be overlooked (or eclipsed) because of the high expression level of the same protein in another subcellular compartment(s). Although, this concept is not particularly novel. For example, it is already known that many different proteins can localize to distinct cellular locations (e.g., permanent mitochondrial and peroxisomal localization of many proteins or transient localization of particular proteins to separate cell compartments). The authors apply a yeast system and an α-complementation assay to test further the role of such eclipsed proteins in mitochondrial biology. Specifically, they focus on the ubiquitin (Ub, or as abbreviated incorrectly in this manuscript; Ubi) conjugation pathway, components of which have never been convincingly shown to localize inside the mitochondria. This work proposes that certain ubiquitination events can occur inside yeast mitochondria. This work would represent a significant/exceptional discovery if supported by compelling data. However, the major problem with this work is that the conclusions are based on the ectopic expression of distinct proteins. This approach is not failproof in precise protein expression/delivery to the specific subcellular locations and is likely to result in a non-specific localization. Thus, the problem of eclipsed proteins is addressed by the methodology that may lead to the artificial generation of eclipsed overexpressed proteins. A more effective approach would be if the authors found a way to study this issue with endogenous proteins. The need for overexpression of mitochondria-targeted ubiquitin makes it challenging to reconcile the physiological role of these fundings. In addition, some critical technical issues and omissions further reduce the potential impact of this work (see Specific comments above). For example, strong evidence of mitochondria fraction purity and additional evidence that all the essential constructs used in this work are not misdirected to a different compartment are needed.

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

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---

Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript, Zhang et al. investigate whether ubiquitination occurs inside mitochondria of the budding yeast S. cerevisiae. They first observe thanks to a sensitive complementation assay that several components of the yeast ubiquitination (and deubiquitination) machinery can localize inside mitochondria. To be able to specifically probe ubiquitin conjugates assembled inside mitochondria they fused HA-tagged ubiquitin to a mitochondrial targeting sequence. Using this construct, they demonstrate that ubiquitin conjugates can be assembled in mitochondria. A series of elegant experiments demonstrates that the pattern of ubiquitin conjugates depends on the mitochondrial localization and the activity of the ubiquitin conjugating enzyme Rad6. Altogether, these results convincingly demonstrate that ubiquitination can occur inside yeast mitochondria when ubiquitin is intentionally targeted inside this organelle. It however remains unclear whether mitochondrial ubiquitination occurs in endogenous conditions (without targeting ubiquitin into this compartment) and whether it affects mitochondrial functions.

Major comments:

1) The materials and methods section is lacking important information (western blot protocol, details of antibodies, strains, plasmids...). It is thus difficult to evaluate how several experiments were performed and how their design (e.g. the promoters chosen to express tagged proteins) could impact the interpretation of the results. This is a major issue that needs to be corrected. The main text should also explicitly indicate whether tagged proteins used in the alpha-complementation assay are overexpressed or not.

2) Despite the previous comment, the data presented in the manuscript convincingly demonstrate that multiple components of the ubiquitination machinery can localize within mitochondria and that ubiquitin conjugates can be assembled in mitochondria when ubiquitin is modified to be intentionally targeted into this compartment. However, little data is shown to support the hypothesis that ubiquitin conjugates can be assembled in mitochondria when ubiquitin is not fused to a mitochondrial targeting sequence. Thus, in my opinion, the evidences presented in the current manuscript are not sufficient to conclude that ubiquitin conjugates are assembled in mitochondria in endogenous conditions (as this is done implicitly). Additional evidences are needed to draw this conclusion (see some experimental suggestions hereafter). Without further evidences, the speculative aspects of the claim that "ubiquitination occurs in the mitochondrial matrix" should be discussed explicitly.

3) The authors used a mass spectrometry approach to identify mitochondrial ubiquitination substrates. However, they have not yet succeeded in identifying a substrate whose modification is specifically regulated by a given component of the mitochondrial ubiquitination machinery. They have also not identified a phenotype or process impacted by mitochondrial ubiquitination. Thus, at this stage, the biological consequences of mitochondrial ubiquitination remain elusive.

4) The authors have not directly investigated whether ubiquitin itself (without a mitochondrial targeting sequence) localizes in mitochondria. I encourage them to address this question since it would provide an important piece of evidence suggesting that mitochondrial ubiquitination can occur in endogenous conditions. This could be done using the alpha-complementation assay and the results could be presented within Figure 1. Ideally this experiment should be performed without overexpressing ubiquitin. Note that if the authors decide to use a C-terminally tagged form of ubiquitin for this experiment, the GG motif of ubiquitin should be mutated to avoid cleavage of the alpha tag by cellular DUBs. This form of ubiquitin will not be conjugatable, but this is not an issue for this experiment since its aim is to determine whether ubiquitin can be targeted to mitochondria, not to probe conjugates.

5) In the top panels of Figure 2 and S1, free ubiquitin is well detectable in the total and cytosolic fractions. It is however not clear to me whether it is also detectable in the concentrated mitochondrial fraction. If yes and if it would be resistant to trypsin digestion, it would provide an additional evidence that endogenous ubiquitin can be targeted to the mitochondrial matrix (see previous comment).

6) The data shown in the top panel of Figure 2 and S1 also suggest that free ubiquitin is less concentrated in mitochondria than in the cytosol (since it is more difficult to detect in the concentrated mitochondrial fraction than in the cytosolic fraction, see previous comment). It is thus possible that the use of preSu9-HA-Ubi (or preFum1-HA-Ubi) lead to an artificially high intra-mitochondrial concentration of free ubiquitin. As the concentration of free ubiquitin is known to impact ubiquitination processes, I encourage the authors to compare the relative levels of free ubiquitin present in the mitochondrial fraction prepared from wt and preSu9-HA-Ubi (or preFum1-HA-Ubi) expressing cells. If free ubiquitin is detectable in mitochondrial fractions and resistant to trypsin (see previous comment), this could be done by repeating the experiment shown in Figure 3B and probing the blot with an antibody that recognizes free ubiquitin.

7) I strongly encourage the authors to provide more data indicating that "ubiquitination occurs in mitochondria" by performing experiments that do not rely on the use of the preSu9-HA-Ubi or other forms of ubiquitin that are intentionally targeted to mitochondria. For instance, they could analyse the pattern of HA-Ubi conjugates of trypsin digested mitochondrial fractions prepared from wt, rad6-delta, and rad6-delta complemented with preSu9-Rad6-alpha-SL17. Note that if trypsin digested mitochondrial fractions are too contaminated by ubiquitinated proteins present outside mitochondria to perform this experiment, the authors may use the unspecific DUB Usp2 as an alternative protease to strip ubiquitinated proteins from the mitochondria periphery.

Minor comments:

1) Overall, the manuscript is well organized and easy to follow. The text is clearly written; the figures are well annotated.

2) The authors should provide full images of all the blots with anti-ubiquitin and anti-HA antibodies so that one can see the bands corresponding to free ubiquitin (or free HA-Ubi). For instance, in Figure 3B, it is not possible to see the presence (or absence) of the band corresponding to free HA-Ubi because the very bottom of the image is cut.

3) The authors should indicate whether the MTS of Su9 (and Fum1) are expected to be cleaved after import of preSu9-HA-Ubi (and preFum1-HA-Ubi) in mitochondria. They should also label on the corresponding immunoblots the presence (or absence) of the band corresponding to the free preSu9-HA-Ubi (and preFum1-HA-Ubi) (or HA-Ubi if the MTS is expected to be cleaved from these constructs).

4) In Figure 3B, the ubiquitin conjugates produced with preSu9-HA-Ubi and preFum1-HA-Ubi have different migration patterns. I think this should be explicitly mentioned and discussed. Could it be due to the presence of lysine residues in the Su9 or Fum1 MTS that could lead to the assembly of artificial ubiquitin chains?

5) The authors indicate that "endogenous Rad6 [...] is expressed at very low levels and can hardly be detected in the mitochondrial fraction by WB (Figure S5)". I did not manage to observe the band corresponding to endogenous Rad6 in the mitochondrial fraction in the pdf. The authors should provide a more contrasted or better quality image.

CROSS-CONSULTATION COMMENTS

• I agree with reviewer 2 that proper validation of the complementation assay is crucial for this manuscript. I was myself wondering whether it uses endogenously tagged proteins or whether it is based on an overexpression system. I imagine this information will be detailed in the manuscript in preparation mentioned by the authors. I am therefore wondering whether it would be possible to ask the authors to provide the draft of this manuscript (or at least the validation part).

• I agree with most comments of reviewer 3. Regarding the hypothesis that preSu9-HA-Ubi could form aggregates on the cytosolic surface of the mitochondria, I think that the results presented on Figure 7B rather argue against it (since they indicate that Rad6 localized inside mitochondria can restore the pattern of ubiquitin conjugates). That's why (in my opinion) the major question the author now need to adress is whether intra-mitochondrial ubiquitination occurs in endogenous conditions (ie without forcing ubiquitin into this compartment and without E2 or E3 overexpression).

Significance

The finding that ubiquitination occurs inside mitochondria would be an important conceptual advance, which would open new perspectives both for ubiquitination and mitochondrial biology research. However, the significance of the current manuscript is limited because the presented evidences heavily rely on the use of artificial conditions (ubiquitin tagged with a mitochondrial-targeting sequence) that may trigger irrelevant ubiquitination events. The significance would be much higher if the authors would provide further evidences indicating that intra-mitochondrial ubiquitination occurs in endogenous conditions and/or if they had identified a mitochondrial process specifically impacted by mitochondrial ubiquitination.

Expertise of the reviewer: Ubiquitination, Yeast biology, protein-protein interactions. No specific expertise in mitochondrial biology

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Reply to the reviewers

Reviewer #1:

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1) The authors could consider qualifying the observations as preliminary as no

mechanistic data or longer-term pathophysiology is investigated. Indeed, the latter is well

beyond the current scope and may require generation of cell-type specific STING ki mice.

• *

Thank you for the comment. We have qualified our observations as preliminary (line 662).

Indeed, generating cell-type specific STING ki mice is part of our future plans.

2) The authors consistently write "NF-kB/inflammasomes" - these two pathways (although

related) are quite distinct and should not be lumped together in such a way.

• *

Thank you for this important note, we now corrected the text (for example see section headings in the Results section, lines 338 and 415).

3) Line 79: "NRLP3" should be corrected to NLRP3.

• *

Line 210: age of "adult mice" in weeks should be state in the text and figure legend.

Thank you, corrected.

4) Line 262: In Figure 3B and D the images look very different and there is no indication of

what a positive inclusion is? This should be indicated on the image.

• *

Thank you for the suggestion. We replaced the corresponding panels with new images, where we show the nuclei with blue, and the Thioflavin S staining with magenta pseudo-color (current Figure 3E). We marked the outline of Thioflavin S positive cells with yellow. An inset showing the magnification of some neurons with inclusions is also presented.

5) Line 280: The data of Ifi44 should also be mentioned in the text.

• *

Thank you. We performed new experiments to show the gene expression changes in the

striatum and in the substantia nigra, therefore majority of the gene expression data from the cortex has been moved to the supplementary material (supplemental Figures 3 and 5), and is not discussed in detailed in the current manuscript.

6) Line 290: Figure 4, Examining IL-1B and Caspase-1 transcripts is not a readout of

inflammasome activation. pro-IL1B is upregulated in response to NFkB activity. Inflammasome

activation is commonly examined in other methods e.g. via ASC puncta formation (imaging

based), active IL-1B secretion (ELISA), Caspase-1 and IL-1B cleavage via western blot

Thank you for this suggestion, we performed new experiments and added the data as Figure 6.

• We performed Western blot analysis to detect IL-1β cleavage and NLRP3 proteins from the striatum (Figure 6C-E). 2) We quantified the number of ASC puncta within microglia and astroglia from striatal sections (Figure 6F-I). 3). 3) We also measured the protein levels of several additional immune mediators in the striatum of STING ki and KO animals (supplemental Figure 6, summary heatmap is on Figure 7A). 7) Line 310: The NF-kB subunit examined should be stated (p65?). Furthermore, IRF3

translocation might be a better readout for STING activation.

• *

We indeed detected the p65 subunit of NF-kB (antibody is listed in the supplemental Table), and now it is also indicated in the text (line 366). We also performed subcellular fractionation and quantified IRF3 in the nuclear and cytoplasmic fractions. The data is now added on Figure 6A, B.

8) Discussion: Given the findings here suggest a strong role for NF-kB, a short discussion

of IFN vs non-IFN responses from STING should be included. There have been a number of

seminal papers demonstrating the importance of non-IFN STING responses of late as well as

much evidence from SAVI mice to suggest some non-IFN driven pathologies.

• *

Thank you for the suggestion. The data on inflammasomes were given a separate section in the results (from line 395). In the discussion, from line 535 we discuss the IFN dependent response and from line 548 we discuss the non-IFN driven pathways.

9) Discussion: Is there any evidence from the human SAVI patients of neuroinflammation

etc. This should be mentioned either way in the discussion

• *

Thank you for this comment. The manifestation of neurological symptoms is not a core feature of the human SAVI disease. Some patients suffer from various neurological symptoms e.g. calcification of basal ganglia, spastic diplegia and episodes of seizure (Fremond et al., 2021). We inserted a short text in discussion (lines 532-534).

10) Discussion: There is a large body of work demonstrating STING-induced cell death in

numerous cell types. Despite this it is not mentioned nor discussed but should be. It could

represent how dopaminergic neurons are lost in the STING ki mice.

• *

Thank you for pointing out the gap in our discussion. We added additional text in lines 604-618.

11) The resolution/quality of some of the imaging is not great but this may be due to PDF

Compression

Thank you, we upload the figures with higher resolution.

Reviewer #2:

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1) The authors base their conclusions (line 215-216) on the neuroinflammatory status of

their mice strongly on an assessment of the Iba1 and GFAP-positive area fraction. Increase of

Iba1 and GFAP areas does not necessarily correlate with an increased cytokine production and

release by the cells. Therefore, in addition the measurement of cytokine mRNAs it would be

necessary to measure cytokines also on protein level (see also #4 and #5).

• *

Thank you for this suggestion, we measured the protein levels of several immune mediators with LEGENDplex™ assay from the striatum, and the new data are included as Figure 7A and supplemental Figure 6.

2) In the same context: Is the increase of Iba1 and GFAP- covered area due to increased

proliferation of microglia and astrocytes or due to increased expression of these markers in

activated glia? How is the number of Iba1/GFAP-positive cells affected?

• *

We quantified the number of glia cells in the striatum and in the substantia nigra of adult STING WT and STING ki mice, and, parallel with higher immunoreactivity for the corresponding markers, we detected increased number of cells as well. The quantifications are now included in supplemental Figure 1.

3) Nowadays we know that microglia and astrocytes can exist in a variety of activated

states which can be either beneficial or detrimental. An analysis of disease-associated

microglial markers (Keren-Shaul et al. 2017) would give a good picture of the state microglia are

in.

• *

Thank you for the suggestion. In addition to the panel of immune modulators at the protein level (supplemental Figure 6), we performed qPCR analysis of additional “M1” marker (Nos2) and additional “M2” markers (Il4, Fizz2, Ym1) (Gong et al., 2019). The data is included in Figure 7A and shown in supplemental figure 6. The findings are described from line 431.

4) It also would be of interest to determine which cell type is responsible for the observed

neurodegeneration. Which cytokines are released by microglia or astrocytes upon STING

activation? Even in vitro experiments would help here to get a more profound understanding.

• *

We agree with the suggestion, however, the further in vitro experiments are beyond the scopes of this study and will be the basis of a future project.

5) In line 273 the authors describe that STING is known to activate NFkB and the

inflammasome. As proof that this is also occurring in their mouse, they perform qPCR analysis

of whole brain IL-1b, TNF-a and Casp1 expression. While this analysis indicates that there is

indeed an increased mRNA production of proinflammatory cytokines in the brains of STING ki

mice, it does not give any indication whether the inflammasome is active or not. The inflammasome is a protein complex largely regulated on protein level. Meaning an assessment

of the cleavage of Caspase 1 on protein level or the presence of cleaved IL-1b in comparison to

uncleaved Pro-IL-1b by Western Blot as well as a staining for the number of inflammasomes

would be required to draw these conclusions.

• *

Thank you for the suggestion. We performed additional experiments: 1) Western blot to detect pro-IL1b and IL1b and NLRP3 proteins from the striatum (Figure 6C-E), and 2) we quantified the number of ASC puncta within microglia and astroglia from striatal sections (Figure 6F-I).

6) To conclude that NFkb/inflammasome pathway is the most active/crucial in astrocytes

(line 354) a staining for ASC inflammasomes would be of importance, especially as astrocytes

normally do not express NLRP3.

• *

Thank you for this comment. We stained brain sections for ASC specks and for microglia (Iba1) and astroglia (GFAP) markers (Figure 6F-I). Although amount of ASC specks in astroglia was lower than in microglia, we found still a substantial amount of ASC specks in astroglia in the brains of STING ki animals.

7) As already shown for ALS (Yu et al., 2020) and Parkin KO (Sliter et al. 2018), the authors want to

further assess the relevance of the STING pathway to PD (line 27-28). Therefore, an in-depth analysis of

key PD hallmarks beyond phosphorylated a-synuclein, loss the other was parkin/PINK related (so TDP

deleted) of TH-stained neurons and dopamine reduction is needed. In the discussion the authors

hypothesize that autophagy (line 467) may be linked to the observed phenotype. Therefore,

assessment of autophagy/mitophagy as well as mitochondrial dysfunction and mtDNA should

be analysed. In the same line of thought it would be important to know if and how the observed

dopamine reduction effects mouse behaviour, thus mice should be subjected to the Rotarod or

pole or beam walk test.

• *

Thank you for these suggestions. In the work by Yu et al. and Sliter et al., the STING pathway was shown to mediate neurodegeneration resulting from TDP-43 pathology and mitochondrial damage. Our work is complementary by investigating the effects of constitutive activation of STING. We have therefore focused on the signaling pathways downstream of STING. As mentioned above, the most important next step will be to separate the contributions of neuronal and glial cells by generating cell type specific STING activation. Of course, it will be interesting to see at a later time point whether STING activation feeds back. We also speculate that STING activation may also cause TDP-43 pathology. Yet, this will be part of a future study. To acknowledge that the pathology is not specific to alpha-synuclein, we added a short statement from line 634.

With respect to the comprehensive analysis of the PD phenotype, our work includes the

classical parameters of TH neuron number, TH fiber density, dopamine concentration and

synuclein pathology. With respect to mouse behavior, we note that the STING ki mice have severe inflammation in the lung, kidney and other (peripheral) organs, reduced body weight and reduced lifespan (Luksch et al., 2019; Motwani et al., 2019; Siedel et al., 2020). Motor deficits cannot be attributed to dopamine neuron degeneration and for this reason were not included (stated in the Discussion, lines 624-625). In order to expand the description of the PD phenotype we now included measurements of cytosolic reactive oxygen species, mitochondrial oxygen species and nitric oxide, which result from inflammation and are known to affect dopaminergic neurons (new Figure 8).

Reviewer #3:

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1) The method for quantification of TH-positive cells is not sufficient. They just described

how they stained every fifth sections but did not mention how they count. This is a critical point

and they should carefully provide information more than just referring their previous paper.

Counting of dopaminergic neurons and quantification of fibers was described in a dedicated section of the methods. This section has now been expanded (from line 154).

2) It is not persuasive that they did not investigate local inflammation in SN. They

presented increased microglia and astrocytes in the striatum but not analyzed these cells in SN

• *

Indeed, we measured neuroinflammation in the substantia nigra as well, however, although increased in STING ki mice, it was less pronounced than neuroinflammation in the striatum. We now include the quantification of area fraction as well as cell number counting of microglia and astroglia in the substantia nigra of STING WT and STING ki animals (supplemental Figure 1), and also the expression of inflammatory mediators in Figure 4.

3) In Figure 3, they analyzed alpha-synuclein phosphorylation and beta-sheet structure in

the striatum. This is funny from the aspect of Parkinson's disease, which dominantly affects SN.

They should perform similar experiments with SN samples. In a different aspect, the aggregates

detected by Thio S may not be alpha-synuclein and could be tau, TDP43 or other substances.

Phospho-synuclein of course does not mean aggregation, so they can consider electron

microscopy.

• *

We agree with the reviewer. To complement our data, we therefore performed solubility assay both from the striatum and from the substantia nigra to quantify the ratio of alpha-synuclein in the Triton X-100 soluble and insoluble fractions (Figure 3C, D) as previously (Szego et al., 2022; Szegő et al., 2019). Additionally, we quantified phosphorylated alpha-synuclein from the substantia nigra as well Figure 3A,B).

We also agree with the reviewer that the presence of Thioflavin S-positive inclusions may also contain other, beta-sheet forming proteins and noted this from line 634.

4) Figure 5, pSTAT3 increased in Iba1-negative cells, which seem neurons from the size of

nuclei. First, the authors should investigate the identity of pSTAT3-positive cells with GFAP and

MAP2. If pSTAT3 is actually increased in neurons, what does it mean in the pathology? For

instance, in viral infection, STAT3 activation triggers suicide of neurons to prevent further

proliferation of viral particles in neurons. Is it homologous or other function?

• *

Thank you for this suggestion. The brain sections were stained for Iba1 and GFAP. pSTAT3 nuclear staining indeed increased in non-glia cells, based on the morphology, we think in neurons. However, detailed characterization of the signal is out of the scopes of this (preliminary) study.

5) In Figure 6 and overall, cell types in which the activation of three signaling pathways,

were mixed up and hard to understand the actual situation in the brain.

• *

In our model, STING is activated in all cells. Consequently, we cannot determine the origin of immune mediators found elevated in the STING ki mice. This will require cell type specific STING activation. In order to react to the reviewer’s comment and be clearer, we have added more details about the brain region and age of mice used for each analysis also in the figures.

6) In the method section, the original paper for generation of heterozygous STING N153S

KI mice should be Warner et al, JEM 2017.

• *

We used a STING N153S ki mouse strain that was independently generated in the Technical University Dresden (Luksch et al., 2019).

7) NF-κB stains seem located in cytoplasm in Figure 5B.

• *

We agree: especially in the young STING ki mice, cytoplasmic NF-kB staining is increased

compared to STING WT mice. To quantify nuclear translocation, however, we counted the

number of those cells where NF-kB signal was overlapping with the nuclear Hoechst staining.

8) In Figure 4 and 6, why the authors evaluate gene expressions in frontal cortex instead of

SN or striatum.

• *

As noted in several comments, we show here that the STING-induced pathology involves

dopaminergic neurons, but believe that it is not specific for the dopaminergic system given that STING-ki is ubiquitously expressed. For practical reasons, we have used cortical samples for the expression analysis. For consistency, we now performed additional qPCR measurement from the striatum and from the substantia nigra and included them as new Figure 4 and supplemental Figure 6N-Q. The previous data from the cortex was moved to the supplemental Figures 3 and 5. Additionally, we measured the levels of several inflammatory modulators from the striatum of STING ki and KO animals (Figure 7A and supplemental figure 6A-M).

9) In some groups (Sting-ki;ifnar1-/- in Fig 6C, 6E), the values were separated to two

groups, which makes readers to doubt on soundness of their genotyping.

• *

Our genotyping protocol is highly standardized, and the genotype of the animals were correctly assigned. Here we provide an example of gel images showing the products after PCR reactions for the STING N153S allele (Figure 1a), STING WT allele (Figure 1b), Ifnara WT allele (Figure 1c) and lack of Ifnara allele (Figure 1d) of the same animals. We note that a bimodal distribution of phenotypes is often observed in Ifnar-/- mice.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors tried to investigate the role of STING in neurodegeneration of dopaminergic neurons with heterozygous STING N153S knock-in mice and their offspring mated with IFNAR or Casp1 KO mice. They observed preliminarily the reduction of dopaminergic neurons (TH-positive cells) in substantia nigra (SN), and added further investigation mostly based on morphological analysis. Though the topic they investigated is highly important, their data remain in preliminary states and are not well organized from the aspect of brain regions and cell types (i.e., neuron, astrocyte or microglia). It is a pity that they did not provide sufficient results for this important question.<br /> The rationale for that they focused on alpha-synuclein but not on other neurodegenerative disease proteins is not strong. Collectively, although their data have not reached to construction of a hypothesis, depending on the level of journal, the manuscript could be publishable after extensive additional experiments and rigorous revision.

Major points

1. The method for quantification of TH-positive cells is not sufficient. They just described how they stained every fifth sections but did not mention how they count. This is a critical point and they should carefully provide information more than just referring their previous paper.
2. It is not persuasive that they did not investigate local inflammation in SN. They presented increased microglia and astrocytes in the striatum but not analyzed these cells in SN.
3. In Figure 3, they analyzed alpha-synuclein phosphorylation and beta-sheet structure in the striatum. This is funny from the aspect of Parkinson's disease, which dominantly affects SN. They should perform similar experiments with SN samples. In a different aspect, the aggregates detected by Thio S may not be alpha-synuclein and could be tau, TDP43 or other substances. Phospho-synuclein of course does not mean aggregation, so they can consider electron microscopy.
4. Figure 5, pSTAT3 increased in Iba1-negative cells, which seem neurons from the size of nuclei. First, the authors should investigate the identity of pSTAT3-positive cells with GFAP and MAP2. If pSTAT3 is actually increased in neurons, what does it mean in the pathology? For instance, in viral infection, STAT3 activation triggers suicide of neurons to prevent further proliferation of viral particles in neurons. Is it homologous or other function?
5. In Figure 6 and overall, cell types in which the activation of three signaling pathways, were mixed up and hard to understand the actual situation in the brain.

Minor points

1. In the method section, the original paper for generation of heterozygous STING N153S KI mice should be Warner et al, JEM 2017.
2. NF-κB stains seem located in cytoplasm in Figure 5B.
3. In Figure 4 and 6, why the authors evaluate gene expressions in frontal cortex instead of SN or striatum.
4. In some groups (Sting-ki;ifnar1-/- in Fig 6C, 6E), the values were separated to two groups, which makes readers to doubt on soundness of their genotyping.

Significance

• Conceptual for the field.
• Genetic analysis of the hyperactive STING mouse model in neurodegeneration is new.
• Researchers in the field of neurodegeneration and immunology audience might be interested.
• Neurodegeneration, innate immunity, molecular biology, neuropathology, neurology.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Szegö et al. show that constitutive activation of the stimulator of interferon genes (STING) by the gene variant N153S in a heterozygous mouse model leads to reduction of dopaminergic neurons and increased glial cell activation. The comparison of juvenile (5 weeks) and adult (20 weeks) mice nicely shows that increased glial cell activation preceded the neurodegeneration induced by STING activation. Assessment of cytokine mRNA expression as well as phosphorylated a-synuclein revealed increased pathology in adult STING ki mice. The authors identified NF-kB, Casp1 as well as nuclear pSTAT to be upregulated in these mice. Using a conclusive step-by-step assessment of the STING cascade components, the authors show that glial activation and dopaminergic neuron degeneration partially depend both on Casp1 and Ifnar1.

Major points:

1. The authors base their conclusions (line 215-216) on the neuroinflammatory status of their mice strongly on an assessment of the Iba1 and GFAP-positive area fraction. Increase of Iba1 and GFAP areas does not necessarily correlate with an increased cytokine production and release by the cells. Therefore, in addition the measurement of cytokine mRNAs it would be necessary to measure cytokines also on protein level (see also #4 and #5).
2. In the same context: Is the increase of Iba1 and GFAP- covered area due to increased proliferation of microglia and astrocytes or due to increased expression of these markers in activated glia? How is the number of Iba1/GFAP-positive cells affected?
3. Nowadays we know that microglia and astrocytes can exist in a variety of activated states which can be either beneficial or detrimental. An analysis of disease-associated microglial markers (Keren-Shaul et al. 2017) would give a good picture of the state microglia are in.
4. It also would be of interest to determine which cell type is responsible for the observed neurodegeneration. Which cytokines are released by microglia or astrocytes upon STING activation? Even in vitro experiments would help here to get a more profound understanding.
5. In line 273 the authors describe that STING is known to activate NFkB and the inflammasome. As proof that this is also occurring in their mouse, they perform qPCR analysis of whole brain IL-1b, TNF-a and Casp1 expression. While this analysis indicates that there is indeed an increased mRNA production of proinflammatory cytokines in the brains of STING ki mice, it does not give any indication whether the inflammasome is active or not. The inflammasome is a protein complex largely regulated on protein level. Meaning an assessment of the cleavage of Caspase 1 on protein level or the presence of cleaved IL-1b in comparison to uncleaved Pro-IL-1b by Western Blot as well as a staining for the number of inflammasomes would be required to draw these conclusions.
6. To conclude that NFkb/inflammasome pathway is the most active/crucial in astrocytes (line 354) a staining for ASC inflammasomes would be of importance, especially as astrocytes normally do not express NLRP3.
7. As already shown for ALS (Yu et al., 2020) and Parkin KO (Sliter et al. 2018), the authors want to further assess the relevance of the STING pathway to PD (line 27-28). Therefore, an in-depth analysis of key PD hallmarks beyond phosphorylated a-synuclein, loss of TH-stained neurons and dopamine reduction is needed. In the discussion the authors hypothesize that autophagy (line 467) may be linked to the observed phenotype. Therefore, assessment of autophagy/mitophagy as well as mitochondrial dysfunction and mtDNA should be analysed. In the same line of thought it would be important to know if and how the observed dopamine reduction effects mouse behaviour, thus mice should be subjected to the Rotarod or pole or beam walk test.

Significance

The manuscript is well written and clearly structured. The data are convincing and correlate well with earlier works, however they lack novelty. The findings that STING exhibits proinflammatory (Abdullah et al. 2018; Sharma et al., 2020; Glück et al., 2017; Yu et al. 2020, 2021) and neurodegenerative effects (e.g. the rescue of neuron loss and motoric defect shown in STING-KO Parkin mutator mice by Sliter et al. 2018) were already shown. The later paper points out already the relevance of STING in PD. All pathway components investigated here were already known to be triggered by STING and/or are known for their involvement in neurodegeneration and an unbiased screening for novel pathways triggered by STING, which could have revealed new perspectives, was not included. An assessment of the following aspects would give a missing novel insight into the role of STING in neurodegeneration.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In the paper by Szego et al., the authors examined the contribution of the innate immune receptor STING to neuroinflammation and the degeneration of dopaminergic neurons. To do this they utilised a systemic mouse model of STING-associated vasculopathy with onset in infancy (SAVI) driven by a gain-of-function knock-in (ki) mutation in STING (N153S in this case). This mouse model has been well characterised previously with a focus on the major pathologies commonly observed in the human SAVI patients (e.g. Interstitial Lung Disease, pulmonary fibrosis) but little has been done to examine neuroinflammation in this setting. As such, the approach is a good one and the observations made suggest that aberrant STING activation, in addition to driving neuroinflammation, causes loss of dopaminergic neurons and may contribute to aSyn pathology. Overall this is an interesting observation study but lacks any mechanistic insights into how STING may mediate these processes and if what the functional consequences of STING-induced neuroinflammation are for the animal - If aged do they ultimately acquire a PD-like phenotype?

Major comments:

• Based on the data presented the key conclusions from the authors are convincing and not overstated.
• The authors could consider qualifying the observations as preliminary as no mechanistic data or longer-term pathophysiology is investigated. Indeed, the latter is well beyond the current scope and may require generation of cell-type specific STING ki mice.
• The data and the methods are presented in such a way that ensure they are reproducible.
• All the experiments appear to be adequately replicated and appropriate statistical analysis has been applied.

Minor comments:

• The authors consistently write "NF-kB/inflammasomes" - these two pathways (although related) are quite distinct and should not be lumped together in such a way.
• Line 79: "NRLP3" should be corrected to NLRP3.
• Line 210: age of "adult mice" in weeks should be state in the text and figure legend.
• Line 262: In Figure 3B and D the images look very different and there is no indication of what a positive inclusion is? This should be indicated on the image.
• Line 280: The data of Ifi44 should also be mentioned in the text.
• Line 290: Figure 4, Examining IL-1B and Caspase-1 transcripts is not a readout of inflammasome activation. pro-IL1B is upregulated in response to NFkB activity. Inflammasome activation is commonly examined in other methods e.g. via ASC puncta formation (imaging based), active IL-1B secretion (ELISA), Caspase-1 and IL-1B cleavage via western blot.
• Line 310: The NF-kB subunit examined should be stated (p65?). Furthermore, IRF3 translocation might be a better readout for STING activation.
• Discussion: Given the findings here suggest a strong role for NF-kB, a short discussion of IFN vs non-IFN responses from STING should be included. There have been a number of seminal papers demonstrating the importance of non-IFN STING responses of late as well as much evidence from SAVI mice to suggest some non-IFN driven pathologies.
• Discussion: Is there any evidence from the human SAVI patients of neuroinflammation etc. This should be mentioned either way in the discussion.
• Discussion: There is a large body of work demonstrating STING-induced cell death in numerous cell types. Despite this it is not mentioned nor discussed but should be. It could represent how dopaminergic neurons are lost in the STING ki mice.
• The resolution/quality of some of the imaging is not great but this may be due to PDF compression.

Significance

• The findings represent a conceptual advance in the field by placing STING as a central mediator in neurological immune dysregulation. This work is of note as it provides evidence of a direct role for STING activity in neuroinflammation which has been otherwise implicated via genetic depletion in other studies in mouse models of PD and ALS.
• This manuscript is of particular interest to researchers in the innate immunity/immunology fields, neuroinflammation and far beyond due to the enormous attention currently surrounding the cGAS-STING pathway in disease and the rationale design of STING agonists and inhibitors aimed at improving outcomes in numerous inflammatory disease pathologies.
• 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.
  • I have over ten years' experience in the innate immunity field. Most relevant to this manuscript, I have a strong research program on STING and have an excellent molecular understanding of the pathway as well as the literature surrounding cGAS-STING in disease pathology. I have a basic understanding of neuroinflammation but am by no means an expert in that area. Hence, I cannot fully assess if the authors have used the best methods to make their conclusions.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

In this paper by the Vagner lab, co-transcriptional cleavage (CoTC) is discovered as a mechanism to ensure 3'-end processing of selected genes under conditions of global inhibition of 3'-end processing under DNA damage conditions.

While global inhibition of 3'-end processing acts as a fail-safe mechanism to ensure that mutations arising from DNA damage are not propagated (and instead repaired), the expression of repair genes must be maintained under these conditions. In an elegant serious of experiments, Sfaxi and coauthors have identified CoTC as a mechanism, which allows specific pre-mRNAs to escape 3'-end processing inhibition in response to UV-induced DNA damage.

This is an important discovery, the article reads well and most of the experiments are technically sound. That having said, I think the authors did not 'sell' this important finding very well. While they initially started their studies based on processing of the p53 pre-mRNA, they later performed RNAseq (Figure 5&6) to identify further genes that are regulated in a CoTC-dependent manner - analogous to the p53 pre-mRNA. In doing so, the authors identify and validate further CoTC-dependent genes. Given the global RNAseq approach that the authors have undertaken but not yet fully exhausted, there are probably more genes hidden that are processed in a similar way.

I would recommend harvesting the hidden treasure to more comprehensively understand CoTC-dependent processing and its relation to DNA damage conditions. In my opinion, it would be important to perform

1. GO enrichment analyses of the 108 pre-mRNAs more effectively processed under UV and address the question whether DNA damage repair-related terms can be retrieved
2. study of further DNA-damaging conditions to address the question if similar patterns and genes can be retrieved under these conditions
3. complementary analysis of data derived from tumor genome databases whether mutations in the identified CoTC-sites are enriched (which one would expect)

Finally I wonder, whether a small scheme illustrating conventional versus CoTC processing could enhance access for a broader readership.

Minor Comments:

Page 4, 2nd paragraph, last sentence: what is "vcxPAS"?

Page 6, 2nd paragraph, the TBP RNA is not explained.

Page 6, 2nd paragraph and following paragraphs. The PCF11-depletion experiments to sort out conventional versus CoTC-dependence is not very well controlled: it is surprising to see that depletion of PCF11, which is already absent under UV (Fig. 1A), seems to modulate processing of TBP under this condition (Fig. 1E). In order to turn this into a bona fide positive control for the entire experimental set-up, it is relevant to show that there are residual PCF11-levels under UV that can be further downregulated by siRNAs under this condition (currently this is not supported by the WB data in Fig. 1B).

Page 8, 1st paragraph, last sentence: I find the reference to GAPDH and WDR13 as part of a figure that comes far below is a bit confusing

Page 9, last paragraph, page 10, 1st paragraph: What does the analysis of WDR12, GAPDH and TBP exactly control for?

Figure 3. Overall, I find the information shown in Fig. 3 somewhat confusing and wonder whether the quality can be improved (partial co-localization of spots, are the spots shown in D -UV an artifact? Etc.)

Figure 4. I find the composition of panels C and D not very intuitive (I would reorganize the data such that each panel shows the RNA and protein expression data for each candidate individually (panel C for p53 and panel D for p21, respectively)

Figure 5, panel B: The figure shows that the by far largest number of genes (>3000/3722) is not differentially regulated under UV compared to no-UV conditions. Does this question the commonly made statement that 3'-end processing is globally inhibited under UV quoted here (page 14, 2nd paragraph) and elsewhere?

Referees cross-commenting

@reviewer 1 & 3: I fully agree; the PCF11 depletion under UV-conditions is clearly visible. Thank you!

Significance

This is an important study to better understand the function and target genes of CoTC-mediated 3'-end processing. It thereby extends earlier studies mainly adressing the underlying molecular mechanisms and rationalizes the function (and evolution) of this gene regulatory principle.

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Referee #2

Evidence, reproducibility and clarity

DNA damage leads to transient inhibition of 3' end processing and a marked reduction of cellular Pcf11 levels, a component of the cleavage factor II (CF II). In previous work, St¬ephan Vagner and colleagues described that p53 mRNA escapes the 3' end processing inhibition through the actions of the DHX36 RNA-helicase and the heterogenous RNA binding protein hnRNP H/F. However, this previous work failed to identify a mechanism through which DHX36 and hnRNP H/F would mediate the escape. In this work Stephane Vagner and his colleagues describe now how a sequence located 1200 nt downstream of the P53 poly(A) signal (PAS) is required to alleviate p53 mRNA from the general DNA-damage-dependent 3' end processing block. The presence of this element makes p53 mRNA 3' end processing independent from CTD-serine-2-phosphorylation and the CFII factor Pcf 11. As a high proportion of non-cleaved p53 pre-mRNA can be found in the nucleoplasm, the authors suggest that this element may be a co-transcriptional cleavage inducing site (CoTC). Deletion of this element renders p53 mRNA susceptible to DNA-damage-induced 3' end processing inhibition and leads to a p53 protein reduction after UV-exposure. Consequently, expression of down-stream targets of p53 is also reduced. The authors identify 9 more candidates for CoTC in other genes encoding for proteins required for the DNA-damage response.

Major points:

Although Figures 4 and S7 clearly show how long the RNA is that is retained on the chromatin, it is not clear, how long the RNA is that is released into the nucleoplasm. A Co-TC mechanism would pose that either nucleoplasmic CPSF-mediated cleavage and/or nucleoplasmic exonucleolytic degradation preceded nucleoplasmic polyadenylation. Neither of these points has been addressed by the current manuscript. This could be addressed by transcript reverse transcription analysis with nuclear RNA, in the background of an exosome ko to see if this would allow stabilisation of the un-cleaved RNA and its detection in the nucleoplasmic fraction.

Minor points:

It would be good if the site of action of DHX36 and hnRNP H/F could be repeated and put into context with the Co-TC element.

Introduction; I feel the pause-type termination is probably better explained in either Cortazar et al 2019 or Gromak et al 2006.

There may be a typo towards the end of the second paragraph: vcxPAS. If this is not a typo, it would be helpful to have this explained better.

Figure 1A/B the conclusion: "These observations suggest that PCF11 might be dispensable for pre-mRNA 3' end processing following UV-induced DNA damage" is in contradiction to the general 3' end processing defect following DNA-damage that the authors cite. This statement is only understandable with the prior knowledge of p53 mRNA being able to escape this inhibition. I feel it would be helpful to rephrase this.

Figure 1 E): shifting the entire axis up, is to my reading counterintuitive. I would show all graphs at the same scale.

Williamson et al (Svejstrup) 2017 showed through DRB-washed PRO-seq profiles that Pol II elongation speed is reduced for at least 8 hrs following UV-exposure, resulting in depletion from Pol II in gene bodies and concentration towards the gene beginnings (transcript start sites, TSS). It would be helpful to have an idea how the transcriptional profile looks on p53 at the time point of analysis - and at which time point after DNA-damage insult the 3' end processing inhibition starts. Such study could also form the beginning of a more in-depth analysis on how the CoTC is mediated. Such an in-depth analysis should also probe the chromatin crosslinking of RNA Pol II, as well as 3' end factors at the regular PAS and downstream Co-TC element. The fact that the smFISH shows signal for the downstream probes of Rad53, suggests that Pol II regularly transcribes to these positions. Could there be another PAS-dependent termination signal in further downstrea areas?

Figure 5) the sequencing procedure should be explained better in the main text. From the text it is not clear, what sort of sequencing was performed.

Referees cross-commenting

@ Reviewer #1:

Generally agree with Reviewer 1. 2) Figure 3B : I agree that this experiment would benefit from better description. In fact, wouldnt one expect to be there signal in Figure 3D after UV, since cleavage is inhibited? Unless Williamson et al is taken into account, showing that transcription is generally slowed.

@ Reviewer #3:

Generally find all these suggestions are very valid and would increase the value of the manuscript. I am not sure if I understand correctly/agree with two comments:

If understood correctly, this reviewer suggests that there is no Pcf11 under UV treatment conditions as suggested in Figure 1A. However, Figure 1B might show a longer Western Blot exposure or have more material loaded, showing that there is some Pcf11 available for si-mediated knockdown.

Figure 5 Panel B. I would agree that this panel is not very well explained. My interpretation so far has been in quartiles (left top, less cleaved, less total; top right less cleaved, more total upon UV versus bottom left more cleaved, downregulated and bottom right more cleaved upreagulated upon UV). In which case a significant number of transcripts is no cleaved upon UV. To help with interpretation at least a longer legend could be added.

Significance

This manuscript is overall convincing and adds more gravitas to the highly debated observation of co-transcriptional cleavage events. Although this study is by no means mechanistically exhaustive, it shows that the proposed mechanism may be true for the genes of DNA-damage repair factors that need to be "exempted" from the general DNA-damage-induced inhibition of 3' end cleavage. This opens up the exciting possibility that co-transcriptional elements can be used under specific, controlled environmental conditions. Although alternative explanations are possible to explain these pre-mRNA's release from the chromatin, 3' end processing at the regular poly(A) signal is for these RNAs clearly inhibited.

For a complete classification as Co-TC element however, additional experiments would be required. I am not adding these to the major or minor points, as these in my eyes would constitute a new story. The original literature on CoTC (West et al 2004, Teixeira et al 2004), posed that a Co-TC event provides a 5'phospho entry site that could be used by a molecular torpedo (Xrn2). Part of the controversy about Co-TC cleavage is the question of how such a 5'phospho-end could chemically be generated by autocatalytic cleavage. To substantiate the claim that these elements are indeed Co-TC cleavage events either generated by auto-catalytic cleavage or another enzymatic function, the authors should test if they promote termination in this homologous, as well as a heterologous context.

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Referee #1

Evidence, reproducibility and clarity

Sfaxi et al., significantly extended a current knowledge of the mechanism and the function of co-transcriptional RNA cleavage (CoTC). First, the authors focused on TP53 genes to study the CoTC. They showed TP53 transcripts are cleaved independently of PCF11 and Pol II CTD Ser2 phosphorylation in the UV-treated cells, concluding RNA cleavage at polyadenylation site (PAS) of the TP53 gene occurs post-transcriptionally. This strongly suggests that TP53 gene transcription termination is regulated by CoTC. They also showed a biological importance of the CoTC on TP53 gene expression. Depletion of the potential TP53 CoTC genomic region impaired mRNA and protein levels of p53 and its target p21. This deregulated G1-S phase progression in cell cycle following UV treatment. Finally they extended these findings to other genes by the novel screening approach of the CoTC.

Minor comments:

1. P4, Second paragraph, Another model~; Two more papers need to be cited. "Dye and Proudfoot 2001 Cell" "West et al., 2008 Mol Cell"
2. Figure 3B; The authors should explain more about foci detected by probes A and B.
3. P10, Last line, strong decrease~; (Figures 4E and ~) -> (Figure 4E, right panels, and~)
4. Figure 5C; The author should show the entire image of the RNA-seq reads in the gene region, but not just in the windows described in Figure 5A. Also, TP53 and GAPDH genes need to be shown for the controls.

Referees cross-commenting

I totally agree with Reviewer #2.

Significance

Overall this paper is well described and written. In my view, this will bring important information to the transcription termination field.

Note, I am not sure that the authors need to include the generality of the CoTC in Figures 5 and 6 since their RNA-seq analysis and its validation for biological functions are incomplete. Therefore I feel that focusing on the TP53 gene may enhance the impact of this paper.

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Reply to the reviewers

Manuscript number: RC-2022-01481R

Corresponding author(s): Sebastian Voigt. Mirko Trilling, David Schwefel

1. General Statements [optional]

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2. Description of the planned revisions

Reviewer #1: Evidence, reproducibility and clarity

Using proteome profiling of rat CMV infected cells, the authors of this study identify the E27 protein of rat cytomegalovirus as being crucial for proteasomal degradation of STAT2. Since E27 shares 56% sequence identity to the previously characterized STAT2 antagonist M27 of murine CMV the authors investigated association of E27 with the Cullin4-RING UbL CRL4. Using gel filtration chromatography they provide evidence that E27 forms a stable ternary complex with DDB1 and STAT2 suggesting that E27 bridges STAT2 to DDB1 which is further corroborated by data from cross-linking mass spectrometry. A cross-linked DDB1/DDA1/E27/STAT2 complex was then used for cryo-EM imaging experiments. The subsequent single particle analysis yielded a density map at 3.8 A resolution that was further used to generate an E27 molecular model. At this point it should be noted that resolution was not very high and data form AlphaFold2 prediction and CLMS experiments were necessary to build a model which was described as having "sufficient quality", however, no quality parameters are included for this model. In this model, a cryptic zinc-binding motif was identified that turned out to be well conserved in M27. At this point the study switches to a mutational analysis of M27: MCMV mutants either lacking M27 or bearing an AxAxxAA triple mutation were investigated both in cell culture and in animal models. Surprisingly, the M27-AxAxxA mutant while exhibiting attenuated IFN inhibition was still more active than an M27 deletion mutant. Later during the study it is postulated that this may be due to the fact that E27 binding to STAT2 abrogates the interaction with IRF9, however, this is only predicted from modeling and no experimental data are provided for this hypothesis. Furthermore, modeling approaches were used to predict how E27 replaces endogenous CRL4 substrate receptors and how E27 recruits STAT2 to mediate CRL4-catalysed ubiquitin transfer.

Reviewer #1: Significance

__Reviewer #1: __This is an interesting and well written paper describing for the first time in molecular detail how a cytomegalovirus-encoded interferon antagonist degrades STAT2 by mimicking the molecular surface properties of cellular CRL4 substrate receptors.

This study should be of broad interest for both virologists and structural biologists.

Authors Response: We thank the reviewer for the insightful and constructive evaluation. We are very grateful for highlighting the significance of our work.

Reviewer #1: Major points

__Reviewer #1: __To my opinion the authors should perform mutational analysis in the context of E27 and RCMV. I accept that switching to M27 may be easier due to established procedures for MCMV mutagenesis and analysis, however, since all structural work is primarily done on E27 it would be consequent to confirm these structural predictions in the context of E27 before switching to a related protein.

Authors Response: As the Reviewer appreciated, there were multiple reasons for the switch from RCMV-E E27 to MCMV M27. Most importantly, the MCMV in vivo infection model in mice is very well-established. Please also note that MCMV is applied far more often by virologists and immunologist as a standard model. Thus, the extension of our findings from RCMV to MCMV increases the relevance and outreach of the study. By performing the experiments in the MCMV context, we also aimed to emphasise that the function of the zinc-binding motif, which structurally organises the DDB1-binding domain, is functionally conserved among E27/M27-like proteins. Obviously, Reviewer #1 could ask why we do not solve the structure of M27 parallel to E27. With the sole exception of E27, none of the rodent M27 homologues could be produced recombinantly in a soluble form, preventing the purification and structure analysis of M27.

Since we agree with Reviewer #1 that the extension from E27 to M27 may read “a bit rough” without a mutational analysis in the E27 context, we will construct RCMV-E E27 mutants leading to Cys=>Ala exchanges in the Zn-binding motif. An analysis of the interaction between DDB1 and these E27 mutants will be included in the revised manuscript.

__Reviewer #1: __Moreover, data on the replication of the generated E27 deletion RCMV should be included in the manuscript (i.e. growth curves).

Authors Response: RCMV mutants lacking the E27 gene exhibit an impaired replication. According to the suggestion, the growth curves will be part of the revised manuscript.

Reviewer #1: The hypothesis that STAT2/E27 interaction is sterically incompatible with IRF9 binding is only based on structural prediction. It would help if the authors could present experimental evidence for such a mechanism.

Authors Response: The hypothesis is based on three lines of argumentation: (i) structural data regarding the binding interface between STAT2 and E27 covering the known STAT2-IRF9 interface (Fig. 7F) (Rengachari et al., 2018). (ii) The finding that M27 mutants incapable to bind DDB1 and induce STAT2 degradation along the ubiquitin proteasome pathway retain a residual capacity to inhibit ISRE signaling, suggesting that the binding of M27 to STAT2 suffices to elicit some signaling inhibitory functions (Fig. 7G). (iii) To elicit their function, CRL4 substrate receptors such as E27 interact with two partners. As we discussed elsewhere (Le-Trilling and Trilling, 2020), a simultaneous development of two independent traits violates evolutionary and probability theories. Thus, these receptors must acquire their binding interfaces sequentially, and the first interaction must provide an evolutionary advantage allowing the fixation of the allele in the population. Afterwards, the second binding interface evolves. Thus, a hypothesis in which E27/M27 precursors evolved the capacity to bind STAT2, preventing its association with IRF9 thereby establishing relevant but incomplete IFN inhibition (before the DDB1 interface was invented leading to STAT2 degradation by the proteasome), provides a parsimonious explanation for all these findings without violating evolutionary constraints. To corroborate our argumentation, we will analyse if E27 indeed displaces IRF9 from STAT2 by analytical gel filtration and/or co-immunoprecipitation experiments.

Reviewer #2: Evidence, reproducibility and clarity

__Reviewer #2: __The manuscript entitled "Structure and mechanism of a novel cytomegaloviral DCAF mediating interferon antagonism" by Dr. Schwefel and colleagues cleverly combines biochemistry, mass-spectrometry, Cryo-EM and cell biology to dissect how RCMV-E hijacks its hosts ubiquitylation machinery to mediate proteasomal degradation of STAT2, a key player driving the antiviral IFN response. They identify E27 as DDB1-binding element, which is able promote CRL4-dependent ubiquitylation of STAT2, and demonstrate its effect on STAT2 levels by knockout RCMV-E strains. These findings are supported by in vitro reconstitution of the DDB1/E27/STAT2 complex and analyses via XL-MS and Cryo-EM. The obtained data are then powerfully validated and analysed in mutational strains via infection of homologue in vivo models. The results collectively explain how E27 mimics endogenous CRL4 substrate receptors, thereby recruiting STAT2 to be targeted by CLR4 for ubiquitylation in a NEDD8-dependent manner.

Overall this is an important study that provides convincing insights on how rodent CMVs antagonize their host interferon response by exploiting its ubiquitin-proteasome system.

The manuscript is well written and its introduction is extraordinarily comprehensive. There are a few minor points for the authors to consider below.

Authors Response: We thank the reviewer for this very positive assessment.

Reviewer #2: Significance

Reviewer #2: The work of Schwefel and colleagues combines several powerful state-of-the art techniques to dissect the mechanism of the viral protein E27 and, for the first time, provides a rational for its ability to act as STAT2 antagonist. They performed outstanding structure-function analyses of the ubiquitin system, including the first global proteomic profiling of RCMV-infected cells, setting the standard for its human counterpart as rodent CMVs are commonly used as infection models. The manuscript is highly suitable for publication in any of the journals associated with the review commons platform.

Authors Response: Again, we thank the reviewer for these kind words and the appreciation of our work.

Reviewer #2: CROSS-CONSULTATION COMMENTS

Reviewer #2: This reviewer agrees that at least testing mutants in the E27 in some assays would be appropriate.

Authors Response: As detailed in the response to Reviewer #1, we will generate RCMV-E E27 mutants targeting the Zn-binding motif by site-directed mutagenesis. An analysis of the interaction between DDB1 and these E27 mutants will be included in the revised manuscript.

Reviewer #3: Evidence, reproducibility and clarity

__Reviewer #3: __Le-Trilling et al. present the first proteomic analysis of RCMV-infected cells, where they identified STAT2 as one of the most heavily downregulated (and degraded) proteins. This analysis showed that RCMV mediated degradation of STAT2 is conserved in closely related species used as animal models (rat and mouse) and human, despite the intra-host adaptation of each CMV. They also identify E27 as the RCMV factor that targets STAT2 for degradation, that exhibits ~50% homology with MCMV pM27. This study also identifies a Zinc binding motif in E27 using Cryo-EM which is conserved in other CMV species and is potentially involved in antagonising Type I and III responses.

Reviewer #3: Significance

__Reviewer #3: __The present work provides the first proteomics analysis of RCMV infection in rat cells, comparing infected vs non-infected rat fibroblasts to access potential RCMV targets. Then, it focuses on the characterisation of RCMV E27 and its role targeting and interacting with STAT2 (plus recruiting the Cul4 complex for STAT2 degradation). Finally, it provides the Cryo-EM structure of E27 and its CMV homologues, and the structure of the complex of E27 with elements of the CUL4 complex and STAT2. This is the first time that E27 function and structure are characterised. These are all novel findings - although the mouse homologue M27 has previously been found to interact with and degrade STAT2 (published by some of the same authors in Plos pathogens in 2011, (https://doi.org/10.1371/journal.ppat.1002069). Therefore the chief novel information is the structural studies.

The manuscript will be of interest to researchers working with human and animal herpesviruses.

My field of expertise is in Virology, Innate Immunity and host-virus interactions from an evolutionary perspective. I do not have expertise in Cryo-EM, so I could not evaluate the methods used in the section.

__Authors Response: __We thank the reviewer for the positive evaluation of our work and its significance.

Reviewer #3: Major points

__Reviewer #3: __1. The authors claim the identification of a Zinc-binding motif in the protein E27 (RCMV) using Cryo-EM, then validation of the phenotype with MCMV WT, delM27 and M27 AxAxxA. To justify the change to MCMV to perform the functional validation, they stated "MCMV M27, the closest E27 homologue, exhibits 56% and 76% amino acid sequence identity and similarity, respectively (Fig. S4B). E27 and M27 AlphaFold2 structure predictions are almost indistinguishable (RMSD of 1.195 Å, 6652 aligned atoms) (Figs. 3B, S4A), and structural alignment of these predictions demonstrated conservation of side chain positions involved in zinc-binding (Fig. 3C). Thus, M27 represents a valid model to study functional consequences of interference with the zinc coordination motif through site-directed mutagenesis, and to test the predictive power of our E27/M27 model". Although they rationalise the change to MCMV to validate the functional outcomes of the newly identified zinc binding motif with alignments and Cryo-EM data, it falls within the DDB1 binding region that is less conserved (Fig S4B). The addition of a mouse model here provides a solid result but given the aim of the paper is to provide a proper characterisation of RCMV and elucidate some inter-species adaptations, I strongly recommend the validation with E27 here given the potential impact of this motif. Rather than having to repeat this in a rat model (which would clearly be a large amount of work), this could simply be achieved by constructing the relevant deletion / mutant viruses and assessing in vitro in a relevant cell line (readout - either virus titre or luciferase assay as shown in Figure 3G/H).

__Authors Response: __Please also see our responses to the other reviewers. Briefly, we will apply side-directed mutagenesis to alter the CxCxxC motif in E27 that binds the zinc ion, and analyse the interaction of these E27 mutants with DDB1. In this context, we would like to add that almost two thirds of E27 residues in direct contact with DDB1 are at least type-conserved in M27, and the zinc-coordinating side chains are totally conserved (Fig. 3C). Together with a predicted similar structural organization of the respective binding regions (Fig. S11), and in light of our MCMV mutagenesis results (Fig. 7), it is highly likely that the DDB1-binding mode is conserved between E27 and M27. As mentioned above, we will put this assumption to the test in the revision process.

__Reviewer #3: __Furthermore, in Figure 2, the GF assay was performed using full-length DDB1, however CLMS was performed using DDB1 delBPB (interchange between these two proteins continues in the remainder of the paper). This should be at least justified, and preferably one or other of wt DDB1 and DDB1 delBPB used in the GF or CLMS assay where this has not yet been performed. Later on in the results section (Fig 5E), the authors use wt DDB1 while in fig 4 they used the delBPB to describe the interaction with E27 - would be relevant to have consistency across the paper and some supplementary data that could support using one or the other in each assay.

__Authors Response: __Protein complex preparations including full length DDB1 did not yield cryo-EM reconstructions at appropriate resolution for model building, almost certainly due to the known flexibility of the DDB1 BPB, impeding proper alignment of the cryo-EM particle images. This is why we switched to DDB1ΔBPB. Importantly, the structure model including full length DDB1 (Fig. S12B) clearly demonstrates that the BPB is located on the opposite side of the E27 binding interface on DDB1 (where it is situated to flexibly connect to the CUL4 scaffold to create the ubiquitination zone around immobilised substrates [Fig. 6]). This rules out an involvement of DDB1 BPB in E27- and/or STAT2-binding processes. Several previous studies have employed DDB1ΔBPB to facilitate structure determination, and have successfully applied the resulting structural models for functional follow-up experiments in the context of complete CRL4 assemblies (Bussiere et al., 2020; Petzold et al., 2016; Slabicki et al., 2020). Nevertheless, we will repeat GF experiments with DDB1ΔBPB for consistency and include these data in the revised manuscript.

Reviewer #3: Minor points

__Reviewer #3: __2. Although they present sufficient detail in the methods, further details in the text should be given as to the number of repeats performed in each case, and whether the data shown is representative or based on an average of repeats (preferably the latter; if representative, the data for other repeats should be shown in supplementary information).

Authors Response: We will add this information in the revised version of the manuscript.

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

Reviewer #1: Major points

__Reviewer #1: __Resolution of the cryoEM structure is rather low and many predictions of the manuscript are based on modeling using AlphaFold2 prediction. The authors describe their model as of "sufficient quality", however, no quality measures are included in the manuscript. At least the discussion should address limitations of the used approach.

Authors Response: While we apologize for not sufficiently describing our quality measures, we respectfully disagree regarding the conclusion. Our resolution (3.8 Å, map 1) lies well within the 3–4 Å resolution range of the vast majority of structures deposited to the Electron Microscopy Data Bank during the last five years (https://www.emdataresource.org/statistics.html). Nevertheless, de novo modelling in this resolution regime is challenging. This is why we sought additional guidance through cross-linking mass spectrometry (XL-MS) restraints and AlphaFold2. Please also note that modelling of E27 was not based solely on the AlphaFold2 prediction. Instead, a partial model corresponding to the α-domain was manually built in map 1, guided by XL-MS information (see Methods - “Model building and refinement” and Fig. S5B, grey cartoon). This partial model proved to be in very good agreement with AlphaFold2 predictions (RMSD of 1.489 Å, 2764 aligned atoms). Only after this initial sanity check, the computational prediction was used for model completion, adjustment, and refinement.

We now added graphical overviews of model fits in Figs. S5 and S10. Furthermore, we included detailed views of the fit of relevant side chains involved in intermolecular interaction to the experimental density (Fig. S7, S9). We also calculated and listed quality indicators of the model-to-map fit in Table S1 (correlation coefficients and model resolution based upon model-map FSC). To ensure the validity of our atomic model using an alternative method besides cryo-EM and XL-MS, we have performed site-directed mutagenesis of critical binding regions in E27, followed by in vitro reconstitution and analytical GF (Fig. S7B, C, S9B, C). The text was revised accordingly (see p10 [ll22] and p14 [ll26]).

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__Reviewer #1: __The authors identify a cryptic zinc-binding motif in E27 that is conserved in homologous proteins. For this reviewer it is not clear: is there experimental evidence for zinc binding of E27 or can the presence of zinc reliably be detected in their structural data? If not, it would be worth to confirm zinc binding.

Authors Response: Our structural data show a tetragonal metal coordination geometry, involving three cysteine side chains and one histidine side chain, with coordination bond lengths of 2.2 Å between the histidine nitrogen and the metal ion, and of 2.4 Å between the cysteine sulfurs and the metal ion. The density feature cannot be explained by another type of side chain interaction, e.g. a disulfide bond, because this would lead to a steric clash with the remaining adjacent side chains. Based on the knowledge on metal-binding sites in proteins and metal-coordination chemistry, these characteristics indicate the presence of a structural zinc-binding site for the following reasons: (i) after magnesium, zinc is the second most prevalent metal in the Protein Data Bank (https://metalpdb.cerm.unifi.it/getSummary), however, magnesium is coordinated octahedrally by oxygen ligands (Tang and Yang, 2013); (ii) the most abundant zinc ligands are cysteine and histidine; (iii) the most abundant zinc coordination number is four ligands; (iv) the average coordination bond lengths are 2.12±0.19 Å and 2.33±0.12Å for nitrogen-zinc and sulfur-zinc interactions, respectively (Ireland and Martin, 2019; Laitaoja et al., 2013), which is in very good agreement with our structural observations. We included this argumentation in the revised manuscript (see p9 [ll21]), and added Fig. S5C for visualization.

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Reviewer #2: Minor points

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Reviewer #2: Page 2, line 3. "Here," should be inserted before "Global proteome profiling..." to highlight the work of this manuscript.

Authors Response: We changed the text accordingly.

Reviewer #2: Page 3, line 21. "IFNs" instead of "IFN"

Authors Response: We changed the text accordingly.

Reviewer #2: Page 4, lines 9,15,27. "Ubiquitin Ligases (UbL)" is not a common abbreviation and could be mistaken for Ubl (Ubiquitin-like proteins). Possible abbreviation is "E3s" for Ubiquitin E3 ligases

Authors Response: We have amended the respective abbreviations accordingly.

Reviewer #2: Page 4 line 25. "RBX1" is the more common term for "ROC1"

Authors Response: This has been corrected throughout the manuscript.

Reviewer #2: Page 5 lines 1-9. Citing of the first structure of DDB1 in complex with a viral protein is recommended. (Ti Li et al. Cell 2006)

Authors Response: We thank the reviewer for this important suggestions and cited this landmark publication.

Reviewer #2: Figure 1 a) STAT2 dot is cut off in second panel. I recommend highlighting STAT2 in both panels.

We amended the figure accordingly. We furthermore additionally highlighted the “STAT2” text in both panels by increasing the font size and putting it in bold type.

Reviewer #2: Page 7 line 17. "Cross-linking MS (CLMS)" is commonly abbreviated as (XL-MS)

Authors Response: We changed the text accordingly.

Reviewer #2: Figure 2 a-c) These panels could benefit from thinner lines in order to increase visibility of chromatograms and cross-links.

Authors Response: The panels were changed accordingly.

Reviewer #2: Figure 2 a-b) Could the authors elaborate on why STAT2 is stoichiometrically

underrepresented in the SDS-PAGE of the E27/DDB1/STAT2 complex?

Authors Response: We applaud Reviewer #2 for their in-depth examination. Honestly, we were also puzzled by this. Based on the cryo-EM single particle analysis, we found an explanation: We separated a major contamination in silico during 2D classification (~12% of all particles). Out of curiosity, we reconstructed a density map from these particles (now shown in Fig. S3). The map was identical to a previous cryo-EM structure of the E. coli protein ArnA (Yang et al., 2019), a notorious contaminant in E. coli Ni-NTA protein purifications (Andersen et al., 2013). ArnA migrates similar to E27 on the SDS-PAGE, the band runs just a little bit faster (compare fraction 6 [ArnA] and fractions 8/9 [E27] from the SDS-PAGE of the analytical GF run of E27 in isolation, Fig. 2A, green trace). However, in analytical GF, ArnA elutes at higher molecular weight fractions, since it forms a hexamers (Ve~10.2 ml). Incidentally, this elution volume of the ArnA hexamer almost equals the one of DDB1 or DDB1ΔBPB/DDA1/E27/STAT2 complexes. This leads to a superposition of ArnA and E27 bands in the respective SDS-PAGE lanes corresponding to GF fraction 6. Accordingly, we conclude that it is actually not STAT2 that is underrepresented, but rather E27 seems overrepresented due to SDS-PAGE band overlap with the ArnA contaminant. We have now indicated the contaminant in Fig. 2A, amended the legend, and extended Fig. S3 to indicate at which point of the cryo-EM analysis the contaminating ArnA particles were separated, and to show the ArnA model to map fit.

In addition to this, it might be that potential STAT2 degradation products (marked by ** in Fig. 2), which seem to co-migrate with STAT2/E27 complexes, occupy FL STAT2 binding sites on E27.

Reviewer #2: Paragraph "The E27 structure.." page 9. Placing this paragraph after the overall

structure is recommended.

Authors Response: Accordingly, we have now moved this section to the end of the results section.

Reviewer #2: Figure 3 a) The grey mesh being laid over the ribbon structures is not contributing to the overall visibility. Adding a panel of the cryo-EM structure alone in cost of alphafold models is recommended.

Figure 4a) same issue with grey mesh

Authors Response: Thank you very much for the very good suggestions. We have removed the mesh representation, and included panels just showing the segmented cryo-EM map in the new Fig. 3A.

Reviewer #2: c) panels could benefit from fewer amino acids being labeled/shown

Authors Response: We understand the motives of the Reviewer. However, we would prefer to depict all relevant side chain interactions in these panels. The rearrangement of the figure, i.e. showing the overview of the interacting regions before the detailed panels, should make them more accessible (new Fig. 3B).

__Reviewer #2: __d) may want to avoid red-green coloring to improve for colorblindness

Authors Response: We are deeply sorry for our ignorance in this regard. We changed the colors accordingly (see new Fig. 3B, C).

__Reviewer #2: __Figure 6a) s.a grey mesh

Authors Response: We removed the mesh representations and included panels just showing the segmented cryo-EM density in the new Fig. 5C.

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Reviewer #2: CROSS-CONSULTATION COMMENTS

__Reviewer #2: __A 3.8 A overall resolution map and the approach to fitting may be suitable, but it is unclear from the authors' figures whether the side-chains shown in the figures are clearly visible in the map or if they are modeled by some other approach. Side chains should ideally be visible in the maps if shown in figures, and if not, close-ups of the corresponding regions of the maps should be shown with sufficient depthcue to allow the reader to gauge how the map corresponds to the model.

Authors Response: This is a crucial point. As mentioned in the response to Reviewer #1, major point 2, we have now included very detailed views of the fit of relevant side chains involved in intermolecular interaction to the experimental density (Fig. S7, S9).

__Reviewer #2: __Along these lines, the figures with the mesh maps do not clearly show how well the model fits the map. This needs to be clearly visible in figures, and ideally maps and models provided to reviewers in order for the reviewers to gauge the level of accuracy of the fit.

Authors Response: Please see our response to Reviewer #1, major point 2. Briefly, we have now included graphical overviews of model fits in Figs. S5 and S10. We also calculated and listed quality indicators of the model-to-map fit in Table S1 (correlation coefficients and model resolution based upon model-map FSC). To ensure the validity of our atomic model using an alternative method besides cryo-EM and XL-MS, we have performed site-directed mutagenesis of critical binding regions in E27, followed by in vitro reconstitution and analytical GF (Fig. S7B, C, S9B, C). The text was extended accordingly (see p10 [ll22] and p14 [ll26]).

__Reviewer #2: __At minimum, the authors have nicely assembled proteomics and cell biological data indicating that E27 hijacks CRL4 to turn over Stat2 in rat cells in a manner paralagous to M27 hijacking in mouse cells, biophysical/structural data for a model of a CUL4-DDB1-E27-Stat2 complex, and mutagenesis of a putative zinc binding site in M27.

I feel most of the issues raised by all 3 reviewers could be addressed in the text, with more clarity about the structural models, and better explanation for why the construct with proteins from various organisms were used for structural studies (the authors had made human DDB1 before, and it expressed well, and perhaps didn't consider to make from rat? Or this mixture expressed, purified best? Gave best quality EM data?).

Authors Response: We thank Reviewer #2 for her/his overall assessment. As mentioned in the two cross-consultation comments before, and in the response to Reviewer #1, major point 2, we strived to provide adequate measures allowing to judge the quality of our structural models in the present updated version of the manuscript. In addition, as indicated in the response to reviewer #3, major point 2, we have now added Fig. S12 and extended the Discussion to explain and justify the use of different protein constructs.

__Reviewer #2: __Also, the presentation of the zinc binding site should come after the overall structure. As for the use of MCMV to assess the role of the zinc binding site, placing this last in the text might allow this to flow better.

Authors Response: Thank you very much for this suggestion. The manuscript has been restructured as recommended: details of the zinc-binding motif and the MCMV assays are now shown in Fig. 7 and described in the text just before the Discussion.

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Reviewer #3: Major points

__Reviewer #3: __2. Given that previous data in mice showed that the E27 homologue pM27 binds a component of host Cullin4-RING UbLs (CRL4), to induce the poly-ubiquitination of STAT2, the current study also addressed if this mechanism was preserved in RCMV. Yet, they seemed to do this with E27, rnSTAT2 and hsDDB1 - Page 7 lines 1 to 3: "These results prompted us to explore the association of E27 with Rattus norvegicus (rn) STAT2 and Homo sapiens (hs) DDB1 in vitro. Importantly, 1128 of 1140 amino acids are identical between hsDDB1 and rnDDB1 (...)". They identify the residues and regions where the DDB1 is different between both species, but should provide a structure/alignment with this highlighted. In addition, DDB1 is a DNA damage protein that is annotated in the Rattus norvegicus genome. The authors should justify the assays between rnSTAT2-hsDDB1 instead of using the both proteins from rn, and present the equivalent data for rnDDB1 in the paper.

Authors Response: Among the 12 alterations between human and rat DDB1, 4 are type-conserved (Fig. S12A). Thus, >99% of amino acids are identical or similar. We mapped all exchanges on a model of full length human DDB1 bound to E27 and the rat STAT2 CCD. None are involved in intermolecular interactions (Fig. S12B, C). Please note that due to the high conservation of DDB1 across eukaryotes, this inter-species approach has been used by us and others to study DDB1-containing complexes (e.g., the SV5V, WHX, SIV Vpx and Vpr, zebrafish DDB2, and chicken CRBN proteins have been in vitro reconstituted with human DDB1 for structural characterisation) and valid biological conclusions have been drawn from these studies (Angers et al., 2006; Banchenko et al., 2021; Fischer et al., 2014; Fischer et al., 2011; Li et al., 2006; Li et al., 2010; Schwefel et al., 2015; Schwefel et al., 2014; Wu et al., 2015).

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Reviewer #3: Minor points

__Reviewer #3: __1. In fig 5D, the authors present the H-box alignment, where it is clear that this motif is not conserved. The lack of H-box conservation should be discussed in the results and discussion, to provide an explanation for the competition/binding observed.

Authors Response: We respectfully disagree. There is conservation of amino acid side chains, regarding their physicochemical properties, observable in the H-box motif. Furthermore, the secondary structure is conserved. Please note, that the H-box is not our invention but rather represented a well-accepted motif known in the field, see e.g., (Li et al., 2010). We extended the discussion to cover this point (p21 [ll15]).

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__Reviewer #3: __3. The authors commence their abstract justifying the study on the grounds of the usefulness of rodent HCMV counterparts as common infection models for HCMV. They should return to this theme in the discussion - what is the usefulness of their findings with regards to HCMV (particularly given the relatively low homology between E27 and HCMV pUL27, and the alternative mechanism for STAT2 antagonism encoded by HCMV UL145)?

Authors Response: We extended the discussion in this regard. Briefly, our data, to our knowledge for the first time, reveal that RCMV (like MCMV) exploits CRL4 to induce proteasomal degradation of STAT2. With pUL145, HCMV relies on an analogous protein. In clear contrast to HCMV, RMCV and MCMV are both amenable to in vivo experiments in small animal models. Over 40 years ago, HCMV has been called the troll of transplantation due to its grim impact on immunosuppressed individuals after transplantation surgery (Balfour, 1979). Despite tremendous efforts, HCMV still harms and kills graft recipients. While MCMV allows various experiments regarding general principles of cytomegaloviral pathogenesis and antiviral immunity, one shortcoming is that the mouse obviously is a rather small animal, preventing various chirurgical and solid organ transplantation (SOT) procedures. In clear contrast, SOT procedures that are indispensable for human medicine can be recapitulated in rat models. Thus, according to our opinion, our work lays the molecular foundation for future studies addressing the relevance of STAT2 and CMV-induced STAT2 degradation in rat SOT models.

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

-

• *

References

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Angers, S., Li, T., Yi, X., MacCoss, M.J., Moon, R.T., and Zheng, N. (2006). Molecular architecture and assembly of the DDB1-CUL4A ubiquitin ligase machinery. Nature 443, 590-593.

Balfour, H.H., Jr. (1979). Cytomegalovirus: the troll of transplantation. Arch Intern Med 139, 279-280.

Banchenko, S., Krupp, F., Gotthold, C., Burger, J., Graziadei, A., O'Reilly, F.J., Sinn, L., Ruda, O., Rappsilber, J., Spahn, C.M.T., et al. (2021). Structural insights into Cullin4-RING ubiquitin ligase remodelling by Vpr from simian immunodeficiency viruses. PLoS pathogens 17, e1009775.

Bussiere, D.E., Xie, L., Srinivas, H., Shu, W., Burke, A., Be, C., Zhao, J., Godbole, A., King, D., Karki, R.G., et al. (2020). Structural basis of indisulam-mediated RBM39 recruitment to DCAF15 E3 ligase complex. Nat Chem Biol 16, 15-23.

Fischer, E.S., Bohm, K., Lydeard, J.R., Yang, H., Stadler, M.B., Cavadini, S., Nagel, J., Serluca, F., Acker, V., Lingaraju, G.M., et al. (2014). Structure of the DDB1-CRBN E3 ubiquitin ligase in complex with thalidomide. Nature 512, 49-53.

Fischer, E.S., Scrima, A., Bohm, K., Matsumoto, S., Lingaraju, G.M., Faty, M., Yasuda, T., Cavadini, S., Wakasugi, M., Hanaoka, F., et al. (2011). The molecular basis of CRL4DDB2/CSA ubiquitin ligase architecture, targeting, and activation. Cell 147, 1024-1039.

Ireland, S.M., and Martin, A.C.R. (2019). ZincBind-the database of zinc binding sites. Database (Oxford) 2019.

Laitaoja, M., Valjakka, J., and Janis, J. (2013). Zinc coordination spheres in protein structures. Inorg Chem 52, 10983-10991.

Le-Trilling, V.T.K., and Trilling, M. (2020). Ub to no good: How cytomegaloviruses exploit the ubiquitin proteasome system. Virus Res 281, 197938.

Li, T., Chen, X., Garbutt, K.C., Zhou, P., and Zheng, N. (2006). Structure of DDB1 in complex with a paramyxovirus V protein: viral hijack of a propeller cluster in ubiquitin ligase. Cell 124, 105-117.

Li, T., Robert, E.I., van Breugel, P.C., Strubin, M., and Zheng, N. (2010). A promiscuous alpha-helical motif anchors viral hijackers and substrate receptors to the CUL4-DDB1 ubiquitin ligase machinery. Nature structural & molecular biology 17, 105-111.

Petzold, G., Fischer, E.S., and Thoma, N.H. (2016). Structural basis of lenalidomide-induced CK1alpha degradation by the CRL4(CRBN) ubiquitin ligase. Nature 532, 127-130.

Rengachari, S., Groiss, S., Devos, J.M., Caron, E., Grandvaux, N., and Panne, D. (2018). Structural basis of STAT2 recognition by IRF9 reveals molecular insights into ISGF3 function. Proceedings of the National Academy of Sciences of the United States of America 115, E601-E609.

Schwefel, D., Boucherit, V.C., Christodoulou, E., Walker, P.A., Stoye, J.P., Bishop, K.N., and Taylor, I.A. (2015). Molecular Determinants for Recognition of Divergent SAMHD1 Proteins by the Lentiviral Accessory Protein Vpx. Cell host & microbe 17, 489-499.

Schwefel, D., Groom, H.C., Boucherit, V.C., Christodoulou, E., Walker, P.A., Stoye, J.P., Bishop, K.N., and Taylor, I.A. (2014). Structural basis of lentiviral subversion of a cellular protein degradation pathway. Nature 505, 234-238.

Slabicki, M., Kozicka, Z., Petzold, G., Li, Y.D., Manojkumar, M., Bunker, R.D., Donovan, K.A., Sievers, Q.L., Koeppel, J., Suchyta, D., et al. (2020). The CDK inhibitor CR8 acts as a molecular glue degrader that depletes cyclin K. Nature 585, 293-297.

Tang, S., and Yang, J.J. (2013). Magnesium Binding Sites in Proteins. In Encyclopedia of Metalloproteins, R.H. Kretsinger, V.N. Uversky, and E.A. Permyakov, eds. (New York, NY: Springer New York), pp. 1243-1250.

Wu, Y., Koharudin, L.M., Mehrens, J., DeLucia, M., Byeon, C.H., Byeon, I.J., Calero, G., Ahn, J., and Gronenborn, A.M. (2015). Structural Basis of Clade-specific Engagement of SAMHD1 (Sterile alpha Motif and Histidine/Aspartate-containing Protein 1) Restriction Factors by Lentiviral Viral Protein X (Vpx) Virulence Factors. The Journal of biological chemistry 290, 17935-17945.

Yang, M., Chen, Y.S., Ichikawa, M., Calles-Garcia, D., Basu, K., Fakih, R., Bui, K.H., and Gehring, K. (2019). Cryo-electron microscopy structures of ArnA, a key enzyme for polymyxin resistance, revealed unexpected oligomerizations and domain movements. J Struct Biol 208, 43-50.

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Referee #3

Evidence, reproducibility and clarity

Le-Trilling et al. present the first proteomic analysis of RCMV-infected cells, where they identified STAT2 as one of the most heavily downregulated (and degraded) proteins. This analysis showed that RCMV mediated degradation of STAT2 is conserved in closely related species used as animal models (rat and mouse) and human, despite the intra-host adaptation of each CMV. They also identify E27 as the RCMV factor that targets STAT2 for degradation, that exhibits ~50% homology with MCMV pM27. This study also identifies a Zinc binding motif in E27 using Cryo-EM which is conserved in other CMV species and is potentially involved in antagonising Type I and III responses.

Major and minor concerns to be addressed:

Major points

1. The authors claim the identification of a Zinc-binding motif in the protein E27 (RCMV) using Cryo-EM, then validation of the phenotype with MCMV WT, delM27 and M27 AxAxxA. To justify the change to MCMV to perform the functional validation, they stated "MCMV M27, the closest E27 homologue, exhibits 56% and 76% amino acid sequence identity and similarity, respectively (Fig. S4B). E27 and M27 AlphaFold2 structure predictions are almost indistinguishable (RMSD of 1.195 Å, 6652 aligned atoms) (Figs. 3B, S4A), and structural alignment of these predictions demonstrated conservation of side chain positions involved in zinc-binding (Fig. 3C). Thus, M27 represents a valid model to study functional consequences of interference with the zinc coordination motif through site-directed mutagenesis, and to test the predictive power of our E27/M27 model". Although they rationalise the change to MCMV to validate the functional outcomes of the newly identified zinc binding motif with alignments and Cryo-EM data, it falls within the DDB1 binding region that is less conserved (Fig S4B). The addition of a mouse model here provides a solid result but given the aim of the paper is to provide a proper characterisation of RCMV and elucidate some inter-species adaptations, I strongly recommend the validation with E27 here given the potential impact of this motif. Rather than having to repeat this in a rat model (which would clearly be a large amount of work), this could simply be achieved by constructing the relevant deletion / mutant viruses and assessing in vitro in a relevant cell line (readout - either virus titre or luciferase assay as shown in Figure 3G/H).
2. Given that previous data in mice showed that the E27 homologue pM27 binds a component of host Cullin4-RING UbLs (CRL4), to induce the poly-ubiquitination of STAT2, the current study also addressed if this mechanism was preserved in RCMV. Yet, they seemed to do this with E27, rnSTAT2 and hsDDB1 - Page 7 lines 1 to 3: "These results prompted us to explore the association of E27 with Rattus norvegicus (rn) STAT2 and Homo sapiens (hs) DDB1 in vitro. Importantly, 1128 of 1140 amino acids are identical between hsDDB1 and rnDDB1 (...)". They identify the residues and regions where the DDB1 is different between both species, but should provide a structure/alignment with this highlighted. In addition, DDB1 is a DNA damage protein that is annotated in the Rattus norvegicus genome. The authors should justify the assays between rnSTAT2-hsDDB1 instead of using the both proteins from rn, and present the equivalent data for rnDDB1 in the paper. Furthermore, in Figure 2, the GF assay was performed using full-length DDB1, however CLMS was performed using DDB1 delBPB (interchange between these two proteins continues in the remainder of the paper). This should be at least justified, and preferably one or other of wt DDB1 and DDB1 delBPB used in the GF or CLMS assay where this has not yet been performed. Later on in the results section (Fig 5E), the authors use wt DDB1 while in fig 4 they used the delBPB to describe the interaction with E27 - would be relevant to have consistency across the paper and some supplementary data that could support using one or the other in each assay.

Minor points:

1. In fig 5D, the authors present the H-box alignment, where it is clear that this motif is not conserved. The lack of H-box conservation should be discussed in the results and discussion, to provide an explanation for the competition/binding observed.
2. Although they present sufficient detail in the methods, further details in the text should be given as to the number of repeats performed in each case, and whether the data shown is representative or based on an average of repeats (preferably the latter; if representative, the data for other repeats should be shown in supplementary information).
3. The authors commence their abstract justifying the study on the grounds of the usefulness of rodent HCMV counterparts as common infection models for HCMV. They should return to this theme in the discussion - what is the usefulness of their findings with regards to HCMV (particularly given the relatively low homology between E27 and HCMV pUL27, and the alternative mechanism for STAT2 antagonism encoded by HCMV UL145)?

Significance

The present work provides the first proteomics analysis of RCMV infection in rat cells, comparing infected vs non-infected rat fibroblasts to access potential RCMV targets. Then, it focuses on the characterisation of RCMV E27 and its role targeting and interacting with STAT2 (plus recruiting the Cul4 complex for STAT2 degradation). Finally, it provides the Cryo-EM structure of E27 and its CMV homologues, and the structure of the complex of E27 with elements of the CUL4 complex and STAT2. This is the first time that E27 function and structure are characterised. These are all novel findings - although the mouse homologue M27 has previously been found to interact with and degrade STAT2 (published by some of the same authors in Plos pathogens in 2011, (https://doi.org/10.1371/journal.ppat.1002069). Therefore the chief novel information is the structural studies.

The manuscript will be of interest to researchers working with human and animal herpesviruses.

My field of expertise is in Virology, Innate Immunity and host-virus interactions from an evolutionary perspective. I do not have expertise in Cryo-EM, so I could not evaluate the methods used in the section.

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Referee #2

Evidence, reproducibility and clarity

The manuscript entitled "Structure and mechanism of a novel cytomegaloviral DCAF mediating interferon antagonism" by Dr. Schwefel and colleagues cleverly combines biochemistry, mass-spectrometry, Cryo-EM and cell biology to dissect how RCMV-E hijacks its hosts ubiquitylation machinery to mediate proteasomal degradation of STAT2, a key player driving the antiviral IFN response. They identify E27 as DDB1-binding element, which is able promote CRL4-dependent ubiquitylation of STAT2, and demonstrate its effect on STAT2 levels by knockout RCMV-E strains. These findings are supported by in vitro reconstitution of the DDB1/E27/STAT2 complex and analyses via XL-MS and Cryo-EM. The obtained data are then powerfully validated and analysed in mutational strains via infection of homologue in vivo models. The results collectively explain how E27 mimics endogenous CRL4 substrate receptors, thereby recruiting STAT2 to be targeted by CLR4 for ubiquitylation in a NEDD8-dependent manner.

Overall this is an important study that provides convincing insights on how rodent CMVs antagonize their host interferon response by exploiting its ubiquitin-proteasome system. The manuscript is well written and its introduction is extraordinarily comprehensive. There are a few minor points for the authors to consider below.

Minor points:

Page 2, line 3. "Here," should be inserted before "Global proteome profiling..." to highlight the work of this manuscript.

Page 3, line 21. "IFNs" instead of "IFN"

Page 4, lines 9,15,27. "Ubiquitin Ligases (UbL)" is not a common abbreviation and could be mistaken for Ubl (Ubiquitin-like proteins). Possible abbreviation is "E3s" for Ubiquitin E3 ligases

Page 4 line 25. "RBX1" is the more common term for "ROC1"

Page 5 lines 1-9. Citing of the first structure of DDB1 in complex with a viral protein <br /> is recommended. (Ti Li et al. Cell 2006)

Figure 1 a) STAT2 dot is cut off in second panel. I recommend highlighting STAT2 <br /> in both panels.

Page 7 line 17. "Cross-linking MS (CLMS)" is commonly abbreviated as (XL-MS)

Figure 2 a-c) These panels could benefit from thinner lines in order to increase visibility of chromatograms and cross-links.

Figure 2 a-b) Could the authors elaborate on why STAT2 is stoichiometrically underrepresented in the SDS-PAGE of the E27/DDB1/STAT2 complex?

Paragraph "The E27 structure.." page 9. Placing this paragraph after the overall structure is recommended.

Figure 3 a) The grey mesh being laid over the ribbon structures is not contributing to the overall visibility. Adding a panel of the cryo-EM structure alone in cost of alphafold models is recommended.

Figure 4a) same issue with grey mesh c) panels could benefit from fewer amino acids being labeled/shown d) may want to avoid red-green coloring to improve for colorblindness

Figure 6a) s.a grey mesh

Referees cross-commenting

A 3.8 A overall resolution map and the approach to fitting may be suitable, but it is unclear from the authors' figures whether the side-chains shown in the figures are clearly visible in the map or if they are modeled by some other approach. Side chains should ideally be visible in the maps if shown in figures, and if not, close-ups of the corresponding regions of the maps should be shown with sufficient depthcue to allow the reader to gauge how the map corresponds to the model.

Along these lines, the figures with the mesh maps do not clearly show how well the model fits the map. This needs to be clearly visible in figures, and ideally maps and models provided to reviewers in order for the reviewers to gauge the level of accuracy of the fit.

At minimum, the authors have nicely assembled proteomics and cell biological data indicating that E27 hijacks CRL4 to turn over Stat2 in rat cells in a manner paralagous to M27 hijacking in mouse cells, biophysical/structural data for a model of a CUL4-DDB1-E27-Stat2 complex, and mutagenesis of a putative zinc binding site in M27.

I feel most of the issues raised by all 3 reviewers could be addressed in the text, with more clarity about the structural models, and better explanation for why the construct with proteins from various organisms were used for structural studies (the authors had made human DDB1 before, and it expressed well, and perhaps didn't consider to make from rat? Or this mixture expressed, purified best? Gave best quality EM data?). Also, the presentation of the zinc binding site should come after the overall structure.

As for the use of MCMV to assess the role of the zinc binding site, placing this last in the text might allow this to flow better. This reviewer agrees that at least testing mutants in the E27 in some assays would be appropriate.

Significance

The work of Schwefel and colleagues combines several powerful state-of-the art techniques to dissect the mechanism of the viral protein E27 and, for the first time, provides a rational for its ability to act as STAT2 antagonist. They performed outstanding structure-function analyses of the ubiquitin system, including the first global proteomic profiling of RCMV-infected cells, setting the standard for its human counterpart as rodent CMVs are commonly used as infection models. The manuscript is highly suitable for publication in any of the journals associated with the review commons platform.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Using proteome profiling of rat CMV infected cells, the authors of this study identify the E27 protein of rat cytomegalovirus as being crucial for proteasomal degradation of STAT2. Since E27 shares 56% sequence identity to the previously characterized STAT2 antagonist M27 of murine CMV the authors investigated association of E27 with the Cullin4-RING UbL CRL4. Using gel filtration chromatography they provide evidence that E27 forms a stable ternary complex with DDB1 and STAT2 suggesting that E27 bridges STAT2 to DDB1 which is further corroborated by data from cross-linking mass spectrometry. A cross-linked DDB1/DDA1/E27/STAT2 complex was then used for cryo-EM imaging experiments. The subsequent single particle analysis yielded a density map at 3.8 A resolution that was further used to generate an E27 molecular model. At this point it should be noted that resolution was not very high and data form AlphaFold2 prediction and CLMS experiments were necessary to build a model which was described as having "sufficient quality", however, no quality parameters are included for this model. In this model, a cryptic zinc-binding motif was identified that turned out to be well conserved in M27. At this point the study switches to a mutational analysis of M27: MCMV mutants either lacking M27 or bearing an AxAxxAA triple mutation were investigated both in cell culture and in animal models. Surprisingly, the M27-AxAxxA mutant while exhibiting attenuated IFN inhibition was still more active than an M27 deletion mutant. Later during the study it is postulated that this may be due to the fact that E27 binding to STAT2 abrogates the interaction with IRF9, however, this is only predicted from modeling and no experimental data are provided for this hypothesis. Furthermore, modeling approaches were used to predict how E27 replaces endogenous CRL4 substrate receptors and how E27 recruits STAT2 to mediate CRL4-catalysed ubiquitin transfer.

Major comments:

1. To my opinion the authors should perform mutational analysis in the context of E27 and RCMV. I accept that switching to M27 may be easier due to established procedures for MCMV mutagenesis and analysis, however, since all structural work is primarily done on E27 it would be consequent to confirm these structural predictions in the context of E27 before switching to a related protein. Moreover, data on the replication of the generated E27 deletion RCMV should be included in the manuscript (i.e. growth curves).
2. Resolution of the cryoEM structure is rather low and many predictions of the manuscript are based on modeling using AlphaFold2 prediction. The authors describe their model as of "sufficient quality", however, no quality measures are included in the manuscript. At least the discussion should address limitations of the used approach.
3. The authors identify a cryptic zinc-binding motif in E27 that is conserved in homologous proteins. For this reviewer it is not clear: is there experimental evidence for zinc binding of E27 or can the presence of zinc reliably be detected in their structural data? If not, it would be worth to confirm zinc binding.
4. The hypothesis that STAT2/E27 interaction is sterically incompatible with IRF9 binding is only based on structural prediction. It would help if the authors could present experimental evidence for such a mechanism.

Significance

This is an interesting and well written paper describing for the first time in molecular detail how a cytomegalovirus-encoded interferon antagonist degrades STAT2 by mimicking the molecular surface properties of cellular CRL4 substrate receptors.

This study should be of broad interest for both virologists and structural biologists.

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Reply to the reviewers

Manuscript number: RC-2022-01528

Corresponding author(s): Elena Taverna and Tanja Vogel

1. General Statements [optional]

We thank the reviewers for the comments and points they raised. We think what we have been asked is a doable task for us and we are confident we will manage to address all points in a satisfactory manner.

2. Description of the planned revisions

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

Reviewer’s comment: The manuscript investigated the role of DOT1L during neurogenesis especially focusing on the earlier commitment from APs. Using tissue culture method with single-cell tracing, they found that the inhibition of DOT1L results in delamination of APs, and promotes neuronal differentiation. Furthermore, using single cell RNA-seq, they seek possible mechanisms and changes in cellular state, and found a new cellular state as a transient state. Among differentially expressed genes, they focused on microcephaly-related genes, and found possible links between epigenetic changes led by DOT1L inhibition and epigenetic inhibition by PRC2. Based on these findings, they suggested that DOT1L could regulate neural fate commitment through epigenetic regulation. Overall, it is well written and possible links from epigenetic to metabolic regulation are interesting. However, there are several issues across the manuscript.

Response to Reviewer and planned revision:

We thank the reviewer’s 1 for her/his comments and constructive criticism.

We hope the revision plan will address the points raised by the reviewer in a satisfactory manner.

Major issues:

* *Reviewer’s comment: 1) It is not clear whether the degree of H3K79 methylation (or other histones) changes during development, and whether DOT1L is responsible for those changes. It is necessary to show the changes in histone modifications as well as the levels of DOT1L from APs to BPs and neurons, and to what extent the treatment of EPZ change the degree of histone methylation.

Response to Reviewer and planned revision:

• As for the level of DOT1L protein We tried several commercially available antibodies, but they do not work in the mouse, even after multiple attempts and optimization. So, unfortunately we will not be able to provide this piece of information.

• As for the level of DOT1L mRNA We will provide info regarding the DOT1L mRNA level in APs, BPs and neurons by using scRNAseq data from E12, E14, E16 WT cerebral cortex.

• As for the levels of H3K79methylation, we did not intend to claim that the histone methylation is responsible for the reported fate transition. We will edit the text to avoid any possible confusion. If it is deemed to be necessary to address the point raised by the reviewer, we do have 3 options, that we here in order of priority and ease of execution from our side.

• immunofluorescence with an Ab against H3K79me2 using CON and EPZ-treated hemispheres.

• FACS sort APs, BPs and neurons from CON and EPZ-treated hemispheres, followed by immunoblot for H3K79me2 to assess the H3K79me2 levels. As for the FACS sorting, we will use a combinatorial sorting in the lab on either a TUBB3-GFP or a GFP-reporter line using EOMES-driven mouse lines. This strategy has already been employed in the lab by Florio et al., 2015 and we will use it with minor modifications.
• scCut&Tag for H3K79me2 from CON and EPZ-treated hemispheres. This option entails a collaboration with the Gonzalo Castelo-Branco lab in Sweden and might therefore require additional time to be established and carried out. Reviewer’s comment:

Furthermore, the study mainly used pharmacological bath application. DOT1L has anti-mitotic effect, thus it is not clear whether the effect is coming from the inhibition of transmethylation activity.

Response to Reviewer and planned revision:

In a previous work we used a genetic model (DOT1L KO mouse) that showed microcephaly (Franz et al. 2019). For this study, we wanted to fill a gap in knowledge by understating if the DOT1L effect was mediated by its enzymatic activity. For this reason, we choose to use the pharmacological inhibition with EPZ, whose effect on DOT1L activity has been extensively reported and documented in literature (EPZ is a drug currently in phase clinical 3 studies).

The stringent focus of this study on the pharmacological inhibition is thus a step toward understanding what specific roles DOT1L can play, both as scaffold or as enzyme.

Here, we concentrate on the enzymatic function and the scaffolding function is beyond the scope of this specific study. We can further discuss and elaborate on the rationale behind this in the revised manuscript.

Reviewer’s comment:

In addition, the study assumed that the effect of EPZ is cell autonomous. However, if EPZ treatment can change the metabolic state in a cell, it would be possible that observed effects was non-cell autonomous. It would be important to address if this effect is coming in a cell-autonomous manner by other means using focal shRNA-KD by IUE.

Response to Reviewer and planned revision:

We did not claim that the effect of EPZ is cell autonomous, we are actually open on this point, as we consider both explanations to be potentially valid. We will edit the text to avoid any possible confusion on what we assume and what not.

As a general consideration, it is entirely possible that the effects are non-cell autonomous. We will comment and elaborate on that in the revised manuscript.

If the reviewer/journal considers this a point that must be addressed experimentally, then we will proceed as follows:

• DOT1L shRNA-KD via in utero electroporation, followed by either
• in situ hybridization for ASNS to check if ASNS transcript is increased upon DOT1L shRNA-KD compared to CON
• FACS sorting of the positive electroporated cells (CON and DOT1L shRNA-KD), followed by qPCR to assess the levels of ASNS
• If the reviewer wants us to check for a more downstream effect on fate, then we will immuno-stain the DOT1L shRNA-KD and CON with TUBB3 AB and/or TBR1 AB (as already done in the present version of the manuscript). Reviewer’s comment: 2) The possible changes in cell division and differentiation were found by very nice single-cell tracing system. However, changes in division modes occurring in targeted APs such as angles of mitotic division and the expression of mitotic markers were not addressed. These information is critical information to understand mechanisms underlying observed phenotype, delamination, differentiation and fate commitment.

Response to Reviewer and planned revision:

Previous effects of DOT1L manipulation on the mitotic spindle were observed in a previous paper, using DOT1L KO mouse (Franz et al. 2019). Considering that in our experiments we do use a pharmacological inhibition, we will address this point by quantifying the spindle angle in CON and EPZ-treated cortical hemispheres.

We will co-stain for DAPI to visualize the DNA/chromosomes, and for phalloidin (filamentous actin counterstain) that allows for a precise visualization of the apical surface and of the cell contour, as it stains the cell cortex.

Of note, the protocols we are referring to are already established in the lab, based on published work from the Huttner lab (Taverna et al, 2012; Kosodo et al, 2005).

Reviewer’s comment: 3) The scRNA-seq analysis indicated interesting results, but was not fully clear to explain the observed results in histology. In fact, in single cell RNA-seq, the author claimed that cells in TTS are increased after EPZ treatment, which are more similar to APs. However, in histological data, they found that EPZ treatment increased neuronal differentiation. These data conflicts, thus I wonder whether "neurons" from histology data are actually neurons? Using several other markers simultaneously, it would be important to check the cellular state in histology upon the inhibition/KD of DOT1L.

Response to Reviewer and planned revision:

The reviewer’s comment is valid, and we indeed found that TTS cells are an intermediate state between APs and neurons in term of transcriptional profile. This is the reason why we called this cell cluster transient transcriptional state.

We plan to address this point by staining for TBR1 and/or CTIP2 in CON and EPZ-treated hemispheres and to expand with this EOMES and SOX2 co-staining.

Minor issues:

Reviewer’s comment: Figure 1 - It is not clear delaminated cells are APs, BPs or some transient cells (Sox2+ Tubb3+??). It is important to use several cell type-specific and cell cycle markers simulnaneously to characterize cell-type specific identity of the analysed cells by staining. These applied to Fig1B,D,E,F,G,as well as Fig2,3.

Response to Reviewer and planned revision:

We will address this point by using a combinatorial staining scheme for several fate markers such as TUBB3, EOMES and SOX2, as suggested by the reviewer.

Reviewer’s comment: - Please provide higher magnification images of labelled cells (Fig 1H)

Response to Reviewer and planned revision:

In the revised manuscript, we will provide higher magnification for the staining.

Reviewer’s comment: - Please provide clarification on the criteria of Tis21-GFP+ signal thresholding.

Response to Reviewer and planned revision:

In the revised manuscript, we will provide a clarification on the criteria of Tis21-GFP+ signal thresholding.

Reviewer’s comment: - Splitting the GFP signal between ventricular and abventricular does not convincingly support the "more basal and/or differentiated" states after EPZ treatment.

Response to Reviewer and planned revision:

We will provide a clarification regarding this point.

Reviewer’s comment: - Please explain the presence of Tis21-GFP+ cells at the apical VZ.

Response to Reviewer and planned revision:

Tis21-GFP+ cells at the apical VZ has been extensively reported in the literature, since the first paper by Haubensak et al. regarding the generation of the Tis21-GFP+ line. In a nutshell, T Tis21-GFP+ cells are present throughout the VZ (therefore also in the apical portion) as neurogenic, Tis21-GFP positive cells are undergoing mitosis at the apical surface. Indeed, the presence of Tis-21 GFP signal have been extensively used by the Huttner lab and collaborators to score apical neurogenic mitosis. In addition, since AP undergo interkinetic nuclear migration, it follows that Tis21-GFP+ nuclei are going to be present throughout the entire VZ.

In the revised manuscript, we will explain this point and cite additional literature.

Reviewer’s comment: - Order the legends in same order as the bars.

Response to Reviewer and planned revision:

We will follow reviewers’ recommendation and order the legends accordingly.

Reviewer’s comment: Figure 2 -Fig 2B) The difference between CON and EPZ apical contacts is not clear and does not match with the graph in Fig 2E.

Response to Reviewer and planned revision:

We will explain Fig. 2B in more detail and provide additional images in the revised manuscript.

Reviewer’s comment: -Supp Fig 2 - are these injected slices cultured in control conditions? Please include this in the text and figure/figure legend

Response to Reviewer and planned revision:

In the revised manuscript, the text will be changed to address this point and provide clearer info.

Reviewer’s comment: Fig 2C) The EPZ-treated DxA555+ cells exhibit morphological change of cell shape. Is this phenotype? please comment on the image shown for EPZ treatment panel.

Response to Reviewer and planned revision:

We thank the reviewer for having raised this point.

The change in morphology might be a consequence of delamination and or of cell fate. In the revised manuscript, we will certainly better comment on this very relevant point and expand the discussion accordingly.

Reviewer’s comment: Fig 2F - 2G) Data presented on EOMES+ and TUBB3+ % are counterintuitive. The authors claimed that TUBB3+ cells are increased and neuronal differentiation is promoted. However, no changes in EOMES+ are observed. What is the explanation? Did the author check the double positive cells? These could be TSS cells?

Response to Reviewer and planned revision:

We thank the reviewer to have raised this point.

As envisioned by the reviewer, we suspect that the counterintuitive data might be due to TSS cell, which based on our scRNAseq data are expressing at the same time several cell type specific markers. It is possible that, since the treatment with EPZ is 24h long, cells (like the TTS cluster) have no time to completely eliminate the EOMES protein. If that were to be the case, then we would expect to still detect (as we indeed do) EOMES immunoreactivity.

To address this point, we will:

• analyze scRNA-seq data and check which is the extent of co-expression of Eomes and Tubb3 mRNAs in the TTS population.
• Check for EOMES and TUBB3 double positive cells in the microinjection experiment. Reviewer’s comment: Figure 2 and Figure 3) the number of pairs analyzed for EPZ is twice as that of Con for comparison of the parameters taken into account. Please include n of each graph in the figure legend of the specific panel if not the same for all panels in that figure (i.e. for figure 3)

Response to Reviewer and planned revision:

We will revise the text accordingly.

Reviewer’s comment:

Figure 3) The data indicated that the number of daughter cell pairs in EPZ samples is almost double than Control. Is this the phenotype? More numbers of daughter cells in EPZ treated samples were observed from the same number of injections? or the number of injected cells were different?

Response to Reviewer and planned revision:

Due to technical reasons, we indeed performed a higher number of injections in EPZ-treated slices. We think this is the main reason behind the difference in number.

If the reason were to be biological, one would expect to see the same trend in IUE experiments, but this is actually not the case. This does suggest/corroborate the idea that the reason behind the difference is mainly technical.

Reviewer’s comment: Figure 4)

• Please clarify if the single cell transcriptomic analysis has been performed only once, and if yes, how statistical testing to compare the cell proportion is carried out with only one batch. Fig 4G)

Response to Reviewer and planned revision:

As for the scRNAseq on microinjected cells:

the scRNA-seq analysis was done once using cells pooled from 3 different microinjection experiments performed in 3 different days.

As for the scRNAseq on IUE cells:

The scRNA-seq analysis was done once using cells pooled from 2-3 different IUE experiments performed in 3 different days.

For all scRNAseq experiments the statistical testing is achieved by intrasample comparisons according to established bioinformatics pipelines. We will better explain this point in the revised manuscript.

Reviewer’s comment: Figure 4 and 5) - Figures are not supportive of the statement regarding APs' neurogenic potential upon DOT1L inhibition. TSS transcriptomic profile resembles more progenitors than neurons. Please comment on TSS neurogenic capacity taking into account the provided GO and RNAseq.

Response to Reviewer and planned revision:

We thank Reviewer 1 for raising this point, It is indeed true that TTS resemble more AP than neurons (as indicated in the Fig. S5B, C). We took that to indicate the fact that these cells are transient and therefore still maintain some AP features. Interestingly, TTS downregulate cell division markers, suggesting a restriction of proliferative potential, as one would expect for cells with an increased neurogenic potential. We will discuss this point in the revised manuscript.

Reviewer’s comment: - Please provide GO analysis for APs and BPs.

Response to Reviewer and planned revision:

Following the reviewer’s suggestion, we will incorporate a more careful and in-depth analysis in the revised version of the manuscript.

Reviewer’s comment: - Reconstruct figure 5A by listing genes in the same order in both Con and EPZ and prioritize EPZ-Con differences instead of cell-cell differences.

Response to Reviewer and planned revision:

We will revise Figure 5A based on the reviewer’s comment.

Reviewer’s comment:

Moreover, the presented genes in the heatmap is not the same in two conditions (i.e. NEUROG1 is present in EPZ but absent in Con). Please justify.

Response to Reviewer and planned revision:

This observation is based on different activities of transcription factor networks in the control and EPZ condition. They are not supposed to be the same as the cell states are altered and different TF are expressed and active upon the treatment in the diverse cell types. In a revised manuscript we will justify this point.

Reviewer’s comment: Fig 5D)

• Please explain why binding of EZH2 on the promoter of Asns is strongly reduced in comparison to a mild significant reduction of H3K79me/H3K27me3 in EPZ compared to Control.

Response to Reviewer and planned revision:

Several explanations are possible

First, the variation can be due to batch effects.

Second, the acute reduction of EZH2 might not be directly accompanied by a reduced histone mark, which is reduced either by cell division or by demethylases. The two processes of getting rid of the mark might be slower than the reduction of EZH2 presence at the respective site.

Based on the reviewer’s comment, we will explain this point in the revised manuscript.

• *

Reviewer’s comment:

Also is the changed directly medicated by DOT1L?

Please test whether DOT1L can bind the promoter of Asns.

Response to Reviewer and planned revision:

To address this relevant issue we will proceed with the following protocol:

• electroporate a tagged version of DOT1L into ESCs
• select ESCs and differentiate them into NPC_48h.
• treat NPC with DMSO (Con) or EPZ
• harvest CON and EPZ-treated NPC
• perform ChIP-qPCR DOT1L at the Asns promoter Reviewer’s comment: Please provide the expression patterns of DOT1L and Asns during neuronal differentiation.

Response to Reviewer and planned revision:

As for Dot1l

Dot1l expression was shown in Franz et al 2019, by ISH from E12.5 to E18.5.

As for Asns

We will provide E14.5 in situ staining of Asns in the developing mouse brain using the Gene Paint database (see Figure below).

We will also show immunostainings for ASNS at mid-neurogenesis, provided that Ab against ASNS works in the mouse.

Other General comments:

Reviewer’s comment: Please Indicate VZ, SVZ and CP on the side of the pictures/ with dot lines in the pictures both for primary figures and supplementary.

Response to Reviewer and planned revision:

We will revise the figures accordingly.

Reviewer’s comment: - The Results and figures sometimes do not support the statement made by the authors

Response to Reviewer and planned revision:

We will carefully check on this and eliminate any overinterpretation or non-supported statements from the text.

• Schemes are not informative/explanatory enough, i.e. time windows of treatment and sample collection, culture conditions details.

Response to Reviewer and planned revision:

We will revise the schemes to include more details. In particular, we plan to add a supplementary figure with a detailed visual description of the protocol, to match the detailed description presented in the materials and methods.

Reviewer’s comment: - A more extensive characterization of TTS cells in terms of differentiation progression and integration would be enlightening

Response to Reviewer and planned revision:

In general, we are facing two main challenges while studying the TTS population: one is the lack of a specific marker gene for TTS, the other is the relatively small size of the TTS subpopulation.

For these reasons, our ability to carry on an in-depth analysis of this cell state is limited.

Considering the reviewer’s comment, in the revised manuscript we will expand the analysis ad characterization of the differentiation potential of TTS using RNA velocity trajectory.

We can also expand the discussion on this point.

Reviewer’s comment: - Picture quality can be improved, provide high magnification images.

Response to Reviewer and planned revision:

We will revise the figures to include higher magnification images.

Reviewer #1 (Significance (Required)):

Reviewer’s comment: The study could be important for the specific field in neural development. It aims to understand mutations in respective genes and brain malformation. If the link between epigenetic and metabolic changes is clearly shown, it will be interesting. However, the current manuscript is still rather descriptive, and clear mechanistic insights were not provided. The study have potentials and additional data will strength the value of study.

Response to Reviewer and planned revision:

We will address the direct impact of DOT1L and H3K79me2 on the Asns gene locus during the revision (see the rationale of the experimental strategy also in the revision plan above). We hope we will thus provide a mechanistic link between epigenetics and altered metabolome.

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

Reviewer’s comment: Appiah et al. present a concise manuscript that provides details and possible mechanisms of their previous work (Franz et al., 2019; Ferrari et al., 2020). The study uses diverse lines of investigation to arrive at most conclusions. However, as interesting as the data is, we find that at the present state, it is not sufficient to prove that, indeed, the asparagine metabolism is regulated by DOTL1/PRC2 crosstalk. The neurogenic shift presented in the first part of the paper is not comprehensive and, therefore, not very convincing. The quality of images provided in the main and supplementary data is less than ideal. Additional data analysis and interpretation of the scRNA seq data may be needed. The authors finally conclude with rescue experiments done in culture and in-vivo, which we believe is the stand-out part of this study. Overall the manuscript has some interesting observations that are often over-interpreted with less supporting data. The manuscript reads well but requires additional data and changes in the claims/interpretation to be suited for publication.

Response to Reviewer and planned revision:

In the revised manuscript, we hope we will address the comments and concerns raised by the reviewer in a satisfactory manner. Comments

Reviewer’s comment: 1) Abstract: Is this statement correct: "DOT1L inhibition led to increased neurogenesis driven by a shift from asymmetric self-renewing to symmetric neurogenic divisions of APs. AP undergoes symmetric division for self-renewal and asymmetric neurogenic divisions.

Response to Reviewer and planned revision:

Based on the current literature (cit. Huttner and Kriegstein), AP undergo:

• symmetric division for proliferative division at early stages of neurogenesis
• asymmetric self-renewing division, generating an AP and a BP at mid neurogenesis. This division is also described as neurogenic, as it produces a BP, that is a step further than AP in term of neurogenic potential.
• symmetric consumptive division at late neurogenesis To avoid any possible confusion, we will re-phrase the sentence to include the adjective “consumptive” and specify the composition of the progeny.

In the revised manuscript, the sentence will read as follow:

"DOT1L inhibition led to increased neurogenesis driven by a shift of APs from asymmetric self-renewing (generating one AP and one BP) to symmetric consumptive divisions (generating two neurons)"

Reviewer’s comment: All the data is based on treatments with EPZ (DOTL1 inhibitor), yet no information is shown to support its targeted activity in this system. A proof of principle in the chosen experimental system is missing; for instance, examining the activity or protein level of DOTL1 and decreased methylation of the target(s) is essential.

Response to Reviewer and planned revision:

EPZ is a well characterized drug, that has been used previously in our lab and by others as well.

As for our lab, the information regarding the inhibitor, its activity and efficiency in inhibiting DOT1L towards H3K79me2 was shown in Franz et al. Supplementary Fig. S6 D, E.

In the present manuscript, an additional confirmation that EPZ targets DOT1L in regard to its H3K79me2 activity is shown in Fig. 5D.

We would refer to this information more explicitly in a revised manuscript.

Reviewer’s comment: 2) Figure 1: The scoring of centrosomes and cilia is insufficient to conclude delamination and increase in basal fates. The effect could be on ciliogenesis or centrosome tethering to the apical end-feet of the AP, and other possible explanations for this observation also exist. The images are too small; larger images or graphic representations could be helpful in addition to the data.

Response to Reviewer and planned revision:

We did not intend to claim that the change in centrosome location demonstrate delamination, but only that it suggests delamination. This criterion has been extensively used as a proxy for delamination by several labs working on the cell biology of neurogenesis, such Huttner and Gotz labs. If the issue persists, we can re-phrase in a more cautious way the text referring to Figure 1 to highlight that the data only suggest delamination.

Response to Reviewer and planned revision:

To make a statement regarding delamination, I would like to see either the dynamics of delamination (organotypic slices images), staining with BP markers, or morphological changes of AP (staining that will reveal loss of adherence) or comparable data to support the observation. In my opinion Supp. Figure 1 is insufficient; the single image is not convincing; I would like to see 3D reconstruction and better-quality images.

Response to Reviewer and planned revision:

We can certainly provide better images and co-stain with relevant markers.

We think it is beyond the scope of the manuscript embarking in live imaging as we are not studying the dynamics of delamination per se.

Reviewer’s comment: Tis21 data (1H), again of low quality, is only a single piece of evidence and the conclusion "suggesting that the acquisition of a basal fate was paralleled by a switch to neurogenesis" is premature. I think other cell cycle exit reporters, Fucci markers, pHis, BrdU, NeuroD, or Tbr2 reporters (Li et al., 2020, (Haydar and Sestan labs)) to name a few, are necessary to establish the conclusions. The authors should show other markers such as PAX6, EOMES, or other upper-layer markers upon cell cycle exit in the SVZ/CP. These additional experiments will assist in cell fate analysis.

Response to Reviewer and planned revision:

We completely understand the points raised by the reviewer, and we plan to address them by co-staining with PAX6/SOX2, PH3 and/or EOMES.

We think establishing the Fucci or EOMES mouse system is beyond the scope of the manuscript. In addition, given the present setting of all labs involved, it would be logistically unattainable (see also comments in the section below).

We think the co-staining scheme and plan will be informative enough to satisfactory address the concerns raised by the reviewer.

Reviewer’s comment: 2) Figure 2: The microinjection experiments are elegant; the images, however, do not complement the experiment. The images of the microinjected cells seem not to be reconstructed from z-stacked optical slices, so often, processes are not continuous (panel B, for example); therefore, it is not clear if an apical process is indeed missing or just not seen.

Response to Reviewer and planned revision:

The mentioned images are reconstructed from continuous Z-stacks, as we always do given the type of data. We can provide better reconstructions and/or additional images.

Reviewer’s comment:

The data analysis should include other parameters; BrdU staining could have given information on cell cycle exit, PAX6, SOX2, and EOMES on the location of the cells in the VZ/sVZ. The quality of images showing EOMES and TUBB3 staining is so low that it makes the reader doubt the validity of the quantifications. "Taken together, these data suggest that the inhibition of DOT1L might favor the acquisition of a neuronal over BP cell fate" This interpretation should be subjected to more investigations. It is possible that this treatment just accelerates the AP-> BP -> Neuronal fate. The author's claim needs to be backed by additional experiments or be changed.

Response to Reviewer and planned revision:

To address this point, we will include in the revised manuscript staining and co-staining with PAX6, SOX2 (see also response above) and provide a BrdU labeling experiment.

Reviewer’s comment: 3) Figure 3: The experiment concept and its performance are impressive, yet the data is insufficient. The images in A that are supposed to be representative show two cells; their location is not clear, and the expression of GFP is not clear; in fact, both pairs seem to be GFP negative (not clear what is the threshold for background). Staining with anti-GFP and a second method to follow neurogenesis is necessary.

Response to Reviewer and planned revision:

We did use different staining methods and schemes to follow neurogenesis. As specified above, we will deepen our analysis by using additional markers, such as TBR1.

Reviewer’s comment: 4) On page 9, lines 8-10, the authors claim that their number of cells was "sufficient" for single-cell analysis; the numbers are Response to Reviewer and planned revision:

In the revised manuscript, we will include the analysis of how many cells are needed to identify cluster of 6 cell types in this paradigm, based for example on the algorithms developed in Treppner et al. 2021.

Reviewer’s comment: 5) The authors use Seurat and RaceID without their appropriate citations in the first mention during the results. The authors also stop immediately after DEG analysis along with clustering. The authors could analyze their RNA-seq data with a trajectory; to say the least, the identification/characterization of TTS and neurons as Neurons I, II, and III are insufficient. There could be multiple ways to show the "fate" of cells in the isolated FACS, which the authors have missed.

Response to Reviewer and planned revision:

We will include the respective citations in a revised manuscript. We provide already differentiation trajectories but will include other methods, including scVelo of FateID to extend the trajectory analyses. We kindly ask the reviewer to also refer to the comments above regarding the TTs cluster characterization as part of our effort to provide a better picture of the different clusters.

Reviewer’s comment: 6) The authors detected candidates like Fgfr3, Nr2f1, Ofd1, and Mme as part of their treated (different approaches) datasets (from their DEG analysis). They correctly cite Huang et al., 2020 but fail to give us a sense of the consequences of these gene dysregulations. The authors can also validate if these proteins are expressed in their treated cells.

Response to Reviewer and planned revision:

In the revised manuscript we will comment on the function of the four genes mentioned.

In addition, we will validate the expression of these genes on protein and transcriptional level through immunostainings -provided that antibodies are working in our system- or smFISH, respectively.

Reviewer’s comment: 7) The authors list a few GO terms (page 10, lines 1-10) and associate them with reduced proliferation; they must cite relevant studies. The authors can also add supplementary data showing which genes in their data correspond to these GO terms.

Response to Reviewer and planned revision:

We thank the reviewer for pointing out the missing citations.

We of course agree on the need to add them, and we will do so in the revised manuscript.

Reviewer’s comment: 8) On Page 11, lines 3-7, the authors describe their method to arrive at the 17 targets with TF activity from the previous analysis. Can the authors describe the method used to correlate the two? The reviewer understands this could be MEME analysis or analysis of earlier datasets of Ferrari et al. 2020. But it must be explicitly stated, and a few examples in supplementary need to be exemplified as this analysis is key to discovering the three metabolic genes.

Response to Reviewer and planned revision:

In the revised manuscript, we will clarify the exact analysis that resulted in the identification of the 17 target genes, using the specific tool for gene network analysis, that is based on our scRNA-seq data alone, but not on the Ferrari et al 2020 data set.

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

n/a

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

Reviewer’s comment: Tis21 data (1H), again of low quality, is only a single piece of evidence and the conclusion "suggesting that the acquisition of a basal fate was paralleled by a switch to neurogenesis" is premature. I think other cell cycle exit reporters, Fucci markers, pHis, BrdU, NeuroD, or Tbr2 reporters (Li et al., 2020, (Haydar and Sestan labs)) to name a few, are necessary to establish the conclusions. The authors should show other markers such as PAX6, EOMES, or other upper-layer markers upon cell cycle exit in the SVZ/CP. These additional experiments will assist in cell fate analysis.

Response to Reviewer and planned revision:

As pointed out above, we think establishing the Fucci or EOMES mice system is beyond the scope of the manuscript as it will not provide more information than the ones we will obtain from systematic and extensive co-staining experiments. In addition, all labs involved are facing a logistic issue (animal house not ready yet, construction works etc) that made the importing and setting up of the colony unattainable for the next 6-10months. If the reviewer and/or the editorial board think this is a major point compromising the entire revision, we kindly ask to contact us again so that we can discuss the issue and arrive to a shared conclusion.

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Referee #2

Evidence, reproducibility and clarity

Appiah et al. present a concise manuscript that provides details and possible mechanisms of their previous work (Franz et al., 2019; Ferrari et al., 2020). The study uses diverse lines of investigation to arrive at most conclusions. However, as interesting as the data is, we find that at the present state, it is not sufficient to prove that, indeed, the asparagine metabolism is regulated by DOTL1/PRC2 crosstalk. The neurogenic shift presented in the first part of the paper is not comprehensive and, therefore, not very convincing. The quality of images provided in the main and supplementary data is less than ideal. Additional data analysis and interpretation of the scRNA seq data may be needed. The authors finally conclude with rescue experiments done in culture and in-vivo, which we believe is the stand-out part of this study. Overall the manuscript has some interesting observations that are often over-interpreted with less supporting data. The manuscript reads well but requires additional data and changes in the claims/interpretation to be suited for publication.

Comments

1. Abstract: Is this statement correct: "DOT1L inhibition led to increased neurogenesis driven by a shift from asymmetric self-renewing to symmetric neurogenic divisions of APs". AP undergoes symmetric division for self-renewal and asymmetric neurogenic divisions.

All the data is based on treatments with EPZ (DOTL1 inhibitor), yet no information is shown to support its targeted activity in this system. A proof of principle in the chosen experimental system is missing; for instance, examining the activity or protein level of DOTL1 and decreased methylation of the target(s) is essential. <br /> 2. Figure 1: The scoring of centrosomes and cilia is insufficient to conclude delamination and increase in basal fates. The effect could be on ciliogenesis or centrosome tethering to the apical end-feet of the AP, and other possible explanations for this observation also exist. The images are too small; larger images or graphic representations could be helpful in addition to the data.

To make a statement regarding delamination, I would like to see either the dynamics of delamination (organotypic slices images), staining with BP markers, or morphological changes of AP (staining that will reveal loss of adherence) or comparable data to support the observation. In my opinion Supp. Figure 1 is insufficient; the single image is not convincing; I would like to see 3D reconstruction and better quality images.

Tis21 data (1H), again of low quality, is only a single piece of evidence and the conclusion "suggesting that the acquisition of a basal fate was paralleled by a switch to neurogenesis" is premature. I think other cell cycle exit reporters, Fucci markers, pHis, BrdU, NeuroD, or Tbr2 reporters (Li et al., 2020, (Haydar and Sestan labs)) to name a few, are necessary to establish the conclusions. The authors should show other markers such as PAX6, EOMES, or other upper-layer markers upon cell cycle exit in the SVZ/CP. These additional experiments will assist in cell fate analysis. 2. Figure 2: The microinjection experiments are elegant; the images, however, do not complement the experiment. The images of the microinjected cells seem not to be reconstructed from z-stacked optical slices, so often, processes are not continuous (panel B, for example); therefore, it is not clear if an apical process is indeed missing or just not seen. The data analysis should include other parameters; BrdU staining could have given information on cell cycle exit, PAX6, SOX2, and EOMES on the location of the cells in the VZ/sVZ. The quality of images showing EOMES and TUBB3 staining is so low that it makes the reader doubt the validity of the quantifications. <br /> "Taken together, these data suggest that the inhibition of DOT1L might favor the acquisition of a neuronal over BP cell fate" This interpretation should be subjected to more investigations. It is possible that this treatment just accelerates the AP-> BP -> Neuronal fate. The author's claim needs to be backed by additional experiments or be changed. 3. Figure 3: The experiment concept and its performance are impressive, yet the data is insufficient. The images in A that are supposed to be representative show two cells; their location is not clear, and the expression of GFP is not clear; in fact, both pairs seem to be GFP negative (not clear what is the threshold for background). Staining with anti-GFP and a second method to follow neurogenesis is necessary. 4. On page 9, lines 8-10, the authors claim that their number of cells was "sufficient" for single-cell analysis; the numbers are <500 for all samples. The authors need to justify this statement or articles that carefully analyze the number required for such a conclusion as references. 5. The authors use Seurat and RaceID without their appropriate citations in the first mention during the results. The authors also stop immediately after DEG analysis along with clustering. The authors could analyze their RNA-seq data with a trajectory; to say the least, the identification/characterization of TTS and neurons as Neurons I, II, and III are insufficient. There could be multiple ways to show the "fate" of cells in the isolated FACS, which the authors have missed. 6. The authors detected candidates like Fgfr3, Nr2f1, Ofd1, and Mme as part of their treated (different approaches) datasets (from their DEG analysis). They correctly cite Huang et al., 2020 but fail to give us a sense of the consequences of these gene dysregulations. The authors can also validate if these proteins are expressed in their treated cells. 7. The authors list a few GO terms (page 10, lines 1-10) and associate them with reduced proliferation; they must cite relevant studies. The authors can also add supplementary data showing which genes in their data correspond to these GO terms. 8. On Page 11, lines 3-7, the authors describe their method to arrive at the 17 targets with TF activity from the previous analysis. Can the authors describe the method used to correlate the two? The reviewer understands this could be MEME analysis or analysis of earlier datasets of Ferrari et al. 2020. But it must be explicitly stated, and a few examples in supplementary need to be exemplified as this analysis is key to discovering the three metabolic genes.

Significance

Appiah et al. present a concise manuscript that provides details and possible mechanisms of their previous work (Franz et al., 2019; Ferrari et al., 2020). The study uses diverse lines of investigation to arrive at most conclusions. However, as interesting as the data is, we find that at the present state, it is not sufficient to prove that, indeed, the asparagine metabolism is regulated by DOTL1/PRC2 crosstalk. The neurogenic shift presented in the first part of the paper is not comprehensive and, therefore, not very convincing. The quality of images provided in the main and supplementary data is less than ideal. Additional data analysis and interpretation of the scRNA seq data may be needed. The authors finally conclude with rescue experiments done in culture and in-vivo, which we believe is the stand-out part of this study.

Overall the manuscript has some interesting observations that are often over-interpreted with less supporting data. The manuscript reads well but requires additional data and changes in the claims/interpretation to be suited for publication.

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Referee #1

Evidence, reproducibility and clarity

The manuscript investigated the role of DOT1L during neurogenesis especially focusing on the earlier commitment from APs. Using tissue culture method with single-cell tracing, they found that the inhibition of DOT1L results in delamination of APs, and promotes neuronal differentiation. Furthermore, using single cell RNA-seq, they seek possible mechanisms and changes in cellular state, and found a new cellular state as a transient state. Among differentially expressed genes, they focused on microcephaly-related genes, and found possible links between epigenetic changes led by DOT1L inhibition and epigenetic inhibition by PRC2. Based on these findings, they suggested that DOT1L could regulate neural fate commitment through epigenetic regulation. Overall, it is well written and possible links from epigenetic to metabolic regulation are interesting. However there are several issues across the manuscript.

Major issues:

1. It is not clear whether the degree of H3K79 methylation (or other histones) changes during development, and whether DOT1L is responsible for those changes. It is necessary to show the changes in histone modifications as well as the levels of DOT1L from APs to BPs and neurons, and to what extent the treatment of EPZ change the degree of histone methylation. Furthermore, the study mainly used pharmacological bath application. DOT1L has anti-mitotic effect, thus it is not clear whether the effect is coming from the inhibition of transmethylation activity. In addition, the study assumed that the effect of EPZ is cell autonomous.However, if EPZ treatment can change the metabolic state in a cell, it would be possible that observed effects was non-cell autonomous. It would be important to address if this effect is coming in a cell-autonomous manner by other means using focal shRNA-KD by IUE.
2. The possible changes in cell division and differentiation were found by very nice single-cell tracing system. However, changes in division modes occurring in targeted APs such as angles of mitotic division and the expression of mitotic markers were not addressed. These information is critical information to understand mechanisms underlying observed phenotype, delamination, differentiation and fate commitment .
3. The scRNA-seq analysis indicated interesting results, but was not fully clear to explain the observed results in histology. In fact, in single cell RNA-seq, the author claimed that cells in TTS are increased after EPZ treatment, which are more similar to APs. However, in histological data, they found that EPZ treatment increased neuronal differentiation. These data conflicts, thus I wonder whether "neurons" from histology data are actually neurons? Using several other markers simultaneously, it would be important to check the cellular state in histology upon the inhibition/KD of DOT1L.

Minor issues:

Figure 1

• It is not clear delaminated cells are APs, BPs or some transient cells (Sox2+ Tubb3+??). It is important to use several cell type-specific and cell cycle markers simulnaneously to characterize cell-type specific identity of the analysed cells by staining.These applied to Fig1B,D,E,F,G,as well as Fig2,3.

• Please provide higher magnification images of labelled cells (Fig 1H)

• Please provide clarification on the criteria of Tis21-GFP+ signal thresholding.
• Splitting the GFP signal between ventricular and abventricular does not convincingly support the "more basal and/or differentiated" states after EPZ treatment.
• Please explain the presence of Tis21-GFP+ cells at the apical VZ.
• Order the legends in same order as the bars.

Figure 2

• Fig 2B) The difference between CON and EPZ apical contacts is not clear and does not match with the graph in Fig 2E.

• Supp Fig 2 - are these injected slices cultured in control conditions? Please include this in the text and figure/figure legend

Fig 2C) The EPZ-treated DxA555+ cells exhibit morphological change of cell shape. Is this phenotype? please comment on the image shown for EPZ treatment panel.

Fig 2F - 2G) Data presented on EOMES+ and TUBB3+ % are counterintuitive. The authors claimed that TUBB3+ cells are increased and neuronal differentiation is promoted. However, no changes in EOMES+ are observed. What is the explanation? Did the author check the double positive cells? These could be TSS cells?

Figure 2 and Figure 3) the number of pairs analyzed for EPZ is twice as that of Con for comparison of the parameters taken into account. Please include n of each graph in the figure legend of the specific panel if not the same for all panels in that figure (i.e. for figure 3)

Figure 3)

• The data indicated that the number of daughter cell pairs in EPZ samples is almost double than Control. Is this the phenotype? More numbers of daughter cells in EPZ treated samples were observed from the same number of injections? or the number of injected cells were different? Figure 4)
• Please clarify if the single cell transcriptomic analysis has been performed only once, and if yes, how statistical testing to compare the cell proportion is carried out with only one batch. Fig 4G)

Figure 4 and 5)

• Figures are not supportive of the statement regarding APs' neurogenic potential upon DOT1L inhibition. TSS transcriptomic profile resembles more progenitors than neurons. Please comment on TSS neurogenic capacity taking into account the provided GO and RNAseq.
• Please provide GO analysis for APs and BPs.

Figure 5)

• Reconstruct figure 5A by listing genes in the same order in both Con and EPZ, and prioritize EPZ-Con differences instead of cell-cell differences. Moreover, the presented genes in the heatmap is not the same in two conditions (i.e. NEUROG1 is present in EPZ but absent in Con). Please justify. Fig 5D)
• Please explain why binding of EZH2 on the promoter of Asns is strongly reduced in comparison to a mild significant reduction of H3K79me/H3K27me3 in EPZ compared to Control. Also is the changed directly medicated by DOT1L? Please test whether DOT1L can bind the promoter of Asns.

Please provide the expression patterns of DOT1L and Asns during neuronal differentiation.

Other General comments: - Please Indicate VZ, SVZ and CP on the side of the pictures/ with dot lines in the pictures both for primary figures and supplementary. - The Results and figures sometimes do not support the statement made by the authors - Schemes are not informative/explanatory enough, i.e. time windows of treatment and sample collection, culture conditions details.. - A more extensive characterization of TTS cells in terms of differentiation progression and integration would be enlightening - Picture quality can be improved, provide high magnification images.

Significance

The study could be important for the specific field in neural development. It aims to understand mutations in respective genes and brain malformation. If the link between epigenetic and metabolic changes is clearly shown, it will be interesting. However, the current manuscript is still rather descriptive, and clear mechanistic insights were not provided. The study have potentials and additional data will strength the value of study.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this work, the authors investigate the effect of using mature mRNAs instead of only nascent mRNA (located at the transcription site) when estimating transcriptional kinetics parameters from single-molecule fluorescent in situ hybridization (smFISH) experiments. The authors find that using nascent mRNA and correcting for cell cycle effects yields more accurate parameter estimates than using mature mRNAs. The author performs smFISH experiments of the GAL10 gene in yeast to test their findings. Also, the authors test different methods to obtain parameter estimates in cases where there is no information about the location of the transcription site.

Major comments:

1.The authors make multiple claims of novelty that conflict with work described in some of their references, particularly: Skinner et al., eLife, 2016; Xu et al., Nature Methods, 2015 and Physical Review Letters, 2016 (References #26,27 and 24 in their manuscript). I could find several instances where the scope of their claims was unclear. Below I describe some cases:

a.The title of this paper, "accurate inference of stochastic gene expression from nascent transcript heterogeneity" could also be the summary conclusion of the three works cited above. However, later in the Introduction of the manuscript, the authors state that their goal is to "understand the impact of post-transcriptional noise and cell-to-cell variability on the accuracy of transcriptional parameters inferred from mature mRNA data," a related yet different topic. I would change the title of the manuscript to reflect their main goal better.

b.I would make their claims of novelty more specific. For example, at the end of the abstract, the authors claim that "our novel data curation method yields a quantitatively accurate picture of gene expression." Quantifying nascent mRNA using smFISH to obtain transcription kinetic parameters has been done before (the references above are an example) also developing the modeling tools to do so (for example, in Xu et al., Physical Review Letters, 2016). What is, exactly, the novelty in their approach? They need to make that explicit or soften their claims.

c.In the Introduction, when discussing the effect of the cell cycle in parameter estimation, they write: "Since estimation of all transcriptional parameters (...) from nascent data as a function of the cell cycle phase has not been reported". However, the work they reference (Skinner et al., eLife, 2016) shows such measurements for multiple transcriptional parameters for different cell cycle stages. The original work may not have gone as far as the current work, but it is unclear what has been done before from the way the authors describe earlier literature.

d.The authors develop a new formulation of the delay telegraph model to obtain kinetic parameters from the nascent RNA copy number statistics. They state in the SI that "Similar delay models have also been studied by other authors," however, the authors do not explain in which way their model differs from previous work. Does their approach have advantages over previously published models?

2.There is a particular choice during their analysis that I find problematic. In section 2.3, the authors state "The transcription site is counted as 1 mRNA, regardless of its intensity, but has a negligible influence since the mean number of mature mRNA is much greater than 1" (the number should be spelled). It is unclear that statement is true for all possible kinetic parameters. It is also hard to evaluate that claim because the authors do not show images of transcription sites that would support it. Trying to find more information, I saw images from previous work from one of the authors ("Optimized protocol for single-molecule RNA FISH to visualize gene expression in S. cerevisiae", figure 4). Those images suggest that the opposite is the case: in the cell shown, the number of mRNAs in the transcription site is not negligible but instead seems to contain most of the mRNAs in the cell. Solving this problem would require the authors to remake their analysis without making this assumption.

3.Overall, I think the current experiments are sufficient to support their claims. Also, the description of methods and references is appropriate to allow other researchers to reproduce their observations. Finally, the experiments are replicated, and enough cells are analyzed to provide enough statistical significance to their claims.

Minor comments:

1.In section 2.1.3, the authors mention using an optimization package written in Julia programing language. A reference to the package needs to be included, either an academic article or the website to the package.

2.In the discussion, the authors state "In addition, live-cell measurements include cells in S phase, which are excluded in smFISH." I do not think that statement is correct. One would expect that a large enough sample of cells assayed with smFISH will contain a subpopulation containing cells in the S-phase.

3.I find the overall presentation of figures and the analysis performed not optimal to convey their points. Below are some suggestions regarding presentation (and in some cases, analysis).

Text suggestions:

a.The meaning of the word "inference" seems to change across the manuscript. In the title, I understand that inference means "estimation," or more explicitly, estimating model parameters from experimental or simulated data. However, in the methods section, the authors write "Mature mRNA inference" and "Nascent mRNA inference." Do they mean "Estimating/Inferring model parameters from synthetic/experimental mature/nascent mRNA datasets"?

b.In the Introduction, the authors use three different terms for cell cycle (cell cycle position, cell cycle stage, and cell cycle phase). It is unclear to me if they are referring to the same concept.

Presentation suggestions:

c.I would remove Figure 2C and put it in the Supplementary information. It shows procedure details that are not fundamental to understanding their claims.

d.I would also relegate the tables in their six datasets in figure 1 and 2 to the Supplementary material. Tables are not very effective methods to present information.

e.I do not think that figures 1c and 2d are needed. Comparing the results from stochastic simulations and the predictions from the models is an internal control that the researchers should do to test the accuracy of their SSA implementation; it does not convey a message related to the main conclusions of their work.

f.I like figure 4a; it conveys one of the main points: not correcting for cell cycle can lead to considerable errors in parameter estimation. I would like to see a similar plot that conveys the difference in parameter estimation when using nascent vs. mature mRNA.

g.Why do the authors have table 1 separated from figure 4 while adding the tables to figures 1 and 2? I would be consistent and move all tables to the supplementary material.

Significance

As described above, some claims do not seem novel considering the references in this manuscript. This is not a problem; the authors can soften their claims to novelty without compromising their other claims. Previous works that estimated mRNA transcription kinetic parameters by quantifying nascent mRNA recognized that using mature mRNA would incur in parameter estimation errors. They considered it evident that quantifying the process closer to the transcription site would improve estimates. Similarly, it was also apparent that adding missing information (the gene copy number based on cell cycle information) would improve parameter estimates. That is why the authors presenting those arguments as findings is unnecessary. However, it is true that here the authors are interested in the level of error, not the fact that getting more accurate (or relevant) measurement will improve estimates.

An item that the authors may want to emphasize is their finding that it is possible to correct for measurements where the identity of the transcription site is unknown. All the works that they cite where nascent mRNA is measured using some method to localize the position of the transcription site. I mammalian cells and fly embryos, it is possible to label introns to identify mRNA located at the transcription site. That is not possible in many yeast genes or other microorganisms.

Which audience would be most interested in this work? I think those searching for methods to quantify transcriptional kinetics in organisms where the identity of the transcription site cannot be measured by smFISH or other novel methods such as Cas-FISH.

I performed studies of transcriptional kinetics in bacteria during my doctorate, and I continue utilizing smFISH in my research.

Referees cross-commenting

I agree with the assessment from the other reviewers. One of reviewer 2's requests (to perform simulations covering the parameter space) is particularly relevant given the main goals of the authors. All reviewers noted that the method used to quantify the number of RNA at the transcription site has shortcomings that need to be addressed

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Referee #2

Evidence, reproducibility and clarity

In the manuscript Fu and co-authors compare accuracy for 2 models that infer kinetics of the transcription from synthetic and experimental data. Specifically, they compare the telegraph model for mRNA and the delayed telegraph model for nascent RNA. They first provide the comparison for synthetically simulated data, and derive that the latter exhibits higher accuracy. Next they apply the model to experimental data from smFISH for PP7-GAL10 strain, and provide the framework to estimate the number of mRNAs and use the intensity at the transcriptional site to infer the number of bounds of polymerase during the transcription (nascent RNA). For the latter, I appreciate that they account for the fact that intensity throughout the transcription will depend on 'spatial' position of polymerase and incorporate this into the framework to infer nascent RNA levels. Additionally, for the experimental data they infer kinetics with and without accounting for cell cycle (accordingly 1 or 2 gene copies), and through comparing to life imaging data from Donovan et al., 2019, they suggest that the model that best describes experimental data is delayed telegraph for nascent RNA when accounted for cell cycle. Finally they provide 2 approaches - called rejection and fusion - to account for potential artifacts in estimation of nascent RNA levels from the intensity at transcriptional sites, and provide the comparison of how this approaches affect the overall fit.

Whereas it is important to have a systematic understanding/comparison for both models as well as for how accounting of cell cycle might improve the overall accuracy, some of the aspects of the results/estimation of values from experimental data require more thorough analysis. Specifically, below I describe points to be addressed:

Major points:

Comparison of the models for simulated data. In the first two chapters of the results the authors compare simulations/parameter inference from the synthetic data for the telegraph-based model for mRNA and delayed telegraph model for nascent RNA, and conclude that the latter provides better accuracy. However, based on the relationship for mean relative error distribution as a function of fON, it seems to me that both models show very similar results, and the support of better accuracy for nascent RNA seems unclear to me. Additionally, simulations are performed for the concise number of parameter sets, and it is unclear how well/uniformly the chosen sets cover the parameter space. I suggest that more thorough analysis is required. One way to do so would be to perform simulations on the same set of parameters that comprehensively cover the parameter space for both models and compare mean error rates in pairwise fashion. Additionally, it might be worth considering comparing error rate for each parameter separately (i.e. for sigma-on, sigma-off and the production rate of mRNAs when promoter is on).

An additional analysis of the accuracy of the estimated values from the experimental data. When it comes to experimental data, the overall fit of any proposed model will depend on both the suitability/correctness of a model to explain the process in question as well as the reliability of the estimates (inputs for the model) from the experiments. Specifically, it is possible that a model (either telegraph for mRNA or delayed telegraph for nascent RNA or both) to explain transcriptional kinetics is fairly accurate, but the input estimates (for accordingly mRNA or nascent RNA) are biased (due to technical artifacts from the experiment and/or the approach towards estimating those values), thus affecting the overall fit of a model and interpretation of the results.

I appreciate that authors address one potential artifact in estimating nascent RNA, where it is possible that the intensity of nascent RNA is overestimated if it is mistakenly confused with mRNA. I suggest that the more detailed analysis of the accuracy for both the number of mRNA molecules and the intensity of nascent RNA is required to provide better insight in how reliably those values are estimated and accordingly whether models might perform poorly due to biased estimates.

Specifically, I am wondering about next aspects:

Mature mRNA: More detailed method section covering the estimate for background signal and spot detection. A potential proximity of mRNA molecules resulting in underestimation of the total number of mRNAs, and how this might affect the fit of the telegraph model. Even though smFISH has been widely used to estimate the number of mRNA molecules (as a total number of spots), the technique has been mostly applied to mammalian cells with considerably bigger cell size. Additionally, the usage of the total number of mRNA molecules in order to estimate transcriptional kinetics from the telegraph model seemingly requires a highly accurate estimate of the total number of molecules. Combined, it is not obvious if potential underestimation of mRNAs (specifically in cells with high number of mRNAs) via smFISH in budding yeast cells might lead to the misleading interpretation of the results. One way to assess whether such 'merging' takes place is to look into the distribution of intensities for cytoplasmic spots (per cell and/or all the cells in the whole field of view). If those distributions frequently show bi/multi-modal behavior, it is worth considering whether a proposed way to estimate mRNA number is suitable in for given model organism/growth conditions/gene, and further extend the analysis on simulated data to provide the robustness of the fit of the telegraph model for mRNAs in cases whether number of mRNAs is underestimated. A more minor issue, but authors state that, for each cell, the highest intensity of the nuclear spot will count as one mRNA, and that it has a negligible influence. I would appreciate a more thorough analytical explanation for this or an additional analysis on the simulated data to support how random +/-1 of mRNAs might affect results of the fit, specifically for cases with ~low average mRNA estimate.

Nascent RNA: I might be missing something, but it seems that for cells in late G2 phase where nucleus is either strongly elongated (and looks like a sand clock) or even exhibits 2 separate nuclei connected with the chromatin bridge - 2 copies of the gene can be spatially resolved and therefore it might happen that 2 independent/separate brightest spots (one per each cell) amount to total estimate of nascent RNA in cases where promoter is on simultaneously in both copies? If so, depending on estimated in the study/prior literature-based estimates for sigma-on/off, the probability of simultaneous transcription might vary and this should be taken into account? This also might partially explain the phenomenon of lower transcriptional activity in G2 which is currently suggested to be explained with dosage compensation? Or are those cells considered as 2 cells in G1? If so, it needs to be specified in the text. Additionally, I suggest that images from microscopy can be provided as a supplement to aid clarity in how cell cycle, number of mRNAs and intensity for nascent RNA were estimated.

Additional experimental validation and/or the discussion of the accuracy of the inference for a different range of parameters. The analysis of the experimental data consists of the (I presume highly comparable with Donovan et al., 2019) single condition (i.e. galactose concentration, glu/galactose ratio) resulting in a single parameter set for transcriptional kinetics. Specifically, it is estimated that sigma on and off will be comparable for the given set up, and therefore, based on simulated data, the estimates will be somewhat reliable for the cell cycle accounted delayed telegraph for nascent RNA. I wonder how in practice (i.e. estimated from the experiments) the same model will perform for a different set of parameters/different conditions. Ideally, I would suggest performing the similar experiment, but where sigma on/sigma off is expected to be different. One way to achieve this with the GAL10 / galactose set up is to tune the glu/gal ratio of the media. Even without a comparison to live-cell tracing, the analysis of estimated parameters for merged and cell cycle specific data can shed light on how suitable the model is for alternative parameters. Alternatively, if the experiment is currently not feasible, I would appreciate a more extensive discussion of the practical suitability of the cell-cycle specific delayed telegraph model for nascent RNA for alternative sets of transcriptional parameters. Considering that the comparison was performed only against 'simple' telegraph model and in introduction authors mention a variety of 'improved' models for mRNA, that account for various sources of heterogeneity, they might be more suitable for alternative set of transcriptional parameters, and might be more suitable that cell cycle specific delayed telegraph for nascent RNA.

Overall, the main statements of the paper - that cell cycle specific inference from the experimental data using delayed telegraph model from nascent RNA performs best (compared to telegraph model from mRNA or not cell cycle specific) are supported, and I agree that understanding of the limitations of the currently popular models (telegraph for mRNA and/or not accounting for cell cycle) is an important addition to the field. I would be happy to further proceed with the revision/acceptance of the paper if the comments above are addressed/considered.

Minor comments:

Current method section is lacking the description of the growth media, which is an important aspect to specify when it comes to budding yeast (particularly when the sugar source is different from the standard glucose and/or results are compared to another publication). In the figure 2b I find the cartoon a little misleading - specifically why polymerase is bound when the promoter is off? If it is to illustrate the case when transcription/polymerase bound occured after promoter is switched off, why there are no polymerase to the right from the current one (as in in the case where promoter is on)? In table1 - there is a typo in the 2nd meta-row - I suspect it should say G2?

Significance

This paper is somewhat outside my core expertise, although closer to the expertise of my postdoc who assisted with the review.

The work is interesting but the generalisability of the conclusions is somewhat limited, partially by the lack of experimental validation. Nevertheless, there are interesting aspects of the study and the area of research is important.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, the authors consider the problem of inferring transcription dynamics from smFISH data. They distinguish between two important experimental situations. The first one considers measurements of mature mRNAs, while the second one considers measurements of nascent mRNA through fluorescent probes targeting PP7 stem loops. The former problem has been previously dealt with extensively, but less work has been done on the context of the latter. The inference approaches are based on maximum likelihood estimation, from which point estimates for promoter-switching and transcription rates are obtained. The study focuses on steady state measurements only. The authors perform several analyses using synthetic data to understand the limitations of both approaches. They find that inference from nascent mRNA is more reliable than inference from mature mRNA distributions. Moreover, they show that accounting for different cell-cycle stages (G1 vs G2) is important and that pooling measurements across the cell-cycle can lead to quantitatively and even qualitatively different inferences. Both approaches are then used to analyze transcription in an experimental system in yeast, for which they find evidence of gene dosage compensation. I consider this an interesting and relevant study, which will appeal to the systems- and computational biology community. The paper is well written and the (computational) methods are described in detail. The experimental description is quite minimal and could profit from further details / explanations. I have several technical criticisms and questions, which I believe should be addressed before publication. Since I am a theorist, I will comment predominantly on the statistical / computational aspects.

Major comments/questions:

-A key reference that is missing is Fritzsch et al. Mol Syst Biol (2018). In this work, the authors have used nascent mRNA distributions and autocorrelations (obtained from live-imaging) to infer promoter- and transcription dynamics. I believe this work should be appropriately cited and discussed.

Synthetic case study:

-Inference and point estimates. The authors use a maximum-likelihood framework to extract point estimates of the parameters. Subsequently, relative absolute differences are used to assess the accuracy of the inference. However, as far as I have understood, this is performed for only a single simulated dataset, for each considered parameter configuration. The resulting metric, however, does not really capture the inference accuracy, since it is based on a single (random) realization of the MLE. I would recommend to at least repeat the inference multiple times for different realizations of the simulated dataset (per parameter configuration) to get a better feeling of the distribution of the MLE (e.g., its bias / variance). Alternatively, identifiability analyses based on the Fisher information could be performed for (some of) the different parameter configurations although this may be computationally more demanding.

-It would be useful to include confidence intervals based on profile likelihoods also for the synthetic case study, in particular for the 6 reported datasets. I would also find it helpful to see comprehensive profile likelihood plots for the key results / parameter inferences in the supplement. This would also provide useful insights into the identifiability of the parameters.

Experimental case study:

-Validation against live-cell data. In the simulation of the autocorrelation function, what was the ratio of cells initialized in G1 / G2, respectively? I'd expect this to have direct influence on the simulated ACF. Moreover, a linear fit is used to correct for "non-stationary effects" in the ACF that supposedly stem from cell-cycle dynamics. First, I don't think this terminology is really accurate, since non-stationarity would lead to an ACF that depends on two parameters (tau_1 and tau_2). I suppose the goal of the linear correction is to remove slow / static population heterogeneity? If yes, wouldn't it be easier / more direct to also change the simulations to non-synchronized cell-cycles? In this case, they should also display the very slow / static components as displayed in the data, which would eliminate the need for the post-hoc correction. I was also wondering whether other statistics (e.g., mean, variance, distributions) match between the simulations and the live-cell experiment? This could provide further validation of the inferred parameters.

-If I understood correctly, the signal intensity of the measured transcription spot is normalized by the median cytoplasmic spot brightness. Since the normalized intensity of a single complete transcript is 1, the cumulative intensity should give a lower bound on the nascent mRNAs. The histograms in Fig. 4b show intensity values in the range of 30, which would mean that at least 30 transcripts contribute to the transcription spot. The total number of nucleoplasmic and cytoplasmic mRNA, however, is in the range of 10 (Fig. 3a). I am probably missing something but how can we reconcile these numbers? The authors mention that the brightest spot just counts for one transcript, but argue that this has negligible influence on mature RNA counts. Could this be a possible explanation for the mismatch?

Minor comments:

-In the experimental case study, the authors argue that the "correct" inference result is the one that accounts for cell-cycle stage, while the other one termed "incorrect". I find this terminology too strong, since every estimate is subject to uncertainty.

-Page 2: "... in a asynchronous population" -> "... in an asynchronous population"

-Page 7: "...parameters sets 3 and 4" -> "...parameter sets 3 and 4"

-Figures 5a and 6a: parameter names and units should go on the y-axis.

Significance

Quantifying kinetic parameters from incomplete and noisy experimental data is a core problem in systems biology. I therefore consider this manuscript to be very relevant to this field. The contribution of this manuscript is largely methodological, although its potential usefulness is demonstrated using experimental data in yeast.

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Reply to the reviewers

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

In recent years, the field has investigated crosstalk between cGMP and cAMP signaling (PMID: 29030485), lipid and cGMP signaling (PMID: 30742070), and calcium and cGMP signaling (PMID: 26933036, 26933037). In contrast to the Plasmodium field, which has benefited from proteomic experiments (ex: PMID 24594931, 26149123, 31075098, 30794532), second messenger crosstalk in T. gondii has been probed predominantly through genetic and pharmacological perturbations. The present manuscript compares the features of A23187- and BIPPO-stimulated phosphoproteomes at a snapshot in time. This is similar to a dataset generated by two of the authors in 2014 (PMID: 24945436), except that it now includes one BIPPO timepoint. The sub-min​​ute phosphoproteomic timecourse following A23187 treatment in WT and ∆cdpk3 parasites is novel and would seem like a useful resource.

CDPK3-dependent sites were detected on adenylate cyclase, PI-PLC, guanylate cyclase, PDE1, and DGK1. This motivated study of lipid and cNMP levels following A23187 treatment. The four PDEs determined to have A23187-dependent phosphosites were characterized, including the two PDEs with CDPK3-dependent phosphorylation, which were found to be cGMP-specific. However, cGMP levels do not seem to differ in a CDPK3- or A23187-dependent manner. Instead, cAMP levels are elevated in ∆cdpk3 parasites. This would seem to implicate a feedback loop between CDPK3, the adenylyl cyclase, and PKA/PKG: CDPK3 activity reduces adenylyl cyclase activity, which reduces PKA activity, which increases PKG activity. The authors don't pursue this direction, and instead characterize PDE2, which does not have CDPK3-dependent phosphosites, and seems out of place in the study

Response:

We agree with reviewer 1 that a feedback loop between CDPK3, the adenylyl cyclase and PKA/PKG is certainly one of several possibilities (and we acknowledge this in the manuscript).

We felt, however, that given the observation that A23187 and BIPPO treatment leads to phosphorylation of numerous PDEs (hinting at the presence of an Ca2+-regulated feedback loop), it was entirely relevant to study these in greater detail. Coupled with the A23187 egress assay on ΔPDE2 parasites - our findings suggest that PDE2 plays an important role in this signalling loop (an entirely novel finding). While PDE2 appears to exert its effects in a CDPK3-independent manner (indeed suggesting that CDPK3 might exert its effects on cAMP levels in a different fashion), this does not detract from the important finding that PDE2 is one of the (likely numerous) components that is regulated in a Ca2+-dependent feedback loop to regulate egress.

We have modified our writing to better reflect the fact that our decision to pursue study of the PDEs was not solely CDPK3-centric.

While we feel that our reasoning for studying the PDEs is solid, we appreciate that further clarification on the putative CDPK3-Adenylate cyclase link would make it easier for the reader to follow the rationale.

We have not studied the direct link between CDPK3 and the Adenylate Cyclase β in more detail, as ACβ alone was shown to not play a major role in regulating lytic growth (Jia et al., 2017).

**MAJOR COMMENTS**

1.Some of the key conclusions are not convincing.

The data presented in Figure 6E, F, and G and discussed in lines 647-679 are incongruent. In Figure 6E, the plaques in the PDE2+RAP image are hardly visible; how can it be that the plaques were accurately counted and determined not to differ from vehicle-treated parasites?

Are the images in 6E truly representative? Was the order of PDE1 and PDE2 switched? The cited publication by Moss et al. 2021 (preprint) is not in agreement with this study, as stated. That preprint determined that parasites depleted of PDE2 had significantly reduced plaque number and plaque size (>95% reduction); and parasites depleted of PDE1 had a substantially reduced plaque size but a less substantial reduction in plaque number.

Response:

The plaques for PDE2+RAP were counted using a microscope since they are difficult to see by eye. We thank the reviewer for detecting our incorrect reference to Moss et al. (2021). This has been corrected in the text. We confirm, however, that the images in 6E are representative of what we observed and do indeed differ from what was seen by Moss et al.. We have acknowledged this clearly in the text.

The differences cannot easily be explained other than by the different genetic systems used. Further studies of the individual PDEs will likely illuminate their role in invasion/ growth, but we feel this would be beyond the scope of this study.

Unfortunately, the length of time required for PDE depletion (72h) is incompatible with most T. gondii cellular assays (typically performed within one lytic cycle, 40-48h). Although the authors performed the assays 3 days after initial RAP treatment, is there evidence that non-excised parasites don't grow out of the population. This should be straightforward to test: treat, wait 3 days, infect onto monolayers, wait 24-48h fix, and stain with anti-YFP and an anti-Toxoplasma counterstain. The proportion of the parasite population that had excised the PDE at the time of the cellular assays will then be known, and the reader will have a sense of how complete the observed phenotypes are. As a reader, I will regard the phenotypes with some level of skepticism due to the long depletion time, especially since a panel of PDE rapid knockdown strains (depletion in __Response:

1. Cellular assays using KO parasites are commonly performed at the point at which protein depletion is detected. Both our western blots and plaque assay results demonstrate that, at the point of assay, there is no substantial outgrowth of non-excised parasites. The original manuscript also includes PCRs performed at the 72 hr time point (See Fig. 6B) to support this.
2. We appreciate the reviewer’s comment re the panel of PDE KD strains. The reviewer notes that there are substantial limitations to conditional KO systems, which similarly applies to KD systems - there are notable pros and cons to each approach. When designing our strategy (pre-publication of the Moss et al., 2022), we made a deliberate decision to use conditional KO strains in light of the fact that residual protein levels in KD systems can cause significant problems, particularly for membrane proteins (all of the investigated PDEs have a transmembrane domain). Tagging of proteins with the degradation domain can have further issues, leading to protein mis-localisation, which we have experienced with several unrelated proteins in the lab.

   The authors should qualify some of their claims as preliminary or speculative, or remove them altogether.

The claims in lines 240-260 are confusing. It seems likely that the two drug treatments have at least topological distinctions in the signaling modules, given that cGMP-triggered calcium release is thought to occur at internal stores, whereas A23187-mediated calcium influx likely occurs first at the parasite plasma membrane.The authors' proposed alternative, that treatment-specific phosphosite behavior arises from experimental limitations and "mis-alignment", is unsatisfying for the following reasons: (1) From the outset, the authors chose different time frames to compare the two treatments (15s for BIPPO vs. 50s for A23187); (2) the experiment comprises a single time point, so it does not seem appropriate to compare the kinetics of phosphoregulation. There is still value in pointing out which phosphosites appear treatment-specific under the chosen thresholds, but further claims on the basis of this single-timepoint experiment are too speculative. Lines 264-267 and 281-284 should also be tempered.

Relatedly, graphing of the data in Figure 1G (accompanying the main text mentioned above) was confusing. Why is one axis a ratio, and the other log10 intensity? What does log10 intensity tell you without reference to the DMSO intensity? Wouldn't you want the L2FC(A23187) vs. L2FC(BIPPO) comparisons? Could you use different point colors to highlight these cases on plot 1E? Additionally, could you use a pseudocount to include peptides only identified in one treatment condition on the plot in 1E? (Especially since these sites are mentioned in lines 272-278 but are not on the plot)

Response:

1. The kinetics of the responses to A23187 and BIPPO are very different. This is why treatment timings are purposely different as they were selected to align pathways to a point where calcium levels peak just prior to calcium re-uptake. We make no mention of kinetic comparisons, and merely demonstrate that at the chosen timepoints, overall signalling correlation is very high. The observation that most of the sites that behave differently between conditions sit remarkably close to the threshold for differential regulation (in the treatment condition where they are not DR - see Fig. 1G) led us to speculate that many of these sites are likely on the cusp of differential regulation. While it is entirely possible that some of these differences are, in fact, treatment specific (and we clearly acknowledge this in the text), we simply state that we cannot confidently discern clear signalling features that allow us to distinguish between the two treatments. We feel that this is an entirely relevant observation given the observed preponderance of both A23187 and BIPPO-dependent DR phosphosites on proteins in the PKG signalling pathway (as current models place this upstream of Ca2+release).
2. Log10 intensity only serves to spread the data for easier visualisation. The only comparison being made relates to the LFCs. Fig. 1Gi shows the LFC scores (x axis) for all sites regulated following A23187 treatment (for which peptides were also identified in BIPPO treatment). On this plot we have highlighted the sites that are differentially regulated following BIPPO but not A23187 treatment (with red showing the DRup and blue showing the DRdown sites). This demonstrates that many of the sites that are regulated following BIPPO but not A23187 treatment cluster close to the threshold for differential regulation in the A23187 dataset - suggesting that many of these sites are likely on the cusp of differential regulation. Fig. 1Gii shows the reverse. While we could highlight the above-mentioned sites on the plot in Fig. 1E, we do not feel that it would demonstrate our point as clearly.

We feel that including a pseudocount on Fig. 1E for peptides lacking quantification in one treatment condition would be visually misleading as the direct correlation being made in Fig. 1E is BIPPO vs A23187 treatment. The sites mentioned in lines 272-278 in the original manuscript (now lines 268-276) are available in the supplement tables.

3.Additional experiments would be essential to support the main claims of the paper.

Genetic validation is necessary for the experiments performed with the PKA inhibitor H89. H89 is nonspecific even in mammalian systems (PMID: 18523239) and in this manuscript it was used at a high concentration (50 µM) The heterodimeric architecture of PKA in apicomplexans dramatically differs from the heterotetrameric enzymes characterized in metazoans (PMID: 29263246), so we don't know what the IC50 of the inhibitor is, or whether it inhibits competitively. Two inducible knockdown strains exist for PKA C1 (PMID: 29030485, 30208022). The authors could request one of these strains and construct a ∆cdpk3 in that genetic background, as was done for the PDE2 cKO strain. Estimated time: 3-4 weeks to generate strain, 2 weeks to repeat assays.

Response:

1. While we appreciate that H89 is not 100% specific for PKA, this is not our only line of evidence that cAMP levels are altered. We demonstrate that cAMP levels are elevated in CDPK3 KO parasites – further substantiating our finding.

The H89 concentration used in our experiment is in keeping with/lower than the concentrations used in other Toxoplasma publications (Jia et al., 2017), and both the Toxoplasma and Plasmodium fields have shown convincingly that H89 treatment phenocopies cKD/cKO of PKA (see Jia et al., 2017; Flueck et al., 2019).

While we agree that the genetic validation suggested by reviewer 1 would serve to further support our findings (though it would not provide further novel insights), the suggested time frame for experimental execution was not realistic. Line shipment, strain generation, subcloning and genetic validation would take substantially longer than 3-4 weeks.

cGMP levels are found to not increase with A23187 treatment, which is at odds with a previous study (lines 524-560). The text proposes that the differences could arise from the choice of buffer: this study used an intracellular-like Endo buffer (no added calcium, high potassium), whereas Stewart et al. 2017 used an extracellular-like buffer (DMEM, which also contains mM calcium and low potassium). An alternative explanation is that 60 s of A23187 treatment does not achieve a comparable amount of calcium flux as 15 s of BIPPO treatment, and a calcium-dependent effect on cGMP levels, were it to exist, could not be observed at the final timepoint in the assay. The experiments used to determine the kinetics of calcium flux following BIPPO and A23187 treatments (Fig. 1B, C) were calibrated using Ringer's buffer, which is more similar to an extracellular buffer (mM calcium, low potassium). In this buffer, A23187 treatment would likely stimulate calcium entry from across the parasite plasma membrane, as well as across the membranes of parasite intracellular calcium stores. By contrast, A23187 treatment in Endo buffer (low calcium) would likely only stimulate calcium release from intracellular stores, not calcium entry, since the calcium concentration outside of the parasite is low. Because calcium entry no longer contributes to calcium flux arising from A23187 treatment, it is possible that the calcium fluxes of A23187-treated parasites at 60 s are "behind" BIPPO-treated parasites at 15 s. The researchers could control these experiments by *either* (i) performing the cNMP measurements on parasites resuspended in the same buffer used in Figure 1B, C (Ringer's) or (ii) measuring calcium flux of extracellular parasites in Endo buffer with BIPPO and A23187 to determine the "alignment" of calcium levels, as was done with intracellular parasites in Figure 1C. No new strains would have to be generated and the assays have already been established in the manuscript. Estimated time to perform control experiments with replicates: 2 weeks. This seems like an important control, because the interpretation of this experiment shifts the focus of the paper from feedback between calcium and cGMP signaling, which had motivated the initial phosphoproteomics comparisons, to calcium and cAMP signaling. Further, the lipidomics experiments were performed in an extracellular-like buffer, DMEM, so it's unclear why dramatically different buffers were used for the lipidomics and cNMP measurements.

Response:

While the initial calibration experiments to measure calcium flux were indeed performed in Ringer’s buffer, the parasites were intracellular. We therefore chose to measure cNMP concentrations of extracellular parasites syringe lysed in Endo buffer, which is better at mimicking intracellular conditions than any other described buffer.

As the reviewer suggested, we measured the calcium flux of extracellular parasites in Endo buffer upon stimulation with either A23187 or BIPPO.

We found that peak calcium response to BIPPO in Endo buffer was similar to that of intracellular parasites (~15 seconds post treatment) (See Supp Fig. 6A). Upon treatment with A23187, extracellular parasites in Endo buffer had a much faster response compared to their intracellular counterparts, with peak flux measured at ~25 seconds post treatment (see Supp Fig. 6B). This indeed does suggest that extracellular parasites in Endo buffer behave differently to A23187 compared to their intracellular counterparts. However, peak calcium response is still occuring within the experimental time course and is not being missed, as the reviewer worries. Moreover, since we are able to detect increased cAMP levels in A23187 treated parasites, Ca2+ flux appears sufficient to alter cNMP signalling.

We did notice however that the intensity of the calcium flux was much weaker in Endo buffer compared to intracellular parasites (see Supp Fig. 6B). We found that this was due to the lack of host-derived Ca2+, since supplementation of Endo buffer with 1 uM CaCl2 restored the intensity of the calcium response to match that of intracellular parasites (see Supp Fig. 6C). We therefore decided to repeat our cGMP measurements, this time using extracellular parasites in Endo buffer supplemented with 1 uM CaCl2. However, we found no differences in cGMP levels in the response to ionophore under these conditions (now Supp Fig. 6D) compared to the previous experiments, so the conclusions from the previous data do not change.

As for the lipidomics experiments, we chose to use DMEM so that our dataset could be compared with other published lipidomic datasets (Katris et al., 2020; Dass et al., 2021) where DMEM was also used as a buffer when measuring global lipid profiles of parasites.

We now acknowledge in the paper that Endo buffer has its shortcomings, and that this could be the reason why we do not detect changes in cGMP concentrations. We do, however, believe that Endo buffer is the best alternative to intracellular parasites and is supported by its consistent use in numerous publications studying Toxoplasma signalling (McCoy et al., 2012; Stewart et al., 2017).

Additional information is required to support the claim that PDE2 has a moderate egress defect (lines 681-687). T. gondii egress is MOI-dependent (PMID: 29030485). Although the parasite strains were used at the same MOI, there is no guarantee that the parasites successfully invaded and replicated. If parasites lacking PDE2 are defective in invasion or replication, the MOI is effectively decreased, which could explain the egress delay. Could the authors compare the MOIs (number of vacuoles per host cell nuclei) of the vehicle and RAP-treated parasites at t = 0 treatment duration to give the reader a sense of whether the MOIs are comparable?

Response:

Since PDE2 KO parasites have a substantial growth defect, we did notice that starting MOIs were consistently lower for the RAP-treated samples compared to the DMSO-treated samples. However, this was also the case for PDE1 KO parasites where we did not see an egress delay. We also found that the egress delay was still evident for ∆CDPK3 parasites, despite having higher starting MOIs than WT parasites in our experiments. Therefore there does not appear to be a link between starting MOIs and the egress delay.

To be sure of our results, we also performed egress assays where we co-infected HFFs with mCherry-expressing WT parasites (WT ∆UPRT) and GFP-expressing PDE2 cKO parasites that were treated with either DMSO or RAP or ∆CDPK3 parasites. This recapitulated our previous findings, confirming the deletion of PDE2 leads to delay in A23187-mediated egress.

4.A few references are missing to ensure reproducibility.

The manuscript states that the kinetic lipidomics experiments were performed with established methods, but the cited publication (line 497) is a preprint. These are therefore not peer reviewed and should be described in greater detail in this manuscript, including any relevant validation.

Response:

We thank the reviewer for pointing this out. We have included a greater description of the methods used in the materials and methods section such that the experiment is reproducible, as per the reviewer’s suggestion. We decided to still make mention of the BioRxiv preprint since we thought it was appropriate for the reader to be informed of ongoing developments in the field.

Please cite the release of the T. gondii proteomes used for spectrum matching (lines 972-973).

Response:

We have included this as per the reviewer’s suggestion.

Please include the TMT labeling scheme so the analysis may be reproduced from the raw files.

Response:

We have included this as per the reviewer’s suggestion in Supp Fig. 3A.

5.Statistical analyses should be reviewed as follows:

Have the authors examined the possibility that some changes in phosphopeptide abundance reflect changes in protein abundance? This may be particularly relevant for comparisons involving the ∆cdpk3 strain. Did the authors collect paired unenriched proteomes from the experiments performed? Alternatively, there may be enriched peptides that did not change in abundance for many of the proteins that appear dynamically phosphorylated.

Response:

We did not collect unenriched proteomes from the experiments performed (although we did perform unenriched mixing checks to ensure equal loading between samples), and believe that this wasn’t a necessity for the following reasons:

1. For within-line treatment analyses, treatment timings are so short (a maximum of 15-50s in the single timepoint experiment) that it would be unlikely to detect substantial changes in protein abundance. Moreover, these unlikely events would affect all phosphosites across a protein, and therefore be detectable.

In our CDPK3 dependency timecourse experiments, we normalise both the WT and ∆CDPK3 strain to 0s, and measure signalling progression over time. Therefore, any difference at timepoints that are not “0” are not originating from basal differences. We also see a consistent increase/decrease in phosphosite detection across the sub-minute timecourse, further confirming that the observed changes are truly down to dynamic changes in phosphorylation and not protein levels.

In the single timepoint CDPK3 dependency analyses (44 regulated sites identified, Data S2), we acknowledge that there could be some risk of altered starting protein abundance between lines. However, if protein abundance were responsible for the changes in phosphosite detection, we would expect all phosphosites across the protein to shift, and we do not observe this. Moreover, when we look at these CDPK3 dependent proteins and compare their phosphosite abundance in untreated WT and ∆CDPK3 lines, we find that for each protein, either all or the majority of phosphosites detected are unchanged (highlighting that there is no substantial difference in this protein’s abundance between lines). Where there are phosphosite differences between lines, these are only ever on single sites on a protein while most other sites are unchanged - implying that these are changes to basal phosphorylation states and not protein levels.

It seems like for Figs. 3B and S5 the maximum number of clusters modeled was selected. Could the authors provide a rationale for the number of clusters selected, since it appears many of the clusters have similar profiles.

The number of clusters is chosen automatically by the Mclust algorithm as the value that maximizes the Bayes Information Criterion (BIC). BIC in effect balances gains in model fit (increasing log-likelihood) against increasing the number of parameters (i.e. number of clusters).

Please include figure panel(s) relating to gene ontology. Relevant information for readers to make conclusions includes p-value, fold-enrichment or gene ratio, and some sort of metric of the frequency of the GO term in the surveyed data set. See PMID: 33053376 Fig. 7 and PMID: 29724925 Fig. 6 for examples or enrichment summaries. Additionally, in the methods, specify (i) the background set, (ii) the method used for multiple test correction, (iii) the criteria constituting "enrichment", (iv) how the T. gondii genome was integrated into the analysis, (v) the class of GO terms (molecular function, biological process, or cellular component), (vi) any additional information required to reproduce the results (for example, settings modified from default).

Response:

We have included the additional information requested in the materials and methods.

We purposely did not include GO figure panels as our analyses are being done across many clusters, making it very difficult to display this information cohesively. We have included all data in Tables S2-S5. These tables included all the relevant information on p-value, enrichment status, ratio in study/ratio in population, class of GO terms etc.

The presentation of the lipidomics experiments in Figure 4A-C is confusing. First, the ∆cdpk3/WT ratio removes information about the process in WT parasites, and it's unclear why the scale centers on 100 and not 1. Second, the data in Figure S6 suggests a more modest effect than that represented in Fig. 4; is this due to day to day variability? How do the authors justify pairing WT and mutant samples as they did to generate the ratios?

Response:

This is a common strategy used by many metabolomics experts (Bailey et al., 2015; Dass et al., 2021; Lunghi et al., 2022). We had originally chosen to represent the data as a ratio since this form of representation helps get rid of the variability that arises between experiments and allows us to see very clear patterns which would otherwise go unnoticed. This variability arises from the amount of lipids in each sample which varies between parasites in a dish, the batch of FBS and DMEM used, and the solutions and even room temperature used to extract lipids on a given day.

However, we agree with the reviewer that depicting the data in Figure 4A-C as a ratio of ∆CDPK3/WT parasites can be confusing, so we have now changed the graphs, plotting WT and ∆CDPK3 levels instead, and have moved the ratio of ∆CDPK3/WT to the Supplementary Figure 5.

The significance test seems to be performed on the difference between the WT and ∆cdpk3 strains, but not relative to the DMSO treatment? Wouldn't you want to perform a repeated measures ANOVA to determine (i) if lipid levels change over time and (ii) if this trend differs in WT vs. mutant strain?

Response:

The reviewer correctly points out that ANOVA is often used for time courses, but we must point out that it is not always strictly appropriate since it can overlook the purpose of the individual experiment design, which in this case is, 1) to investigate the role of CDPK3 compared to the WT parental strain, and 2) specifically to find the exact point at which the DAG begins to change after stimulus to match the proteomics time course.

Our data is clearly biassed towards earlier time points where we have 0, 5, 10, 30, 45 seconds where DAG levels are mostly unchanged compared to the single timepoint 60 seconds which shows a significant difference in DAG using our method of statistical comparison by paired two tailed t-test. Therefore, it would be unwise to use ANOVA when we really want to see when the A23187 stimulus takes effect, which appears to be after the 45 second mark. Therefore, analysing the data by ANOVA would likely provide a false negative result, where the result is non-significant but there is clearly more DAG in WT than CDPK3 after 60 seconds. T-tests are commonly used when comparing the same cell lines grown in the same conditions with a test/treatment, and in this case the test/treatment is CPDK3 present or absent (Lentini et al., 2020).

In the main text, it would be preferable to see the data presented as the proteomics experiments were in Figure 4B and 4C, with fold changes relative to the DMSO (t = 0) treatment, separately for WT and ∆cdpk3 parasites.

Response:

We have now changed the way that we represent the data, plotting %mol instead of the ratio.

Signaling lipids constitute small percentages of the overall pool (e.g. PMID: 26962945), so one might not necessarily expect to observe large changes in lipid abundance when signaling pathways are modulated. Is there any positive control that the authors could include to give readers a sense of the dynamic range? Maybe the DGK1 mutant (PMID: 26962945)?

Response:

DGK1 is maybe not a good example because the DGK1 KO parasites effectively “melt” from a lack of plasma membrane integrity ((Bullen et al., 2016), so this would likely be technically challenging. We don’t see the added value in including an additional mutant control since we can already see the dynamic change over time from no difference (0 seconds) to significant difference (60 seconds) between WT and CDPK3 for DAG and most other lipids. We already see a significant difference between WT and CDPK3 after 60 seconds for DAG, and we can clearly see in sub-minute timecourses the changes or not at the specific points where the A23187 is added (0-5 seconds), the parasites acclimatise, for the A23187 to take effect (10-30 seconds) and for the parasite lipid response to be visible by lipidomics (45-60 +seconds).

Figure 4E: are the differences in [cAMP] with DMSO treatment and A23187 treatment different at any of the timepoints in the WT strain? The comparison seems to be WT/∆cdpk3 at each timepoint. Does the text (lines 562-568) need to be modified accordingly?

Response:

In WT (and ∆CDPK3) parasites, [cAMP] is significantly changed at 5s of A23187 treatment (relative to DMSO). We have modified our figures to include this analysis. The existing text accurately reflects this.

Figure 6I: is the difference between PDE2 cKO/∆cdpk3 + DMSO or RAP significant?

Response

In our original manuscript, there was no statistical difference in [cAMP] between PDE2cKO/∆CDPK3+DMSO and PDE2cKO/∆CDPK3+DMSO+RAP, likely due to the variation between biological replicates. To overcome the issues in variability between replicates, we have now included more biological replicates (n=7). This has led to a significant difference in [cAMP] between PDE2cKO/∆CDPK3 DMSO- and RAP-treated parasites and between PDE2cKO DMSO- and RAP-treated parasites (now Fig. 6I).

**MINOR COMMENTS**

1.The following references should be added or amended:

Lines 83-85: in the cited publication, relative phosphopeptide abundances of an overexpressed dominant-negative, constitutively inactive PKA mutant were compared to an overexpressed wild-type mutant. In this experimental setup, one would hypothesize that targets of PKA should be down-regulated (inactive/WT ratios). However, the mentioned phosphopeptide of PDE2 was found to be up-regulated, suggesting that it is not a direct target of PKA.

Response:

We thank the reviewer for spotting this error, we have now modified our wording.

Cite TGGT1_305050, referenced as calmodulin in line 458, as TgELC2 (PMID: 26374117).

Response:

We have included this as per the reviewer’s suggestion.

Cite TGGT1_295850 as apical annuli protein 2 (AAP2, PMID: 31470470).

Response:

We have included this as per the reviewer’s suggestion.

Cite TGGT1_270865 (adenylyl cyclase beta, Acβ) as PMID: 29030485, 30449726.

Response:

We have included this as per the reviewer’s suggestion.

Cite TGGT1_254370 (guanylyl cyclase, GC) as PMID: 30449726, 30742070.

Response:

We have included this as per the reviewer’s suggestion.

Note that Lourido, Tang and David Sibley, 2012 observed that treatment with zaprinast (a PDE inhibitor) could overcome CDPK3 inhibition. The target(s) of zaprinast have not been determined and may differ from those of BIPPO (in identity and IC50). The cited study also used modified CDPK3 and CDPK1 alleles, rather than ∆cdpk3 and intact cdpk1 as used in this manuscript. That is to say, the signaling backgrounds of the parasite strains deviate in ways that are not controlled.

Response:

While it is true that zaprinast targets have not been unequivocally identified, zaprinast-induced egress is widely thought to be the result of PKG activation, a conclusion that is further supported by the finding that Compound 1 completely blocks zaprinast-induced egress (Lourido, Tang and David Sibley, 2012). Similarly, BIPPO-induced egress is inhibited by chemical inhibition of PKG by Compound 1 and Compound 2 (Jia et al., 2017). Moreover, like zaprinast, BIPPO has been clearly shown to partially overcome the ∆CDPK3 egress delay (Stewart et al., 2017).

2.The following comments refer to the figures and legends:

Part of the legend text for 1G is included under 1H.

Response:

This has been corrected

Figure 1H: The legend mentions that some dots are blue, but they appear green. Please ensure that color choices conform to journal accessibility guidelines. See the following article about visualization for colorblind readers: https://www.ascb.org/science-news/how-to-make-scientific-figures-accessible-to-readers-with-color-blindness____/ . Avoid using red and green false-colored images; replace red with a magenta lookup table. Multi-colored images are only helpful for the merged image; otherwise, we discern grayscale better. Applies to Figures 1B, 5C, 6D. (Aside: anti-CAP seems an odd choice of counterstain; the variation in the staining, esp. at the apical cap, is distracting.)

Response:

We thank reviewer #1 for bringing this to our attention, and have modified our colour usage for all IFAs and Figures 1H and 3E.

We chose CAP staining as the antibody is available in the laboratory and stains both the apical end (which has been shown to contain several proteins important for signalling as well as PDE9) and the parasite periphery, the location of CDPK3.

Figure 1B: When showing a single fluorophore, please use grayscale and include an intensity scale bar, since relative values are being compared.

Response:

We have modified this as per the reviewer’s suggestion

Figure 1C: it is difficult to compare the kinetics of the calcium response when the curves are plotted separately. Since the scales are the same, could the two treatments be plotted on the same axes, with different colors? Additionally, according to the legend, a red line seems to be missing in this panel.

Response:

Fig1C is not intended to compare kinetics, merely to show peak calcium release in each separate treatment condition. We have removed mention of a red line in the figure legend.

Figure 2A: Either Figure S4 can be moved to accompany Figure 2A, or Figure 2A could be moved to the supplemental.

Figure S4 has now been incorporated into Figure 2.

Reviewer #1 (Significance (Required)):

This manuscript would interest researchers studying signaling pathways in protozoan parasites, especially apicomplexans, as CDPK3 and PKG orthologs exist across the phylum. To my knowledge, it is the first study that has proposed a mechanism by which a calcium effector regulates cAMP levels in T. gondii. Unfortunately, the experiments fall short of testing this mechanism.

Response:

We thank reviewer #1 for their comments, but disagree with their assessment that the key points of the manuscript “fall short of experimental testing”.

1. We demonstrate that, following both BIPPO and A23187 treatment, there is differential phosphorylation of numerous components traditionally believed to sit upstream of PKG activation (as well as several components within the PKG signalling pathway itself).
2. We show that some of these sites are CDPK3 dependent, and that deletion of CDPK3 leads to changes in lipid signalling and an elevation in levels of cAMP (dysregulation of which is known to alter PKG signalling).
3. We show that pre-treatment with a PKA inhibitor is able to largely rescue this phenotype.
4. We demonstrate that a cAMP-specific PDE is phosphorylated following A23187 treatment (i.e. Ca2+ flux)
5. We show that this cAMP specific PDE plays a role in A23187-mediated egress.
6. While the latter PDE may not be directly regulated by CDPK3, these findings suggest that there are likely several Ca2+-dependent kinases that contribute to this feedback loop.

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

**Summary:**

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

In this manuscript, Dominicus et al investigate the elusive role of calcium-dependent kinase 3 during the egress of Toxoplasma gondii. Multiple functions have already been proposed for this kinase by this group including the regulation of basal calcium levels (24945436) or of a tyrosine transporter (30402958). However, one of the most puzzling phenotypes of CDPK3 deficient tachyzoites is a marked delay in egress when parasites are stimulated with a calcium ionophore that is rescued with phosphodiesterase (PDE) inhibitors. Crosstalk between, cAMP, cGMP, lipid and calcium signalling has been previously described to be important in regulating egress (26933036, 23149386, 29030485) but the role of CDPK3 in Toxoplasma is still poorly understood.

Here the authors first take an elegant phosphoproteomic approach to identify pathways differentially regulated upon treatment with either a PDE inhibitor (BIPPO) and a calcium ionophore (A23187) in WT and CDPK3-KO parasites. Not much difference is observed between BIPPO or A23187 stimulation which is interpreted by the authors as a regulation through a feed-back loop.

The authors then investigate the effect of CDPK3 deletion on lipid, cGMP and cAMP levels. The identify major changes in DAG, phospholipid, FFAs, and TAG levels as well as differences in cAMP levels but not for cGMP. Chemical inhibition of PKA leads to a similar egress timing in CDPK3-KO and WT parasites upon A23187 stimulation.

As four PDEs appeared differentially regulated in the CDPK3-KO line upon A23187, the authors investigate the requirement of the 4 PDEs in cAMP levels. They show diverse localisation of the PDEs with specificities of PDE1, 7 and 9 for cGMP and of PDE2 for cAMP. They further show that PDE1, 7 and 9 are sensitive to BIPPO. Finally, using a conditional deletion system, they show that PDE1 and 2 are important for the lytic cycle of Toxoplasma and that PDE2 shows a slightly delayed egress following A23187 stimulation.

**Major comments:**

-Are the key conclusions convincing?

The title is supported by the findings presented in this study. However I am not sure to understand why the authors imply a positive feed back loop. This should be clarified in the discussion of the results.

Response:

We believe in a positive feedback loop as, upon A23187 treatment (resulting in a calcium flux), ΔCDPK3 parasites are able to egress, albeit in a delayed manner. This egress delay is substantially, but not completely, alleviated upon treatment with BIPPO (a PDE inhibitor known to activate the PKG signalling pathway). In conjunction with our phosphoproteomic data (where we see phosphorylation of numerous pathway components upstream of PKG upon BIPPO and A23187 treatment - both in a CDPK3 dependent and independent manner), these observations suggest that calcium-regulated proteins (CDPK3 among them) feed into the PKG pathway. As deletion of CDPK3 delays egress, it is reasonable to postulate that this feedback is one that amplifies egress signalling (i.e. is positive).

The phosphoproteome analysis seems very strong and will be of interest for many groups working on egress. However, the key conclusion, i.e. that a substrate overlaps between PKG and CDPK3 is unlikely to explain the CDPK3 phenotype, seems premature to me in the absence of robustly identified substrates for both kinases.

Response:

We certainly do not fully exclude the possibility of a substrate overlap but do lean more heavily towards a feedback loop given (a) the inability to clearly detect treatment-specific signalling profiles and (b) the phospho targets observed in the A23187 and BIPPO phosphoproteomes. We have further clarified our reasoning, and overall tempered our language in the manuscript as per the reviewer’s suggestion.

I am not sure there is a clear key conclusion from the lipidomic analysis and how it is used by the authors to build their model up. Major changes are observed but how could this be linked with CDPK3, particularly if cGMP levels are not affected?

Response:

Our phosphoproteomic analyses identify several CDPK3-dependent phospho sites on phospholipid signalling components (DGK1 & PI-PLC), suggesting that there is indeed altered signalling downstream of PKG. To test whether these lead to a measurable phenotype, we performed the lipidomics analysis. We did not pursue this arm of the signalling pathway any further as we postulated that the changes in the lipid signalling pathway were less likely to play a role in the feedback loop. Nevertheless, we felt that it was worthwhile to include these findings in our manuscript as they support the conclusions drawn from the phosphoproteomics - namely that lipid signalling is perturbed in CDPK3 mutants. We, or others, may follow up on this in future.

We agree with the reviewer that it is surprising that cGMP levels remain unchanged in our experiments when we treat with A23187. Given the measurable difference in cAMP levels between WT and ΔCDPK3 parasites, we postulate that CDPK3 directly or indirectly downregulates levels of cAMP. This would, in turn, alter activity of the cAMP-dependent protein kinase PKAc. Jia et al. (2017) have shown a clear dependency on PKG for parasites to egress upon PKAc depletion, but were also unable to reliably demonstrate cGMP accumulation in intracellular parasites. Similarly, their hypothesis that dysregulated cGMP-specific PDE activity results in altered cGMP levels has not been proven (the PDE hypothesised to be involved has since been shown to be cAMP-specific).

While it is possible that our collective inability to observe elevated cGMP levels is explained by the sensitivity limits of the assay, it is similarly possible that cAMP-mediated signalling is exerting its effects on the PKG signalling pathway in a cGMP-independent manner.

The evidence that CDPK3 is involved in cAMP homeostasis seems strong. However, the analysis of PKA inhibition is a bit less clear. The way the data is presented makes it difficult to see whether the treatment is accelerating egress of CDPK3-KO parasites or affecting both WT and CDPK3-KO lines, including both the speed and extent of egress. This is important for the interpretation of the experiment.

Response:

Fig. 4F shows that there is a significant amount of premature egress in both WT and ∆CDPK3 parasites following 2 hrs of H89 pre-treatment (consistent with previous reports that downregulation of cAMP signalling stimulates premature egress). When we subsequently investigated A23187-induced egress rates of the remaining intracellular H89 pre-treated parasites (Fig. 4Gi-ii) we found that the ∆CDPK3 egress delay was largely rescued. We have moved Fig. 4F to the supplement (now Supp Fig. 5E) in order to avoid confusion between the distinct analyses shown in 4F (pre-treatment analyses) and 4G (egress experiment). These experiments provided a hint that cAMP signalling is affected, which we then validate by measuring elevated cAMP levels in CDPK3 mutant parasites.

The biochemical characterisation of the four PDE is interesting and seems well performed. However, PDE1 was previously shown to hydrolyse both cAMP and cGMP (____https://doi.org/10.1101/2021.09.21.461320____) which raises some questions about the experimental set up. Could the authors possibly discuss why they do not observe similar selectivity? Could other PDEs in the immunoprecipitate mask PDE activity? In line with this question, it is not clear what % of "hydrolytic activity (%)" means and how it was calculated.

The experiments describing the selectivity of BIPPO for PDE1, 7 and 9 as well as the biological requirement of the four tested PDEs are convincing.

Response:

We believe that the disagreement between our findings and those published by Moss and colleagues are due to the differences in experimental conditions. We performed our assays at room temperature for 1 hour with higher starting cAMP concentrations (1 uM) compared to them. They performed their assays at 37ºC for 2 hours with 10-fold lower starting cAMP concentrations (0.1 uM). We have now repeated this set of experiments using the Moss et al. conditions, and find that PDEs 1, 7 and 9 can be dual specific, while PDE2 is cAMP-specific, thereby recapitulating their findings (Now included in the revised manuscript under Supp Fig. 7B). However, we also now performed a timecourse PDE assay using our original conditions and show that the cAMP hydrolytic activity for PDE1 can only be detected following 4 hours of incubation, compared to cGMP activity that can be detected as early as 30 minutes, suggesting that it possesses predominantly cGMP activity (See Supp Fig. 7C). We therefore believe that our experimental setup is more stringent, because if one starts with a lower level of substrate and incubates for longer and at a higher temperature, even minor dual activity could make a substantial difference in cAMP levels. Our data suggests that the cAMP hydrolytic activity of PDEs 1, 7 and 9 is substantially lower than the cGMP hydrolytic activity that they display.

We have also included a clear description of how % hydrolytic activity was calculated in the methods section.

-Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The claim that CDPK3 affects cAMP levels seems strong however the exact links between CDPK3 activity, lipid, cGMP and cAMP signalling remain unclear and it may be important to clearly state this.

Response:

We have modified our wording in the text to more clearly describe our current hypothesis and reasoning.

-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 think that the manuscript contains a significant amount of experiments that are of interest to scientists working on Toxoplasma egress. Requesting experiments to identify the functional link between above-mentioned pathways would be out of the scope for this work although it would considerably increase the impact of this manuscript. For example, would it be possible to test whether the CDPK3-KO line is more or less sensitive to PKG specific inhibition upon A23187 induced?

-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 above-mentioned experiment is not trivial as no specific inhibitors of PKG are available. Ensuring for specificity of the investigated phenotype would require the generation of a resistant line which would require significant work.

__Response: __We agree that this would be an interesting experiment to further substantiate our findings. As indicated by the reviewer, however, the lack of specific inhibitors of PKG means a resistant line would likely be required to ensure specificity.

-Are the data and the methods presented in such a way that they can be reproduced?

It is not clear how the % of hydrolytic activity of the PDE has been calculated.

Response: We have included a clearer description of how % hydrolytic activity was calculated in the methods section.

-Are the experiments adequately replicated and statistical analysis adequate?

This seems to be performed to high standards.

**Minor comments:**

-Specific experimental issues that are easily addressable.

I do not have any comments related to minor experimental issues.

-Are prior studies referenced appropriately?

Most of the studies relevant for this work are cited. It is however not clear to me why some important players of the "PKG pathway" are not indicated in Fig 1H and Fig 3E, including for example UGO or SPARK.

Response:

We have modified Fig 1H and 3E to include all key players involved in the PKG pathway.

-Are the text and figures clear and accurate?

While all the data shown here is impressive and well analysed, I find it difficult to read the manuscript and establish links between sections of the papers. The phosphoproteome analysis is interesting and is used to orientate the reader towards a feedback mechanism rather than a substrate overlap. But why do the authors later focus on PDEs and not on AC or CNBD, as in the end, if I understand well, there is no evidence showing a link between CDPK3-dependent phosphorylation and PDE activity upon A23187 stimulation?

Response:

We thank reviewer#2 and appreciate their constructive feedback re the flow of the manuscript.

Our key findings from the phosphoproteomics study were that 1) BIPPO and A23187 treatment trigger near identical signalling pathways, 2) that both A23187 and BIPPO treatment leads to phosphorylation of numerous components both upstream and downstream of PKG signalling (hinting at the presence of an Ca2+-regulated feedback loop) and 3) several of the abovementioned components are phosphorylated in a CDPK3 dependent manner.

While several avenues of study could have been pursued from this point onwards, we chose to focus on the feedback loop in a broader sense as its existence has important implications for our general understanding of the signalling pathways that govern egress.

We reasoned that, given the differential phosphorylation of 4 PDEs following A23187 and BIPPO treatment (none of which had been studied in detail previously), it was relevant to study these in greater detail.

Coupled with the A23187 egress assay on PDE2 knockout parasites - our findings suggest that PDE2 plays a role in the abovementioned Ca2+ signalling loop. While PDE2 may not exert its effects in a CDPK3-dependent manner (and CDPK3 may, therefore, alter cAMP levels in a different fashion), this does not detract from the important finding that PDE2 is one of the (likely numerous) components that is regulated in a Ca2+-dependent feedback loop to facilitate rapid egress.

We have modified our wording to better reflect our rationale for studying the PDEs irrespective of their CDPK3 phosphorylation status.

While we feel that our reasoning for studying the PDEs is solid, we do appreciate that further clarification on the putative CDPK3-Adenylate cyclase link would elevate the manuscript substantially. However, given the data that the ACb is not playing a sole role in the control of egress, this is likely a non-trivial task and requires substantial work.

It is also unclear how the authors link CDPK3-dependent elevated cAMP levels with the elevated basal calcium levels they previously described. This is particularly difficult to reconcile particularly in a PKG independent manner.

Response:

We previously postulated that elevated Ca2+ levels allowed ΔCDPK3 mutants to overcome a complete egress defect, potentially by activating other CDPKs (e.g. CDPK1). It is similarly plausible that elevated Ca2+ levels in ΔCDPK3 parasites may lead to elevated cAMP levels in order to prevent premature egress.

As noted in our previous responses, we acknowledge that our inability to detect cGMP is surprising. However, given the clarity of our cAMP findings, and the phosphoproteomic evidence to suggest that various components in the PKG signalling pathway are affected, we postulate that we are either unable to reliably detect cGMP due to sensitivity issues, or that cAMP is exerting its regulation on the PKG pathway in a cGMP-independent manner. As noted previously, while the link between cAMP and PKG signalling has been demonstrated by Jia et al., it is not entirely clear how this is mediated.

The presentation of the lipidomic analysis is also not really clear to me. Why do the authors show the global changes in phospholipids and not a more detailed analysis?

Response:

We performed a detailed phospholipid profile of WT and ∆CDPK3 parasites under normal culture conditions. However, due to the sheer quantity of parasites required for this detailed analysis, we were unable to measure individual phospholipid species in our A23187 timecourse. We therefore opted to measure global changes following A23187 stimulation.

As the authors focus on the PI-PLC pathway, could they detail the dynamics of phosphoinositides? I understand that lipid levels are affected in the mutant but I am not sure to understand how the authors interpret these massive changes in relationship with the function of CDPK3 and the observed phenotypes.

Response:

Our phosphoproteomic analyses identified several CDPK3-dependent phospho sites on phospholipid signalling components (DGK1 & PI-PLC), suggesting that (in keeping with all of our other data), there is altered signalling downstream of PKG. To test whether these changes lead to a measurable phenotype, we performed the lipidomics analysis. Following stimulation with A23187, we found a delayed production of DAG in ∆CDPK3 parasites compared to WT parasites. Since DAG is required for the production of PA, which in turn is required for microneme secretion, our finding can explain why microneme secretion is delayed in ∆CDPK3 parasites, as previously reported (Lourido, Tang and David Sibley, 2012; McCoy et al., 2012).

We did not follow this arm of the signalling pathway any further as we postulated that the changes in the lipid signalling pathway were less likely to play a role in the feedback loop. Nevertheless, we felt that it was worthwhile to include these findings in our manuscript as they support the conclusions drawn from the phosphoproteomics - namely that lipid signalling is perturbed in CDPK3 mutants. We, or others, may follow up on this in future.

Finally, the characterisation of the PDEs is an impressive piece of work but the functional link with CDPK3 is relatively unclear. It would also be important to clearly discuss the differences with previous results presented in this this preprint: https://doi.org/10.1101/2021.09.21.461320____.

My understanding is while the authors aim at investigating the role of CDPK3 in A23187 induced egress, the main finding related to CDPK3 is a defect in cAMP homeostasis that is not linked to A23187. Similarly, the requirements of PDE2 in cAMP homeostasis and egress is indirectly linked to CDPK3. Altogether I think that important results are presented here but divided into three main and distinct sections: the phosphoproteomic survey, the lipidomic and cAMP level investigation, and the characterisation of the four PDEs. However, the link between each section is relatively weak and the way the results are presented is somehow misleading or confusing.

Response:

As mentioned in a previous response, we chose to study PDEs in greater detail because of our observation that both A23187 and BIPPO treatments lead to their phosphorylation (hinting at the presence of a Ca2+regulated feedback loop). We were particularly intrigued to study the cAMP specific PDE, as CDPK3 KO parasites suggested that cAMP may play a role in the Ca2+ feedback mechanism. As PDE2 may not be directly regulated by CDPK3, Ca2+ appears to exert its feedback effects in numerous ways. We have modified our wording to better reflect our rationale for studying the PDEs irrespective of their CDPK3 phosphorylation status.

-Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This is a very long manuscript written for specialists of this signalling pathway and I would suggest the authors to emphasise more the important results and also clearly state where links are still missing. This is obviously a complex pathway and one cannot elucidate it easily in a single manuscript.

Response:

We have included an additional summary in our conclusions to better illustrate our findings and clarify any missing links.

Reviewer #2 (Significance (Required)):

-Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This is a technically remarkable paper using a broad range of analyses performed to a high standard.

-Place the work in the context of the existing literature (provide references, where appropriate).

The cross-talk between cAMP, cGMP and calcium signalling is well described in Toxoplasma and related parasites. Here the authors show that, in Toxoplasma, CDPK3 is part of this complex signalling network. One of the most important finding within this context is the role of CDPK3 in cAMP homeostasis. With this in mind, I would change the last sentence of the abstract to "In summary we uncover a feedback loop that enhances signalling during egress and links CDPK3 with several signalling pathways together."

Response:

In light of feedback received from several reviewers, we have made our wording less CDPK3 centric - as our findings relate in part to CDPK3 and, in a broader sense, to a Ca2+ driven feedback loop.

The genetic and biochemical analyses of the four PDEs are remarkable and highlight consistencies and inconsistencies with recently published work that would be important to discuss and will be of interest for the field.

__Response: __We thank reviewer#2 and agree that the PDE findings are of significant importance to the field.

While I understand the studied signalling pathway is complex, I think it would be important to better describe the current model of the authors. In the discussion, the authors indicate that "the published data is not currently supported by a model that fits most experimental results." I would suggest to clarify this statement and discuss whether their work helps to reunite, correct or improve previous models.

__Response: __We have expanded on the abovementioned statement to clarify that the presence of a feedback loop is a major pillar of knowledge required for the complete interpretation of existing signalling data.

Could the authors also speculate about a potential role of PDE/CDPK3 in host cell invasion as cAMP signalling has be shown to be important for this process (30208022 and 29030485)?

__Response: __Existing literature (Jia et al., 2017) suggests that perturbations to cAMP signalling play a very minor role in invasion since parasites where either ACα or ACβ are deleted show no impairment in invasion levels. We currently do not have substantial data on invasion, and are not sure that pursuing this is valuable given the minor phenotypes observed in other studies.

-State what audience might be interested in and influenced by the reported findings.

This paper is of great interest to groups working on the regulation of egress in Toxoplasma gondii and other related apicomplexan pathogens.

-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.

I am working on the cell biology of apicomplexan parasites.

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

**Summary:**

Dominicus et al aimed to identify the intersecting components of calcium, cyclic nucleotides (cAMP, cGMP) and lipid signaling through phosphoproteomic, knockout and biochemical assays in an intracellular parasite, Toxoplasma gondii, particularly when its acutely-infectious tachyzoite stage exits the host cells. A series of experimental strategies were applied to identify potential substrates of calcium-dependent protein kinase 3 (CDPK3), which has previously been reported to control the tachyzoite egress. According to earlier studies (PMID: 23226109, 24945436, 5418062, 26544049, 30402958), CDPK3 regulated the parasite exit through multiple phosphorylation events. Here, authors identified differentially-regulated (DR) phosphorylation sites by comparing the parasite samples after treatment with a calcium ionophore (A23178) and a PDE inhibitor (BIPPO), both of which are known to induce artificial egress (induced egress as opposed to natural egress). When the DCDPK3 mutant was treated with A23187, its delayed egress phenotype did not change, whereas BIPPO restored the egress to the level of the parental (termed as WT) strain, probably by activating PKG.

The gene ontology enrichment of the up-regulated clusters revealed many probable CDPK3-dependent DR sites involved in cyclic nucleotide signaling (PDE1, PDE2, PDE7, PDE9, guanylate and adenylate cyclases, cyclic nucleotide-binding protein or CNBP) as well as lipid signaling (PI-PLC, DGK1). Authors suggest lipid signaling as one of the factors altered in the CDPK3 mutant, albeit lipidomics (PC, PI, PS, PT, PA, PE, SM) showed no significant change in phospholipids. To reveal how the four PDEs indicated above contribute to the cAMP and cGMP-mediated egress, they examined their biological significance by knockout/knockdown and enzyme activity assays. Authors claim that PDE1,7,9 proteins are cGMP-specific while PDE2 is cAMP-specific, and BIPPO treatment can inhibit PDE1-cGMP and PDE7-cGMP, but not PDE9-cGMP. Given the complexity, the manuscript is well structured, and most experiments were carefully designed. Undoubtedly, there is a significant amount of work that underlies this manuscript; however, from a conceptual viewpoint, the manuscript does not offer significant advancement over the current knowledge without functional validation of phosphoproteomics data (see below). A large body of work preceding this manuscript has indicated the crosstalk of cAMP, cGMP, calcium and lipid signaling cascades. This work provides a further refinement of the existing model In a methodical sense, the work uses established assays, some of which require revisiting to reach robust conclusions and avoid misinterpretation. The article is quite interesting from a throughput screening point of view, but it clearly lacks the appropriate endorsement of the hits.The authors accept that identifying the phosphorylation of a protein does not imply a functional role, which is a major drawback as there is no experimental support for any phosphorylation site of the protein identified through phosphoproteomics. In terms of the mechanism, it is not clear whether and how lipid turnover and cAMP-PKA signaling control the egress phenotype (lack of a validated model at the end of this study).

Response:

We thank reviewer #3 for their comments, but respectfully disagree with their assessment that the work presented does not advance current knowledge.

1. We demonstrate that, following both BIPPO and A23187 treatment, there is differential phosphorylation of numerous components traditionally believed to sit upstream of PKG activation (as well as numerous components within the PKG signalling pathway itself). While it may have been inferred from previous studies that A23187 and BIPPO signalling intersect, this has never been unequivocally demonstrated - nor has a feedback loop ever been shown.

We provide a novel A23187-driven phosphoproteome timecourse that further bolsters the model of a Ca2+-driven feedback loop.

We show that deletion of CDPK3 leads to a delay in DAG production upon stimulation with A23187.

We show that some of the abovementioned sites are CDPK3 dependent, and that deletion of CDPK3 leads to elevated levels of cAMP (dysregulation of which is known to alter PKG signalling).

We show that pre-treatment with a PKA inhibitor is able to largely rescue this phenotype.

We demonstrate that a cAMP-specific PDE is phosphorylated following A23187 treatment (i.e. Ca2+ flux)

We show that this cAMP specific PDE plays a role in egress.

While the latter PDE may not be directly regulated by CDPK3, these findings suggest that there are likely several Ca2+-dependent kinases that contribute to this feedback loop.

We also firmly disagree with the reviewer’s assertion that without phosphosite characterisation, we have no support for our model. Following treatment with A23187 (and BIPPO), we clearly show broad, systemic changes (both CDPK3 dependent and independent) across signalling pathways previously deemed to sit upstream of calcium flux. Given the vast number of proteins involved in these signalling pathways, and the multitude of differentially regulated phosphosites identified on each of them, it is highly likely that the signalling effects we observe are combinatorial. Accordingly, we believe that mutating individual sites on individual proteins would be a very costly endeavour which is unlikely to substantially advance our understanding of signalling during egress. Moreover, introducing multiple point mutations in a given protein to ablate phosphorylation may lead to protein misfolding and would therefore not be informative. One of the key aims of this study was to assess how egress signalling pathways are interconnected, and we believe we have been able to show strong support for a Ca2+-driven feedback mechanism in which both CDPK3 and PDE2 play a role through the regulation of cAMP.

While we agree with the reviewer’s statement that a large body of work preceding this manuscript has indicated the crosstalk of cAMP, cGMP, calcium and lipid signalling cascades, a feedback loop has not previously been shown. We believe that this finding is absolutely central to facilitate the complete interpretation of existing signalling data. Furthermore, no previous studies have gone to this level of detail in either proteomics or lipidomics to analyse the calcium signal pathway in any apicomplexan parasite. We argue that the novelty in our manuscript is that it is a carefully orchestrated study that advances our understanding of the signalling network over time with subcellular precision. The kinetics of signalling is not well understood and we believe that our study is likely the first to include both proteomic and lipidomic analyses over a timecourse during the acute lytic cycle stage of the disease. In doing so, we found evidence for a feedback loop that controls the signalling network spatiotemporally, and we characterise elements of this feedback in the same study.

**Major Comments:**

Based on the findings reported here there is little doubt that BIPPO and A23187-induced signaling intersect with each other, as very much expected from previous studies. The authors selected the 50s and 15s post-treatment timing of A23187 and BIPPO, respectively for collecting phosphoproteomics samples. At these time points, which were shown to peak cytosolic Ca2+, parasites were still intracellular (Line #171). How did authors make sure to stimulate the entire signaling cascade adequately, particularly when parasites do not egress within the selected time window? There is significant variability between phosphosite intensities of replicates (Line #186), which may also be attributed to insufficient triggers for the egress across independent experiments. This work must be supported by in vitro egress assays with the chosen incubation periods of BIPPO and ionophore treatment (show the induced % egress of tachyzoites in the 50s and 15s).

Response:

1. We appreciate that the reviewer acknowledges that our data clearly shows that BIPPO and A23187-induced signalling intersect. While this may have been expected from previous studies, this has not previously been shown - and is therefore valuable to the field. Specifically, the fact that A23187-treatment leads to phosphorylation of targets normally deemed to sit upstream of calcium release is entirely novel and adds a substantial layer of information to our understanding of how these signalling pathways work together.

Treatments were purposely selected to align pathways to a point where calcium levels peak just prior to calcium reuptake. At these chosen timepoints, we clearly show that overall signalling correlation is very high. We know from our egress assays using identical treatment concentrations (Fig. 2C), that the stimulations used are sufficient to result in complete egress. We are simply comparing signalling pathways at points prior to egress.

As mentioned in point 2, we show convincingly that the treatments used are sufficient to trigger complete egress. As detailed clearly in the text, we believe that these variations in intensities between replicates are due to slight differences in timing between experiments (this is inevitable given the very rapid progression of signalling, and the difficulty of replicating exact sub-minute treatment timings). We demonstrate that the reporter intensities associated with DR sites correlate well across replicates (Supp Fig. 3C), suggesting that despite some replicate variability, the overall trends across replicates is very much consistent. This allows us to confidently average scores to provide values that are representative of a site’s phosphorylation state at the timepoint of interest.

The reviewer’s suggestion that we should demonstrate % egress at the 50s and 15s treatment timepoints is obsolete - we state clearly in the text that parasites have not egressed at these timepoints. Our egress assays (Fig. 2C) further support this.

The authors discuss that CDPK3 controls the cAMP level and PKA through activation of one or more yet-to-be-identified PDEs(s). cAMP could probably also be regulated by an adenylate cyclase, ACbeta that was found to have CDPK3-dependent phosphorylation sites. If CDPK3 is indeed a regulator of cAMP through the activation of PDEs or ACbeta, it would be expected that the deletion of CDPK3 would perturb the cAMP level, resulting in dysregulation of PKAc1 subunit, which in turn would dysregulate cGMP-specific PDEs (PMID: 29030485) and thereby PKG. All these connections need to explain in a more clear manner with experimental support (what is positive and what is negatively regulated by C____DPK3).

Response:

1. We do not firmly state that CDPK3 regulates cAMP by phosphorylation of a PDE - this is one of the possibilities addressed. We acknowledge the possibility that this could also be via the adenylate cyclase (see line 792).

PMID: 29030485 demonstrates clearly a link between cAMP signalling and PKG signalling, but does not demonstrate how this is mediated. The authors postulate that a cGMP-specific PDE is dysregulated given their observation that PDE2 is differentially phosphorylated in a constitutively inactive PKA mutant, however this was not validated experimentally. We and others (Moss et al., 2022), however, demonstrate that PDE2 is cAMP-specific. This suggests that the model built by PMID: 29030485 requires revisiting. We acknowledge clearly in the text that Jia et al. have shown a link between cAMP and PKG signalling, and hypothesise that CDPK3’s modulation of cAMP levels may affect this (this is in keeping with our phosphoproteomic data).

Moreover, the egress defect is not due to a low influx of calcium in the cytosol because when the ionophore A23187 was added to the CDPK3 mutant, its phenotype was not recovered. Rather, the defect may be due to the low or null activity of PKG that would activate PI4K to generate IP3 and DAG. The latter would be used as a substrate by DGK to generate PA that is involved in the secretion of micronemes and Toxoplasma egress. In this context, authors should evaluate the role of CDPK3 in the secretion of micronemes that is directly related to the egress of the parasite.

1. We agree with the reviewer on their point about calcium influx, and have already acknowledged in the text that the feedback loop does not control release of Ca2+ from internal stores as disruption of CDPK3 does not lead to a delay in Ca2+

We agree, and clearly address in the text, that the egress defect could be due to altered PKG/phospholipid pathway signalling.

(Lourido, Tang and David Sibley, 2012; McCoy et al., 2012) have both previously shown that microneme secretion is regulated by CDPK3. We therefore do not deem it necessary to repeat this experiment, but have made clearer mention of their findings in our writing.

When the Dcdpk3 mutant with BIPPO treatment was evaluated, it was observed that the parasite recovered the egress phenotype. It is concluded that CDPK3 could probably regulate the activity of cGMP-specific PDEs. CDPK3 could (in)activate them, or it could act on other proteins indirectly regulating the activity of these PDEs. Upon inactivation of PDEs, an increase in the cGMP level would activate PKG, which will, in turn, promote egress. From the data, it is not clear whether any phosphorylation by CDPK3 would activate or inactivate PDEs, and if so, then how (directly or indirectly). To reach unambiguous interpretation, authors should perform additional assays.

Response:

As mentioned previously, given the abundance of differentially regulated phosphosites, we do not believe that mutating individual sites on individual proteins is a worthwhile or realistic pursuit.

We clearly show systematic A23187-mediated phosphorylation of key signalling components in the PKA/PKG/PI-PLC/phospholipid signalling cascade, and demonstrate that several of these are CDPK3-dependent. We demonstrate that CDPK3 alters cAMP levels (and that the ∆CDPK3 egress delay in A23187 treated parasites is largely rescued following pre-treatment with a PKA inhibitor). We similarly demonstrate that A23187 treatment leads to phosphorylation of numerous PDEs, including the cAMP specific PDE2, and show that PDE2 knockout parasites show an egress delay following A23187 treatment. While PDE2 may not be directly regulated by CDPK3 (suggesting other Ca2+ kinases are also involved), these findings collectively demonstrate the existence of a calcium-regulated feedback loop, in which CDPK3 and PDE2 play a role (by regulating cAMP).

We acknowledge that we have not untangled every element of this feedback loop, and do not believe that it would be realistic to do so in a single study given the number of sites phosphorylated and pathways involved. We do believe, however, that we have shown clearly that the feedback loop exists - this in itself is entirely novel, and of significant importance to the field.

On a similar note, a possible experiment that can be done to improve the work would be to treat the CDPK3 mutant with BIPPO in conjunction with a calcium chelator (BAPTA-AM) to reveal, which proteins are phosphorylated prior to activation of the calcium-mediated cascades?

Response:

We agree that this would be an interesting experiment to carry out but would involve significant work. This could be pursued in another paper or project but is beyond the scope of this work.

The manuscript claims that PDE1, PDE7, PDE9 are cGMP specific, and BIPPO inhibits only cGMP-specific PDEs. All assays are performed with 1-10 micromolar cAMP and cGMP for 1h. There is no data showing the time, protein and substrate dependence. Given the suboptimal enzyme assays, authors should re-do them as suggested here. (1) Repeat the pulldown assay with a higher number of parasites (50-100 million) and measure the protein concentration. (2) Set up the PDE assay with saturating amount of cAMP and cGMP, which is critical if the PDE1,7,9 have a higher Km Value for cAMP (means lower affinity) compared to cGMP. An adequate amount of substrate and protein allows the reaction to reach the Vmax. Once you have re-determined the substrate specificity (revise Fig 5D), you should retest BIPPO (Fig 5E) in the presence of cAMP and cGMP. It is very likely that you would find the same result as PDE9 and PfPDEβ (BIPPO can inhibit both cAMP and cGMP-specific PDE), as described previously

We have repeated our assay using the exact same conditions outlined by Moss et al. This involved using a similar number of parasites, a longer incubation time of 2 hours at a higher temperature (37ºC) and with a lower starting concentration of cAMP (0.1 uM). We demonstrate that we are able to recapitulate both the Moss et al. and Vo et al. (see Supp Fig. 7B). However, we noticed that these reactions were not carried out with saturating cAMP/cGMP concentrations, since all reactions had reached 100% completion at the end of the assay whereby all substrate was hydrolysed. We therefore believe that based on our original assay, as well as the new PDE1 timecourse that we have performed (Supp Fig. 7C), that PDEs 1, 7 and 9 display predominantly cGMP hydrolysing activity, with moderate cAMP hydrolysing activity.

We also repeated the BIPPO inhibition assay using the Moss et al. conditions, and still observe that the cGMP activity of PDE1 is the most potently inhibited of all 4 PDEs. We also see moderate inhibition of the cAMP activities of PDE1 and PDE9, suggesting that cAMP hydrolytic activity can also be inhibited. Interestingly, the cGMP hydrolytic activities of PDEs 7 & 9, which were previously inhibited using our original assay conditions, no longer appear to be inhibited. This is likely due to the longer incubation time, which masks the reduced activities of these two PDEs following treatment with BIPPO.

The authors did not identify any PKG substrate, which is quite surprising as cAMP signaling itself could impact cGMP. Authors should show if they were able to observe enhanced cGMP levels in BIPPO-treated sample (which is expected to stimulate cGMP-specific PDEs). The author mention their inability to measure cGMP level but have they analyzed cGMP in the positive control (BIPPO-treated parasite line)? Why have they focused only on CDPK3 mutant, whereas in their phosphoproteomic data they could see other CDPKs too? It could be that other CDPK-mediated signaling differs and need PKA/PKG for activation.

In the title, the authors have mentioned that there is a positive feedback loop between calcium release, cyclic nucleotide and lipid signaling, which is quite an extrapolation as there is no clear experimental data supporting such a positive feedback loop so the author should change the title of the paper.

Response:

1. As addressed in our previous response to the reviewer, PMID: 29030485 demonstrates clearly a link between cAMP signalling and PKG signalling, but does not confirm how this is mediated. The authors surmise that a cGMP-specific PDE is dysregulated (although the PDE hypothesised to be involved has since been shown to be cAMP-specific), but are similarly unable to detect changes in cGMP levels. This suggests that their model may be incomplete.

The BIPPO treatment experiment suggested by the reviewer was already included in the original manuscript (see Fig. 4D in original manuscript, now Fig. 4E). With BIPPO treatment we are able to detect changes in cGMP levels.

We did not deem it to be within the scope of this study to study every single other CDPK. We chose to study CDPK3, as its egress phenotype was of particular interest given its partial rescue following BIPPO treatment. We reasoned that its study may lead us to identify the signalling pathway that links BIPPO and A23187 induced signalling.

As addressed in greater detail in our response to reviewer #2, the fact that the feedback loop appears to stimulate egress implies that it is positive.

**Minor Comments:**

Materials & Methods

Explanation of parameters is not clear (Line #360-367). Phosphoproteomics with A23187 (8 micromolar) treatment in CDPK3-KO and WT, for 15, 30 and 60s at 37{degree sign}C incubation with DMSO control. Simultaneously passing the DR and CDPK3 dependency thresholds: CDPK3-dependent phosphorylation

__Response: __We have modified the wording to make this clearer as per the reviewer’s suggestion.

Line #368: At which WT-A23187 timepoint did the authors identify 2408 DR-up phosphosites (15s, 30s or 60s)? Or consistently in all? It should be clarified?

__Response: __As already stated in the manuscript (see line 366 in original manuscript, now line 1047), phosphorylation sites were considered differentially regulated if at any given timepoint their log2FC surpassed the DR threshold.

A23187 treatment of the CDPK3-KO mutant significantly increased the cAMP levels at 5 sec post-treatment, but BIPPO did not show any change. The authors concluded that BIPPO presumably does not inhibit cAMP-specific PDEs. However, the dual-specific PDEs are known to be inhibited by BIPPO, as shown recently (____https://www.biorxiv.org/content/10.1101/2021.09.21.461320v1____). Authors do confirm that BIPPO-treatment can inhibit hydrolytic activity of PfPDEbeta for cAMP as well as cGMP (Line #612). Besides, it was shown in Fig 5E that BIPPO can partially though not significantly block cAMP-specific PDE2. The statements and data conflict each other under different subtitles and need to be reconciled. Elevation of basal cAMP level in the CDPK3 mutant indicates the perturbation of cAMP signaling, however BIPPO data requires additional supportive experiments to conclude its relation with cAMP or dual-specific PDE.

Response:

1. The manuscript to which the reviewer refers does not use BIPPO in any of their experiments. They show that continuous treatment with zaprinast blocks parasite growth in a plaque assay, but do not test whether zaprinast specifically blocks the activity of any of the PDEs.

Having repeated the PDE assay using the Moss et al. conditions (as outlined above), we are now able to recapitulate their findings, showing that PDEs 1, 7 and 9 can display dual hydrolytic activity while PDE2 is cAMP specific. As explained further above, we believe that our original set of experiments are more stringent than the Moss *et al. * To confirm this, we also performed an additional experiment, incubating PDE1 for varying amounts of time using our original conditions (1 uM cAMP or 10 uM cGMP, at room temperature). This revealed that PDE1 is much more efficient at hydrolysing cGMP, and only begins to display cAMP hydrolysing capacity after 4 hours of incubation.

We also measured the inhibitory capacity of BIPPO on the PDEs using the Moss *et al. * During the longer incubation time, it seems that BIPPO is unable to inhibit PDEs 7 and 9, while with the more stringent conditions it was able to inhibit both PDEs. We reasoned that since BIPPO is unable to inhibit these PDEs fully, the residual activity over the longer incubation period would compensate for the inhibition, eventually leading to 100% hydrolysis of the cNMPs. We also see that while the cGMP hydrolysing capacity of PDE1 is completely inhibited, its cAMP hydrolysing capacity is only partially inhibited. These findings and the fact that PDE2 is not inhibited by BIPPO are in line with our experiments where we measured [cAMP] and showed that treatment with BIPPO did not lead to alterations in [cAMP].

The method used to determine the substrate specificity of PDE 1,2,7 and 9 resulted in the hydrolytic activity of PDE2 towards cAMP, while the remaining 3 were determined as cGMP-specific. However, PDE1 and PDE9 have been reported as being dual-specific (Moss et al, 2021; Vo et al, 2020), which questions the reliability of the preferred method to characterize substrate specificity by the authors. It is also suggested to use another ELISA-based kit to double check the results.

Response:

As outlined above, we have repeated the assay using the conditions described by Moss et al. (lower starting concentrations of cAMP, 2 hour incubation period at 37ºC) and find that we are able to recapitulate the results of both Moss et al. and Vo et al.. However, using the Moss et al. conditions, the PDEs have hydrolysed 100% of the cyclic nucleotide, suggesting that these conditions are less stringent than the ones we used originally using higher starting concentrations of cAMP and incubating for 1 hour only at room temperature. With enzymatic assays it is always important to perform them at saturating conditions (as already suggested by the reviewer) and therefore we believe that our original conditions are more stringent than the results using the Moss et al. conditions.

Line #607-608: Authors found PDE9 less sensitive to BIPPO-treatment and concluded PDE2 as refractory to BIPPO inhibition; however, the reduction level of activity seems similar as seen in PDE9-BIPPO treated sample? This strong statement should be replaced with a mild explanation.

__Response: __We have tempered our wording as per the reviewer’s suggestion

Figures and legends:

The introductory model in Fig S1 is difficult to understand and ambiguous despite having it discussed in the text. For example, CDPK1 is placed, but only mentioned at the beginning, and the role of other CDPKs is not clear. In addition, the arrows in IP3 and PKG are confusing. The location of guanylate and adenylate cyclase is wrong, and so on... The figure should include only the egress-related signaling components to curate it. The illustration of host cell in orange color must be at the right side of the figure in connection with the apical pole of the parasite (not on the top). Figure legend should also be rearranged accordingly and citations of the underlying components should be included (see below).

__Response: __We have modified Supp Fig. 1 as per the suggestions of reviewer#2 and #3. We have now modified the localisations of the proteins and have also removed the lines showing the cross talk between pathways. We have also highlighted to the reader that this is only a model and may not represent the true localisations of the proteins, despite our best efforts.

In Figure 5D, would you please provide the western blot analysis of samples before and after pulling down to demonstrate the success of your immunoprecipitation assay. Mention the protein concentration in your PDE enzyme assay. Please refer to the M&M comments above to re-do the enzyme assays.

Response:

We have now included western blots for the pull downs of PDEs 1, 2, 7 and 9 (Supp Fig. 7A). We chose not to measure protein concentrations of samples since all experiments were performed using the same starting parasite numbers, and we do not see large differences in activities between biological replicates of the PDEs.

Figure legend 1C: Line #194: There is no red-dotted line shown in graph! Correct it!

__Response: __We have modified this.

Figure 4Gi-ii: Shouldn't it be labelled i: H89-treatment and ii: A23178, respectively instead of DMSO and H89? (based on the text Line #579).

__Response: __Our labelling of Fig. 4Gi-ii is correct as panel i parasites were pre-treated with DMSO, while panel ii parasites were pre-treated with H89. Subsequent egress assays on both parasites were then performed using A23187.

We have modified the figures to include mention of A23187 on the X axis, and modified the figure legend to clarify pre-treatment was performed with DMSO and H89 respectively.

Bibliography:

Line #57 and 58: Citations must be selected properly! Carruthers and Sibley 1999 revealed the impact of Ca2+ on the microneme secretion within the context of host cell attachment and invasion, not egress as indicated in the manuscript! Similar case is also valid for the reference Wiersma et al 2004; since the roles of cyclic nucleotides were suggested for motility and invasion. Also notable in the fact that several citations describing the localization, regulation and physiological importance of cAMP and cGMP signaling mediators (PMID: 30449726 , 31235476 , 30992368 , 32191852 , 25555060 , 29030485 ) are either completely omitted or not appropriately cited in the introduction and discussion sections.

Response:

We have modified the citations as per the reviewer’s suggestions. We now cite Endo et al., 1987 for the first use of A23187 as an egress trigger, and Lourido, Tang and David Sibley, 2012 for the role of cGMP signalling in egress. We also cite all the GC papers when we make first mention of the GC. We have also removed the Howard et al., 2015 citation (PMID: 25555060) when referring to the fact that BIPPO/zaprinast can rescue the egress delay of ∆CDPK3 parasites.

Grammar/Language

Line #31: After "cAMP levels" use comma

Response:

We have modified this.

36: Sentence is not clear. Does conditional deletion of all four PDEs support their important roles? If so, the role in egress of the parasite?

Response:

We have clarified our wording as per the reviewer’s suggestion. We state that PDEs 1 and 2 display an important role in growth since deletion of either these PDEs leads to reduced plaque growth. We have not investigated exactly what stage of the lytic cycle this is.

40: "is a group involving" instead of "are"

Response:

We found no mention of “a group involving” in our original manuscript at line 40 or anywhere else in the manuscript, so we are unsure what the reviewer is referring to.

108: isn't it "discharge of Ca++ from organelle stores to cytosol"?

__Response: __We thank the reviewer for spotting this error. We have now modified this sentence.

120: "was" instead of "were"

__Response: __Since the situation we are referencing is hypothetical, then ‘were’ is the correct tense.

Reviewer #3 (Significance (Required)):

There is a significant amount of work that underlies this manuscript; however, from a conceptual viewpoint, the manuscript does not offer significant advancement over the current knowledge without functional validation of phosphoproteomics data. In terms of the mechanism, it is not clear whether and how lipid turnover and cAMP-PKA signaling control the egress phenotype (lack of a validated model at the end of this study).In a methodical sense, the work uses established assays, some of which require revisiting to reach robust conclusions and avoid misinterpretation.

Compare to existing published knowledge

A large body of work preceding this manuscript has indicated the crosstalk of cAMP, cGMP, calcium and lipid signaling cascades. This work provides a further refinement of the existing model. The article is quite interesting from a throughput screening point of view, but it clearly lacks the appropriate endorsement of the hits.

Response:

Please refer to our first response to reviewer #3 for our full rebuttal to these points. We respectfully disagree with the assessment that the work presented does not advance current knowledge.

Audience

Field specific (Apicomplexan Parasitology)

Expertise

Molecular Parasitology

References

Bailey, A. P. et al. (2015) ‘Antioxidant Role for Lipid Droplets in a Stem Cell Niche of Drosophila’, Cell. The Authors, 163(2), pp. 340–353. doi: 10.1016/j.cell.2015.09.020.

Bullen, H. E. et al. (2016) ‘Phosphatidic Acid-Mediated Signaling Regulates Microneme Secretion in Toxoplasma Article Phosphatidic Acid-Mediated Signaling Regulates Microneme Secretion in Toxoplasma’, Cell Host & Microbe, pp. 349–360. doi: 10.1016/j.chom.2016.02.006.

Dass, S. et al. (2021) ‘Toxoplasma LIPIN is essential in channeling host lipid fluxes through membrane biogenesis and lipid storage’, Nature Communications. Springer US, 12(1). doi: 10.1038/s41467-021-22956-w.

Endo, T. et al. (1987) ‘Effects of Extracellular Potassium on Acid Release and Motility Initiation in Toxoplasma gondii’, The Journal of Protozoology, 34(3), pp. 291–295. doi: 10.1111/j.1550-7408.1987.tb03177.x.

Flueck, C. et al. (2019) Phosphodiesterase beta is the master regulator of camp signalling during malaria parasite invasion, PLoS Biology. doi: 10.1371/journal.pbio.3000154.

Howard, B. L. et al. (2015) ‘Identification of potent phosphodiesterase inhibitors that demonstrate cyclic nucleotide-dependent functions in apicomplexan parasites’, ACS Chemical Biology, 10(4), pp. 1145–1154. doi: 10.1021/cb501004q.

Jia, Y. et al. (2017) ‘ Crosstalk between PKA and PKG controls pH ‐dependent host cell egress of Toxoplasma gondii ’, The EMBO Journal, 36(21), pp. 3250–3267. doi: 10.15252/embj.201796794.

Katris, N. J. et al. (2020) ‘Rapid kinetics of lipid second messengers controlled by a cGMP signalling network coordinates apical complex functions in Toxoplasma tachyzoites’, bioRxiv. doi: 10.1101/2020.06.19.160341.

Lentini, J. M. et al. (2020) ‘DALRD3 encodes a protein mutated in epileptic encephalopathy that targets arginine tRNAs for 3-methylcytosine modification’, Nature Communications. Springer US, 11(1). doi: 10.1038/s41467-020-16321-6.

Lourido, S., Tang, K. and David Sibley, L. (2012) ‘Distinct signalling pathways control Toxoplasma egress and host-cell invasion’, EMBO Journal. Nature Publishing Group, 31(24), pp. 4524–4534. doi: 10.1038/emboj.2012.299.

Lunghi, M. et al. (2022) ‘Pantothenate biosynthesis is critical for chronic infection by the neurotropic parasite Toxoplasma gondii’, Nature Communications. Springer US, 13(1). doi: 10.1038/s41467-022-27996-4.

McCoy, J. M. et al. (2012) ‘TgCDPK3 Regulates Calcium-Dependent Egress of Toxoplasma gondii from Host Cells’, PLoS Pathogens, 8(12). doi: 10.1371/journal.ppat.1003066.

Moss, W. J. et al. (2022) ‘Functional Analysis of the Expanded Phosphodiesterase Gene Family in Toxoplasma gondii Tachyzoites’, mSphere. American Society for Microbiology, 7(1). doi: 10.1128/msphere.00793-21.

Stewart, R. J. et al. (2017) ‘Analysis of Ca2+ mediated signaling regulating Toxoplasma infectivity reveals complex relationships between key molecules’, Cellular Microbiology, 19(4). doi: 10.1111/cmi.12685.

Vo, K. C. et al. (2020) ‘The protozoan parasite Toxoplasma gondii encodes a gamut of phosphodiesterases during its lytic cycle in human cells’, Computational and Structural Biotechnology Journal. The Author(s), 18, pp. 3861–3876. doi: 10.1016/j.csbj.2020.11.024.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Dominicus et al aimed to identify the intersecting components of calcium, cyclic nucleotides (cAMP, cGMP) and lipid signaling through phosphoproteomic, knockout and biochemical assays in an intracellular parasite, Toxoplasma gondii, particularly when its acutely-infectious tachyzoite stage exits the host cells. A series of experimental strategies were applied to identify potential substrates of calcium-dependent protein kinase 3 (CDPK3), which has previously been reported to control the tachyzoite egress. According to earlier studies (PMID: 23226109, 24945436, 5418062, 26544049, 30402958), CDPK3 regulated the parasite exit through multiple phosphorylation events. Here, authors identified differentially-regulated (DR) phosphorylation sites by comparing the parasite samples after treatment with a calcium ionophore (A23178) and a PDE inhibitor (BIPPO), both of which are known to induce artificial egress (induced egress as opposed to natural egress). When the CDPK3 mutant was treated with A23187, its delayed egress phenotype did not change, whereas BIPPO restored the egress to the level of the parental (termed as WT) strain, probably by activating PKG. The gene ontology enrichment of the up-regulated clusters revealed many probable CDPK3-dependent DR sites involved in cyclic nucleotide signaling (PDE1, PDE2, PDE7, PDE9, guanylate and adenylate cyclases, cyclic nucleotide-binding protein or CNBP) as well as lipid signaling (PI-PLC, DGK1). Authors suggest lipid signaling as one of the factors altered in the CDPK3 mutant, albeit lipidomics (PC, PI, PS, PT, PA, PE, SM) showed no significant change in phospholipids. To reveal how the four PDEs indicated above contribute to the cAMP and cGMP-mediated egress, they examined their biological significance by knockout/knockdown and enzyme activity assays. Authors claim that PDE1,7,9 proteins are cGMP-specific while PDE2 is cAMP-specific, and BIPPO treatment can inhibit PDE1-cGMP and PDE7-cGMP, but not PDE9-cGMP. Given the complexity, the manuscript is well structured, and most experiments were carefully designed. Undoubtedly, there is a significant amount of work that underlies this manuscript; however, from a conceptual viewpoint, the manuscript does not offer significant advancement over the current knowledge without functional validation of phosphoproteomics data (see below). A large body of work preceding this manuscript has indicated the crosstalk of cAMP, cGMP, calcium and lipid signaling cascades. This work provides a further refinement of the existing model. In a methodical sense, the work uses established assays, some of which require revisiting to reach robust conclusions and avoid misinterpretation. The article is quite interesting from a throughput screening point of view, but it clearly lacks the appropriate endorsement of the hits. The authors accept that identifying the phosphorylation of a protein does not imply a functional role, which is a major drawback as there is no experimental support for any phosphorylation site of the protein identified through phosphoproteomics. In terms of the mechanism, it is not clear whether and how lipid turnover and cAMP-PKA signaling control the egress phenotype (lack of a validated model at the end of this study).

Major Comments:

Based on the findings reported here there is little doubt that BIPPO and A23187-induced signaling intersect with each other, as very much expected from previous studies. The authors selected the 50s and 15s post-treatment timing of A23187 and BIPPO, respectively for collecting phosphoproteomics samples. At these time points, which were shown to peak cytosolic Ca2+, parasites were still intracellular (Line #171). How did authors make sure to stimulate the entire signaling cascade adequately, particularly when parasites do not egress within the selected time window? There is significant variability between phosphosite intensities of replicates (Line #186), which may also be attributed to insufficient triggers for the egress across independent experiments. This work must be supported by in vitro egress assays with the chosen incubation periods of BIPPO and ionophore treatment (show the induced % egress of tachyzoites in the 50s and 15s).

The authors discuss that CDPK3 controls the cAMP level and PKA through activation of one or more yet-to-be-identified PDEs(s). cAMP could probably also be regulated by an adenylate cyclase, ACbeta that was found to have CDPK3-dependent phosphorylation sites. If CDPK3 is indeed a regulator of cAMP through the activation of PDEs or ACbeta, it would be expected that the deletion of CDPK3 would perturb the cAMP level, resulting in dysregulation of PKAc1 subunit, which in turn would dysregulate cGMP-specific PDEs (PMID: 29030485) and thereby PKG. All these connections need to explain in a more clear manner with experimental support (what is positive and what is negatively regulated by CDPK3). Moreover, the egress defect is not due to a low influx of calcium in the cytosol because when the ionophore A23187 was added to the CDPK3 mutant, its phenotype was not recovered. Rather, the defect may be due to the low or null activity of PKG that would activate PI4K to generate IP3 and DAG. The latter would be used as a substrate by DGK to generate PA that is involved in the secretion of micronemes and Toxoplasma egress. In this context, authors should evaluate the role of CDPK3 in the secretion of micronemes that is directly related to the egress of the parasite.

When the cdpk3 mutant with BIPPO treatment was evaluated, it was observed that the parasite recovered the egress phenotype. It is concluded that CDPK3 could probably regulate the activity of cGMP-specific PDEs. CDPK3 could (in)activate them, or it could act on other proteins indirectly regulating the activity of these PDEs. Upon inactivation of PDEs, an increase in the cGMP level would activate PKG, which will, in turn, promote egress. From the data, it is not clear whether any phosphorylation by CDPK3 would activate or inactivate PDEs, and if so, then how (directly or indirectly). To reach unambiguous interpretation, authors should perform additional assays. On a similar note, a possible experiment that can be done to improve the work would be to treat the CDPK3 mutant with BIPPO in conjunction with a calcium chelator (BAPTA-AM) to reveal, which proteins are phosphorylated prior to activation of the calcium-mediated cascades? The manuscript claims that PDE1, PDE7, PDE9 are cGMP specific, and BIPPO inhibits only cGMP-specific PDEs. All assays are performed with 1-10 micromolar cAMP and cGMP for 1h. There is no data showing the time, protein and substrate dependence. Given the suboptimal enzyme assays, authors should re-do them as suggested here. (1) Repeat the pulldown assay with a higher number of parasites (50-100 million) and measure the protein concentration. (2) Set up the PDE assay with saturating amount of cAMP and cGMP, which is critical if the PDE1,7,9 have a higher Km Value for cAMP (means lower affinity) compared to cGMP. An adequate amount of substrate and protein allows the reaction to reach the Vmax. Once you have re-determined the substrate specificity (revise Fig 5D), you should retest BIPPO (Fig 5E) in the presence of cAMP and cGMP. It is very likely that you would find the same result as PDE9 and PfPDEβ (BIPPO can inhibit both cAMP and cGMP-specific PDE), as described previously.

The authors did not identify any PKG substrate, which is quite surprising as cAMP signaling itself could impact cGMP. Authors should show if they were able to observe enhanced cGMP levels in BIPPO-treated sample (which is expected to stimulate cGMP-specific PDEs). The author mention their inability to measure cGMP level but have they analyzed cGMP in the positive control (BIPPO-treated parasite line)? Why have they focused only on CDPK3 mutant, whereas in their phosphoproteomic data they could see other CDPKs too? It could be that other CDPK-mediated signaling differs and need PKA/PKG for activation. In the title, the authors have mentioned that there is a positive feedback loop between calcium release, cyclic nucleotide and lipid signaling, which is quite an extrapolation as there is no clear experimental data supporting such a positive feedback loop so the author should change the title of the paper.

Minor Comments:

Materials & Methods

Explanation of parameters is not clear (Line #360-367). Phosphoproteomics with A23187 (8 micromolar) treatment in CDPK3-KO and WT, for 15, 30 and 60s at 37{degree sign}C incubation with DMSO control. Simultaneously passing the DR and CDPK3 dependency thresholds: CDPK3-dependent phosphorylation

Line #368: At which WT-A23187 timepoint did the authors identify 2408 DR-up phosphosites (15s, 30s or 60s)? Or consistently in all? It should be clarified?

A23187 treatment of the CDPK3-KO mutant significantly increased the cAMP levels at 5 sec post-treatment, but BIPPO did not show any change. The authors concluded that BIPPO presumably does not inhibit cAMP-specific PDEs. However, the dual-specific PDEs are known to be inhibited by BIPPO, as shown recently (https://www.biorxiv.org/content/10.1101/2021.09.21.461320v1). Authors do confirm that BIPPO-treatment can inhibit hydrolytic activity of PfPDEbeta for cAMP as well as cGMP (Line #612). Besides, it was shown in Fig 5E that BIPPO can partially though not significantly block cAMP-specific PDE2. The statements and data conflict each other under different subtitles and need to be reconciled. Elevation of basal cAMP level in the CDPK3 mutant indicates the perturbation of cAMP signaling, however BIPPO data requires additional supportive experiments to conclude its relation with cAMP or dual-specific PDE.

The method used to determine the substrate specificity of PDE 1,2,7 and 9 resulted in the hydrolytic activity of PDE2 towards cAMP, while the remaining 3 were determined as cGMP-specific. However, PDE1 and PDE9 have been reported as being dual-specific (Moss et al, 2021; Vo et al, 2020), which questions the reliability of the preferred method to characterize substrate specificity by the authors. It is also suggested to use another ELISA-based kit to double check the results.

Line #607-608: Authors found PDE9 less sensitive to BIPPO-treatment and concluded PDE2 as refractory to BIPPO inhibition; however, the reduction level of activity seems similar as seen in PDE9-BIPPO treated sample? This strong statement should be replaced with a mild explanation.

Figures and legends:

The introductory model in Fig S1 is difficult to understand and ambiguous despite having it discussed in the text. For example, CDPK1 is placed, but only mentioned at the beginning, and the role of other CDPKs is not clear. In addition, the arrows in IP3 and PKG are confusing. The location of guanylate and adenylate cyclase is wrong, and so on... The figure should include only the egress-related signaling components to curate it. The illustration of host cell in orange color must be at the right side of the figure in connection with the apical pole of the parasite (not on the top). Figure legend should also be rearranged accordingly and citations of the underlying components should be included (see below). In Figure 5D, would you please provide the western blot analysis of samples before and after pulling down to demonstrate the success of your immunoprecipitation assay. Mention the protein concentration in your PDE enzyme assay. Please refer to the M&M comments above to re-do the enzyme assays.

Figure legend 1C: Line #194: There is no red-dotted line shown in graph! Correct it!

Figure 4Gi-ii: Shouldn't it be labelled i: H89-treatment and ii: A23178, respectively instead of DMSO and H89? (based on the text Line #579)

Bibliography: Line #57 and 58: Citations must be selected properly! Carruthers and Sibley 1999 revealed the impact of Ca2+ on the microneme secretion within the context of host cell attachment and invasion, not egress as indicated in the manuscript! Similar case is also valid for the reference Wiersma et al 2004; since the roles of cyclic nucleotides were suggested for motility and invasion. Also notable in the fact that several citations describing the localization, regulation and physiological importance of cAMP and cGMP signaling mediators (PMID: 30449726, 31235476, 30992368, 32191852, 25555060, 29030485) are either completely omitted or not appropriately cited in the introduction and discussion sections.

Grammar/Language Line #31: After "cAMP levels" use comma 36: Sentence is not clear. Does conditional deletion of all four PDEs support their important roles? If so, the role in egress of the parasite? 40: "is a group involving" instead of "are" 108: isn't it "discharge of Ca++ from organelle stores to cytosol"? 120: "was" instead of "were"

Significance

There is a significant amount of work that underlies this manuscript; however, from a conceptual viewpoint, the manuscript does not offer significant advancement over the current knowledge without functional validation of phosphoproteomics data. In terms of the mechanism, it is not clear whether and how lipid turnover and cAMP-PKA signaling control the egress phenotype (lack of a validated model at the end of this study).In a methodical sense, the work uses established assays, some of which require revisiting to reach robust conclusions and avoid misinterpretation.

Compare to existing published knowledge

A large body of work preceding this manuscript has indicated the crosstalk of cAMP, cGMP, calcium and lipid signaling cascades. This work provides a further refinement of the existing model. The article is quite interesting from a throughput screening point of view, but it clearly lacks the appropriate endorsement of the hits.

Audience

Field specific (Apicomplexan Parasitology)

Expertise

Molecular Parasitology

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:

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

In this manuscript, Dominicus et al investigate the elusive role of calcium-dependent kinase 3 during the egress of Toxoplasma gondii. Multiple functions have already been proposed for this kinase by this group including the regulation of basal calcium levels (24945436) or of a tyrosine transporter (30402958). However, one of the most puzzling phenotypes of CDPK3 deficient tachyzoites is a marked delay in egress when parasites are stimulated with a calcium ionophore that is rescued with phosphodiesterase (PDE) inhibitors. Crosstalk between, cAMP, cGMP, lipid and calcium signalling has been previously described to be important in regulating egress (26933036, 23149386, 29030485) but the role of CDPK3 in Toxoplasma is still poorly understood.

Here the authors first take an elegant phosphoproteomic approach to identify pathways differentially regulated upon treatment with either a PDE inhibitor (BIPPO) and a calcium ionophore (A23187) in WT and CDPK3-KO parasites. Not much difference is observed between BIPPO or A23187 stimulation which is interpreted by the authors as a regulation through a feed-back loop. The authors then investigate the effect of CDPK3 deletion on lipid, cGMP and cAMP levels. The identify major changes in DAG, phospholipid, FFAs, and TAG levels as well as differences in cAMP levels but not for cGMP. Chemical inhibition of PKA leads to a similar egress timing in CDPK3-KO and WT parasites upon A23187 stimulation.

As four PDEs appeared differentially regulated in the CDPK3-KO line upon A23187, the authors investigate the requirement of the 4 PDEs in cAMP levels. They show diverse localisation of the PDEs with specificities of PDE1, 7 and 9 for cGMP and of PDE2 for cAMP. They further show that PDE1, 7 and 9 are sensitive to BIPPO. Finally, using a conditional deletion system, they show that PDE1 and 2 are important for the lytic cycle of Toxoplasma and that PDE2 shows a slightly delayed egress following A23187 stimulation.

Major comments:

-Are the key conclusions convincing?

The title is supported by the findings presented in this study. However I am not sure to understand why the authors imply a positive feed back loop. This should be clarified in the discussion of the results. The phosphoproteome analysis seems very strong and will be of interest for many groups working on egress. However, the key conclusion, i.e. that a substrate overlaps between PKG and CDPK3 is unlikely to explain the CDPK3 phenotype, seems premature to me in the absence of robustly identified substrates for both kinases.

I am not sure there is a clear key conclusion from the lipidomic analysis and how it is used by the authors to build their model up. Major changes are observed but how could this be linked with CDPK3, particularly if cGMP levels are not affected?

The evidence that CDPK3 is involved in cAMP homeostasis seems strong. However, the analysis of PKA inhibition is a bit less clear. The way the data is presented makes it difficult to see whether the treatment is accelerating egress of CDPK3-KO parasites or affecting both WT and CDPK3-KO lines, including both the speed and extent of egress. This is important for the interpretation of the experiment.

The biochemical characterisation of the four PDE is interesting and seems well performed. However, PDE1 was previously shown to hydrolyse both cAMP and cGMP (https://doi.org/10.1101/2021.09.21.461320) which raises some questions about the experimental set up. Could the authors possibly discuss why they do not observe similar selectivity? Could other PDEs in the immunoprecipitate mask PDE activity? In line with this question, it is not clear what % of "hydrolytic activity (%)" means and how it was calculated. The experiments describing the selectivity of BIPPO for PDE1, 7 and 9 as well as the biological requirement of the four tested PDEs are convincing.

-Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The claim that CDPK3 affects cAMP levels seems strong however the exact links between CDPK3 activity, lipid, cGMP and cAMP signalling remain unclear and it may be important to clearly state this.

-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 think that the manuscript contains a significant amount of experiments that are of interest to scientists working on Toxoplasma egress. Requesting experiments to identify the functional link between above-mentioned pathways would be out of the scope for this work although it would considerably increase the impact of this manuscript. For example, would it be possible to test whether the CDPK3-KO line is more or less sensitive to PKG specific inhibition upon A23187 induced?

-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 above-mentioned experiment is not trivial as no specific inhibitors of PKG are available. Ensuring for specificity of the investigated phenotype would require the generation of a resistant line which would require significant work.

-Are the data and the methods presented in such a way that they can be reproduced?

It is not clear how the % of hydrolytic activity of the PDE has been calculated.

-Are the experiments adequately replicated and statistical analysis adequate?

This seems to be performed to high standards.

Minor comments:

-Specific experimental issues that are easily addressable.

I do not have any comments related to minor experimental issues.

-Are prior studies referenced appropriately?

Most of the studies relevant for this work are cited. It is however not clear to me why some important players of the "PKG pathway" are not indicated in Fig 1H and Fig 3E, including for example UGO or SPARK.

-Are the text and figures clear and accurate?

While all the data shown here is impressive and well analysed, I find it difficult to read the manuscript and establish links between sections of the papers. The phosphoproteome analysis is interesting and is used to orientate the reader towards a feedback mechanism rather than a substrate overlap. But why do the authors later focus on PDEs and not on AC or CNBD, as in the end, if I understand well, there is no evidence showing a link between CDPK3-dependent phosphorylation and PDE activity upon A23187 stimulation? It is also unclear how the authors link CDPK3-dependent elevated cAMP levels with the elevated basal calcium levels they previously described. This is particularly difficult to reconcile particularly in a PKG independent manner.

The presentation of the lipidomic analysis is also not really clear to me. Why do the authors show the global changes in phospholipids and not a more detailed analysis? As the authors focus on the PI-PLC pathway, could they detail the dynamics of phosphoinositides? I understand that lipid levels are affected in the mutant but I am not sure to understand how the authors interpret these massive changes in relationship with the function of CDPK3 and the observed phenotypes.

Finally, the characterisation of the PDEs is an impressive piece of work but the functional link with CDPK3 is relatively unclear. It would also be important to clearly discuss the differences with previous results presented in this this preprint: https://doi.org/10.1101/2021.09.21.461320. My understanding is while the authors aim at investigating the role of CDPK3 in A23187 induced egress, the main finding related to CDPK3 is a defect in cAMP homeostasis that is not linked to A23187. Similarly, the requirements of PDE2 in cAMP homeostasis and egress is indirectly linked to CDPK3. Altogether I think that important results are presented here but divided into three main and distinct sections: the phosphoproteomic survey, the lipidomic and cAMP level investigation, and the characterisation of the four PDEs. However, the link between each section is relatively weak and the way the results are presented is somehow misleading or confusing.

-Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This is a very long manuscript written for specialists of this signalling pathway and I would suggest the authors to emphasise more the important results and also clearly state where links are still missing. This is obviously a complex pathway and one cannot elucidate it easily in a single manuscript.

Significance

-Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This is a technically remarkable paper using a broad range of analyses performed to a high standard.

-Place the work in the context of the existing literature (provide references, where appropriate).

The cross-talk between cAMP, cGMP and calcium signalling is well described in Toxoplasma and related parasites. Here the authors show that, in Toxoplasma, CDPK3 is part of this complex signalling network. One of the most important finding within this context is the role of CDPK3 in cAMP homeostasis. With this in mind, I would change the last sentence of the abstract to "In summary we uncover a feedback loop that enhances signalling during egress and links CDPK3 with several signalling pathways together."

The genetic and biochemical analyses of the four PDEs are remarkable and highlight consistencies and inconsistencies with recently published work that would be important to discuss and will be of interest for the field.

While I understand the studied signalling pathway is complex, I think it would be important to better describe the current model of the authors. In the discussion, the authors indicate that "the published data is not currently supported by a model that fits most experimental results." I would suggest to clarify this statement and discuss whether their work helps to reunite, correct or improve previous models.

Could the authors also speculate about a potential role of PDE/CDPK3 in host cell invasion as cAMP signalling has be shown to be important for this process (30208022 and 29030485)?

-State what audience might be interested in and influenced by the reported findings.

This paper is of great interest to groups working on the regulation of egress in Toxoplasma gondii and other related apicomplexan pathogens.

-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.

I am working on the cell biology of apicomplexan parasites.

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Referee #1

Evidence, reproducibility and clarity

In recent years, the field has investigated crosstalk between cGMP and cAMP signaling (PMID: 29030485), lipid and cGMP signaling (PMID: 30742070), and calcium and cGMP signaling (PMID: 26933036, 26933037). In contrast to the Plasmodium field, which has benefited from proteomic experiments (ex: PMID 24594931, 26149123, 31075098, 30794532), second messenger crosstalk in T. gondii has been probed predominantly through genetic and pharmacological perturbations. The present manuscript compares the features of A23187- and BIPPO-stimulated phosphoproteomes at a snapshot in time. This is similar to a dataset generated by two of the authors in 2014 (PMID: 24945436), except that it now includes one BIPPO timepoint. The sub-minute phosphoproteomic timecourse following A23187 treatment in WT and ∆cdpk3 parasites is novel and would seem like a useful resource.

CDPK3-dependent sites were detected on adenylate cyclase, PI-PLC, guanylate cyclase, PDE1, and DGK1. This motivated study of lipid and cNMP levels following A23187 treatment. The four PDEs determined to have A23187-dependent phosphosites were characterized, including the two PDEs with CDPK3-dependent phosphorylation, which were found to be cGMP-specific. However, cGMP levels do not seem to differ in a CDPK3- or A23187-dependent manner. Instead, cAMP levels are elevated in ∆cdpk3 parasites. This would seem to implicate a feedback loop between CDPK3, the adenylyl cyclase, and PKA/PKG: CDPK3 activity reduces adenylyl cyclase activity, which reduces PKA activity, which increases PKG activity. The authors don't pursue this direction, and instead characterize PDE2, which does not have CDPK3-dependent phosphosites, and seems out of place in the study.

MAJOR COMMENTS

1.Some of the key conclusions are not convincing.

The data presented in Figure 6E, F, and G and discussed in lines 647-679 are incongruent. In Figure 6E, the plaques in the PDE2+RAP image are hardly visible; how can it be that the plaques were accurately counted and determined not to differ from vehicle-treated parasites? Are the images in 6E truly representative? Was the order of PDE1 and PDE2 switched? The cited publication by Moss et al. 2021 (preprint) is not in agreement with this study, as stated. That preprint determined that parasites depleted of PDE2 had significantly reduced plaque number and plaque size (>95% reduction); and parasites depleted of PDE1 had a substantially reduced plaque size but a less substantial reduction in plaque number.

Unfortunately, the length of time required for PDE depletion (72h) is incompatible with most T. gondii cellular assays (typically performed within one lytic cycle, 40-48h). Although the authors performed the assays 3 days after initial RAP treatment, is there evidence that non-excised parasites don't grow out of the population? This should be straightforward to test: treat, wait 3 days, infect onto monolayers, wait 24-48h fix, and stain with anti-YFP and an anti-Toxoplasma counterstain. The proportion of the parasite population that had excised the PDE at the time of the cellular assays will then be known, and the reader will have a sense of how complete the observed phenotypes are. As a reader, I will regard the phenotypes with some level of skepticism due to the long depletion time, especially since a panel of PDE rapid knockdown strains (depletion in < 18h) has recently been generated (Moss et al. 2021 preprint) using strains that have been used by several groups in the field since 2017 (PMID: 28465425). Although the experiments aren't wrong per se; the genetic system used here has substantial limitations, which are not appropriately controlled in the experiments or discussed in the text.

2.The authors should qualify some of their claims as preliminary or speculative, or remove them altogether.

The claims in lines 240-260 are confusing. It seems likely that the two drug treatments have at least topological distinctions in the signaling modules, given that cGMP-triggered calcium release is thought to occur at internal stores, whereas A23187-mediated calcium influx likely occurs first at the parasite plasma membrane. The authors' proposed alternative, that treatment-specific phosphosite behavior arises from experimental limitations and "mis-alignment", is unsatisfying for the following reasons: (1) From the outset, the authors chose different time frames to compare the two treatments (15s for BIPPO vs. 50s for A23187); (2) the experiment comprises a single time point, so it does not seem appropriate to compare the kinetics of phosphoregulation. There is still value in pointing out which phosphosites appear treatment-specific under the chosen thresholds, but further claims on the basis of this single-timepoint experiment are too speculative. Lines 264-267 and 281-284 should also be tempered.

Relatedly, graphing of the data in Figure 1G (accompanying the main text mentioned above) was confusing. Why is one axis a ratio, and the other log10 intensity? What does log10 intensity tell you without reference to the DMSO intensity? Wouldn't you want the L2FC(A23187) vs. L2FC(BIPPO) comparisons? Could you use different point colors to highlight these cases on plot 1E? Additionally, could you use a pseudocount to include peptides only identified in one treatment condition on the plot in 1E? (Especially since these sites are mentioned in lines 272-278 but are not on the plot)

3.Additional experiments would be essential to support the main claims of the paper.

Genetic validation is necessary for the experiments performed with the PKA inhibitor H89. H89 is nonspecific even in mammalian systems (PMID: 18523239) and in this manuscript it was used at a high concentration (50 µM). The heterodimeric architecture of PKA in apicomplexans dramatically differs from the heterotetrameric enzymes characterized in metazoans (PMID: 29263246), so we don't know what the IC50 of the inhibitor is, or whether it inhibits competitively. Two inducible knockdown strains exist for PKA C1 (PMID: 29030485, 30208022). The authors could request one of these strains and construct a ∆cdpk3 in that genetic background, as was done for the PDE2 cKO strain. Estimated time: 3-4 weeks to generate strain, 2 weeks to repeat assays.

cGMP levels are found to not increase with A23187 treatment, which is at odds with a previous study (lines 524-560). The text proposes that the differences could arise from the choice of buffer: this study used an intracellular-like Endo buffer (no added calcium, high potassium), whereas Stewart et al. 2017 used an extracellular-like buffer (DMEM, which also contains mM calcium and low potassium). An alternative explanation is that 60 s of A23187 treatment does not achieve a comparable amount of calcium flux as 15 s of BIPPO treatment, and a calcium-dependent effect on cGMP levels, were it to exist, could not be observed at the final timepoint in the assay. The experiments used to determine the kinetics of calcium flux following BIPPO and A23187 treatments (Fig. 1B, C) were calibrated using Ringer's buffer, which is more similar to an extracellular buffer (mM calcium, low potassium). In this buffer, A23187 treatment would likely stimulate calcium entry from across the parasite plasma membrane, as well as across the membranes of parasite intracellular calcium stores. By contrast, A23187 treatment in Endo buffer (low calcium) would likely only stimulate calcium release from intracellular stores, not calcium entry, since the calcium concentration outside of the parasite is low. Because calcium entry no longer contributes to calcium flux arising from A23187 treatment, it is possible that the calcium fluxes of A23187-treated parasites at 60 s are "behind" BIPPO-treated parasites at 15 s. The researchers could control these experiments by either (i) performing the cNMP measurements on parasites resuspended in the same buffer used in Figure 1B, C (Ringer's) or (ii) measuring calcium flux of extracellular parasites in Endo buffer with BIPPO and A23187 to determine the "alignment" of calcium levels, as was done with intracellular parasites in Figure 1C. No new strains would have to be generated and the assays have already been established in the manuscript. Estimated time to perform control experiments with replicates: 2 weeks. This seems like an important control, because the interpretation of this experiment shifts the focus of the paper from feedback between calcium and cGMP signaling, which had motivated the initial phosphoproteomics comparisons, to calcium and cAMP signaling. Further, the lipidomics experiments were performed in an extracellular-like buffer, DMEM, so it's unclear why dramatically different buffers were used for the lipidomics and cNMP measurements.

Additional information is required to support the claim that PDE2 has a moderate egress defect (lines 681-687). T. gondii egress is MOI-dependent (PMID: 29030485). Although the parasite strains were used at the same MOI, there is no guarantee that the parasites successfully invaded and replicated. If parasites lacking PDE2 are defective in invasion or replication, the MOI is effectively decreased, which could explain the egress delay. Could the authors compare the MOIs (number of vacuoles per host cell nuclei) of the vehicle and RAP-treated parasites at t = 0 treatment duration to give the reader a sense of whether the MOIs are comparable?

4.A few references are missing to ensure reproducibility.

The manuscript states that the kinetic lipidomics experiments were performed with established methods, but the cited publication (line 497) is a preprint. These are therefore not peer reviewed and should be described in greater detail in this manuscript, including any relevant validation.

Please cite the release of the T. gondii proteomes used for spectrum matching (lines 972-973).

Please include the TMT labeling scheme so the analysis may be reproduced from the raw files.

5.Statistical analyses should be reviewed as follows:

Have the authors examined the possibility that some changes in phosphopeptide abundance reflect changes in protein abundance? This may be particularly relevant for comparisons involving the ∆cdpk3 strain. Did the authors collect paired unenriched proteomes from the experiments performed? Alternatively, there may be enriched peptides that did not change in abundance for many of the proteins that appear dynamically phosphorylated.

It seems like for Figs. 3B and S5 the maximum number of clusters modeled was selected. Could the authors provide a rationale for the number of clusters selected, since it appears many of the clusters have similar profiles.

Please include figure panel(s) relating to gene ontology. Relevant information for readers to make conclusions includes p-value, fold-enrichment or gene ratio, and some sort of metric of the frequency of the GO term in the surveyed data set. See PMID: 33053376 Fig. 7 and PMID: 29724925 Fig. 6 for examples or enrichment summaries. Additionally, in the methods, specify (i) the background set, (ii) the method used for multiple test correction, (iii) the criteria constituting "enrichment", (iv) how the T. gondii genome was integrated into the analysis, (v) the class of GO terms (molecular function, biological process, or cellular component), (vi) any additional information required to reproduce the results (for example, settings modified from default).

The presentation of the lipidomics experiments in Figure 4A-C is confusing. First, the ∆cdpk3/WT ratio removes information about the process in WT parasites, and it's unclear why the scale centers on 100 and not 1. Second, the data in Figure S6 suggests a more modest effect than that represented in Fig. 4; is this due to day to day variability? How do the authors justify pairing WT and mutant samples as they did to generate the ratios? The significance test seems to be performed on the difference between the WT and ∆cdpk3 strains, but not relative to the DMSO treatment? Wouldn't you want to perform a repeated measures ANOVA to determine (i) if lipid levels change over time and (ii) if this trend differs in WT vs. mutant strain? In the main text, it would be preferable to see the data presented as the proteomics experiments were in Figure 4B and 4C, with fold changes relative to the DMSO (t = 0) treatment, separately for WT and ∆cdpk3 parasites. Signaling lipids constitute small percentages of the overall pool (e.g. PMID: 26962945), so one might not necessarily expect to observe large changes in lipid abundance when signaling pathways are modulated. Is there any positive control that the authors could include to give readers a sense of the dynamic range? Maybe the DGK1 mutant (PMID: 26962945)?

Figure 4E: are the differences in [cAMP] with DMSO treatment and A23187 treatment different at any of the timepoints in the WT strain? The comparison seems to be WT/∆cdpk3 at each timepoint. Does the text (lines 562-568) need to be modified accordingly?

Figure 6I: is the difference between PDE2 cKO/∆cdpk3 + DMSO or RAP significant?

MINOR COMMENTS

1.The following references should be added or amended:

Lines 83-85: in the cited publication, relative phosphopeptide abundances of an overexpressed dominant-negative, constitutively inactive PKA mutant were compared to an overexpressed wild-type mutant. In this experimental setup, one would hypothesize that targets of PKA should be down-regulated (inactive/WT ratios). However, the mentioned phosphopeptide of PDE2 was found to be up-regulated, suggesting that it is not a direct target of PKA.

Cite TGGT1_305050, referenced as calmodulin in line 458, as TgELC2 (PMID: 26374117).

Cite TGGT1_295850 as apical annuli protein 2 (AAP2, PMID: 31470470).

Cite TGGT1_270865 (adenylyl cyclase beta, Acβ) as PMID: 29030485, 30449726.

Cite TGGT1_254370 (guanylyl cyclase, GC) as PMID: 30449726, 30742070.

Note that Lourido, Tang and David Sibley, 2012 observed that treatment with zaprinast (a PDE inhibitor) could overcome CDPK3 inhibition. The target(s) of zaprinast have not been determined and may differ from those of BIPPO (in identity and IC50). The cited study also used modified CDPK3 and CDPK1 alleles, rather than ∆cdpk3 and intact cdpk1 as used in this manuscript. That is to say, the signaling backgrounds of the parasite strains deviate in ways that are not controlled.

2.The following comments refer to the figures and legends:

Part of the legend text for 1G is included under 1H.

Figure 1H: The legend mentions that some dots are blue, but they appear green. Please ensure that color choices conform to journal accessibility guidelines. See the following article about visualization for colorblind readers: https://www.ascb.org/science-news/how-to-make-scientific-figures-accessible-to-readers-with-color-blindness/ . Avoid using red and green false-colored images; replace red with a magenta lookup table. Multi-colored images are only helpful for the merged image; otherwise, we discern grayscale better. Applies to Figures 1B, 5C, 6D. (Aside: anti-CAP seems an odd choice of counterstain; the variation in the staining, esp. at the apical cap, is distracting.)

Figure 1B: When showing a single fluorophore, please use grayscale and include an intensity scale bar, since relative values are being compared.

Figure 1C: it is difficult to compare the kinetics of the calcium response when the curves are plotted separately. Since the scales are the same, could the two treatments be plotted on the same axes, with different colors? Additionally, according to the legend, a red line seems to be missing in this panel.

Figure 2A: Either Figure S4 can be moved to accompany Figure 2A, or Figure 2A could be moved to the supplemental.

Significance

This manuscript would interest researchers studying signaling pathways in protozoan parasites, especially apicomplexans, as CDPK3 and PKG orthologs exist across the phylum. To my knowledge, it is the first study that has proposed a mechanism by which a calcium effector regulates cAMP levels in T. gondii. Unfortunately, the experiments fall short of testing this mechanism.

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Reply to the reviewers

Manuscript number: RC-2022-01384

Corresponding author(s): Mary O’Riordan and Basel Abuaita

1. General Statements [optional]

We appreciated the positive feedback and helpful suggestions from the reviewers that pointed to a need for more clarity regarding the central focus of the study. Our goal was to take an unbiased approach to evaluating the role of neutrophils during S. Typhimurium (STM) infection of human intestinal epithelial cells (IEC), using human intestinal organoids as a model. An abundance of data point to important inflammatory roles for neutrophils during STM infection of human intestine but the critical mechanisms involved have not been fully elucidated. New data now included in the revised manuscript provide strong support for human PMN-derived IL1-beta as a driver of epithelial cell shedding in STM-infected HIOs, consistent with known differences in local inflammation between human and mouse infection, and this is the focus of the current study. Our data did not support a significant role for human neutrophils in controlling luminal bacterial numbers, but instead the primary human PMNs robustly stimulated epithelial cell responses that led to decreased intraepithelial bacteria. Several recent studies have suggested that caspase-1 is not a critical inflammasome component during STM infection of IEC, which instead use non-canonical inflammasomes, including caspases-4 and -11. Our data point to a human neutrophil-intrinsic function for caspase-1 and IL1-beta that contributes to the inflammatory tone of the intestinal milieu early in STM infection.

2. Point-by-point description of the revisions

Reviewer #1

Major comments:

Some important links are missing to fully support the mechanistic model proposed:* *

1- PMN activity

The authors may strengthen their evidence of PMN activities presented in lines 135 to 143 and in Fig.S2 and S3. In particular, the authors claim that PMNs form NETs in PMN-HIOs but the evidence displayed are limited. In fact, Fig S2 shows the same condition and same staining as Fig 1B but the MPO-positive structures are different. Clarification in the text or the figure would be welcome. Besides, as the authors insist on the relevance of NETs in the discussion, it seems that a clear demonstration and characterization of these structures in the PMN-HIO model would highly benefit the manuscript.

While we commented on NETs in our original manuscript, our conclusions do not rely on the presence or absence of NETs. We have therefore removed the NET data and the reference to NETs. While NETs are potentially interesting in the context of intestinal infection, we understand the reviewer's concern about NETs and anticipate that a more quantitative characterization of NETs may be challenging given the structure and variability of the PMN-HIOs.

Regarding the analyses of the culture supernatants (Fig.S3), only 3 out of the 5 displayed datasets are commented on in the text. The data obtained for BD2 and N-Gal should be either commented or removed from the figure. The author further suggests that Elafin expression in presence of PMN may restrict PMNs' ability to kill Salmonella. Repeating the experiment displayed in Fig S1 in the presence of Elafin as well as in the presence of the supernatant extracted from HIOs and PMN-HIOs would clarify the potential inhibition of PMN killing capacity in the PMN-HIO model.

We now include a sentence on the antimicrobials BD2 and N-GAL to the text (line 135-136). Elafin is one of many molecules that could potentially affect the ability of PMNs to kill Salmonella. We repeated the experiments in S3 Fig with recombinant Elafin. There was a very weak effect on killing in the presence of Elafin, however Elafin can also kill Salmonella directly, complicating interpretation of these experiments. We have now added a sentence in the Discussion to speculate that Elafin is one example of how the epithelium may inhibit the ability of PMNs to kill (line 366-372). These data are not central to our main conclusions and are only intended to provide context to the reader about possible explanations for why PMNs can kill Salmonella directly, but do not significantly alter total bacterial numbers in the HIO model.

The author proposed that infected and uninfected cells are extracted from the epithelium due to PMN activation, suggesting that Salmonella infection of epithelial cells is only indirectly involved in cell shedding. This is an interesting hypothesis that could be tested by measuring cell shedding in a non-infected but PMN-activated (for instance with PMA) PMN-HIO model. This would clarify further the role of PMN in controlling epithelial response to the infection.

We tested this possibility by microinjecting LPS into the lumen of PMN-HIOs (S6 Fig). There was significantly less TUNEL+ signal in LPS-injected PMN-HIOs compared to STM-infected PMN-HIOs, suggesting that active Salmonella infection is required for shedding of both infected and uninfected cells in the presence of PMNs__. __

2- Specificity of RNA-seq profiling:

The authors analyzed the transcriptomic profiling of PMN-HIOs and HIOs infected or not. While these experiments bring to light an interesting difference in inflammasome/cell death transcriptomic programs at the scale of the co-culture model, it is not possible to conclude from which cell type these transcriptomic shifts emerge. To clarify this, the authors stain the co-culture for ASC and observe that ASC-positive cells are PMNs. They conclude that PMNs are most likely the primary site of caspase-1 dependent production of IL1. While their model is theoretically consistent, more direct proofs are necessary to conclude on the cell-type specific transcriptomic program during infection of PMN-HIO and could be obtained by FACS sorting of the cells prior to RNA-seq, for instance using MPO to detect PMNs and E-cadherin to detect epithelial cells.

We now provide evidence that pretreating PMNs with an irreversible Caspase-1 inhibitor before co-culturing with STM-infected HIOs prevented accumulation of luminal TUNEL+ cells (Fig 6B,C). Additionally, IL-1β treatment in the absence of PMNs recapitulated the cell death phenotype of the infected PMN-HIOs (Fig 6D,E) suggesting Caspase-1 activity in PMNs and IL-1β production are necessary for epithelial cell death in the PMN-HIOs.

3- Roles of cytokine

After showing an increased expression/release of IL1 and IL1RA in infected PMN-HIOs, the authors move on to testing the role of caspases on cell shedding. Yet, they do not test the impact of IL1 and IL1RA on cell shedding. As, according to their proposed model, IL1 is acting upstream of caspase-1 to promote cell shedding, testing cell shedding in infected PMN-HIOs in the presence of an IL1 inhibitor would clarify that link. The author also proposed that the decrease of IL33 in PMN-HIOs compared to HIOs could be due to PMN processing, which would give an additional role to PMNs in controlling the epithelial response to infection. In the context of this manuscript, it would be highly relevant to test this hypothesis by measuring the rate of cleaved IL-33.

We now provide data to address these questions about IL-1 signaling. HIOs were microinjected with recombinant IL-1β during STM infection and PMN-HIOs were also treated with IL1RA during STM infection. Cell shedding was measured under these conditions in Fig. 6D-F. Cell shedding was dependent on IL-1 signaling and the model has been updated to reflect this.

We also concentrated supernatants from STM-infected HIOs and PMN-HIOs, probed for cleaved IL33 via western blot and did see some cleavage. However, without being able to block this process it is not possible to conclude what role cleaved IL33 has during infection in the PMN-HIO and IL-1β seems to be sufficient to drive the cell shedding phenotype. Since the status of IL33 is not central to our conclusions, we have removed these data from the manuscript.

4- Roles of caspase

The interpretations of the role of Caspases to restrict bacteria burden are unclear and should be revised (see also minor comment). It appears that both Caspase-1 and Caspase-3 are necessary for efficient cell shedding (Fig4B), Caspase-1 (but not Caspase-3) decreases intraluminal bacteria burden (Fig4C) and Caspase-3 (but not Caspase-1) decreases epithelium-associated bacteria (Fig4D). To reconcile these observations with the hypothesis that cell shedding is responsible for the decrease of intraluminal and epithelium-associated bacterial burden, one may propose that caspase-3 (but not caspase-1) induces cell shedding of mainly non-infected cells (possibly bacteria-associated) and caspase-1 (but not caspase-3) induced cell shedding of infected cells. This could be tested by measuring the % of infected extruded cells upon caspase inhibitor treatments. In addition, these data don't allow to propose that Caspase-3 activation happens downstream of Caspase-1 as suggested by the authors in their abstract figure.

It is difficult to accurately quantify the percent infected cells that are extruded since both infected and uninfected cells are extruded into a luminal space full of bacteria, which may associate with uninfected cells post-extrusion. However, we did observe cells positive for cleaved Caspase-3 when HIOs were treated with IL-1β leading us to infer that Caspase-1 mediated cytokine signaling through IL1R can trigger downstream Caspase-3 activation (Fig. 6G). We have expanded the Discussion to talk about differing roles of Caspases on bacterial burden and association with the epithelium (lines 374-397).

Minor comments:

The majority of the points listed below can be addressed with further analyses of pre-acquired data sets:

Fig1E/1F/4D: each green dot is not likely to be individual bacteria but rather a cluster of bacterium (based on their size). So the y-axis in Fig 1E and Fig4D should not be #STM.

Y-axis labels have been changed to #STM objects

Fig2A: Variations in organoid size and epithelial thickness can be observed between figures. In particular, in Fig 2A, the HIO seems much younger than the other ones displayed in the manuscript.

There is considerable natural variability between HIOs and between batches, a phenomenon observed by many HIO researchers (Hofer et al. Nature Reviews Materials 2021). HIOs were all treated the same way prior to infection, and based on our extensive observations, epithelial thickness does not correlate significantly with a particular experimental condition, as we now show in S10 Fig.

Line 176 to 178, the authors mentioned the TUNEL+ cells in the mesenchyme but rule out the possibility that this phenotype could be infection or PMN-dependent because it is observed in the different conditions. As the picture displayed in Fig2A suggests high differences in the number of TUNEL+ cells in the mesenchyme under the 4 tested conditions, the authors should still quantify this phenomenon (possibly in the supplementary).

This is likely an artifact of culturing and not due to the infection or PMNs. There is variability between HIO batches in the amount of TUNEL signal in mesenchymal cells (for example HIOs in Fig 4A and 5A have very low or no TUNEL positivity in the mesenchyme).

"DAPI" should be written in blue.

This has been corrected.

Fig2C: Could the authors comment on the % of E-cadherin cells that are also TUNEL+? Is it 100%?

On average about 75% of TUNEL+ cells are E-cadherin+. We think that this may be an underestimate because E-cadherin staining intensity decreases in many cells after shedding. This is commented on in the text (lines 178-179).

Fig 2D: The point made on lines 182 to 186 that HIOs contain TUNEL + cells retained in the epithelial lining in the absence of PMNs is not very strongly supported by Fig 2D. Quantification of the number of intraepithelial TUNEL+ cells in the 4 compared conditions would make a more solid case.

We quantified TUNEL intensity in epithelial cells retained in the monolayer (S7 Fig). We do note that there is some variability in this phenotype that correlates with different batches of HIOs__.__

Fig2E: This experiment should be completed with a quantification of the percentage of TUNEL+ cells that are also cleaved caspase3-positive. The data, as currently displayed, do not prove that the cells negative for cleaved caspase 3 are apoptotic cells and thus do not support the sentence "suggesting that multiple forms of cell death were occurring in the PMN-HIO" (line 194).

Cells negative for cleaved Caspase-3 that are TUNEL+ may be undergoing some other form of cell death that is not Caspase-3 dependent, such as necrosis. This possibility is consistent with the decreased TUNEL signal observed upon inhibition of Caspase-4 (Fig 5A,B)__. __However, we have reworded our conclusion to identify more clearly what the data indicate, and where we are drawing inferences.

Fig3A: "IL1RN" should be changed for "IL1RA (IL1RN)" for consistency with Fig 3B.

The heatmap shows gene expression data so IL1RN is more consistent with the gene nomenclature. However, we have added an asterisk to the label on the heatmap, along with a sentence in the figure legend to elucidate.

Fig 4C: The authors should provide the percentage of infected cells rather than the number of bacteria per cell (this information can be included in supplementary).

Percent infected cells has been moved to Fig 4C and the number of bacteria per cell has been moved to Fig 4D__.__

FigS2: The different thicknesses of the epithelial layer observed between PBS and STM panels suggest a difference in scale. This may be double-checked by the authors.

The images are scaled similarly – as noted earlier (S10 Fig), there is considerable natural variability between HIOs that is not correlated with any experimental condition in this study.

Line 197-199, the authors claimed that uninfected cells may be observed in the cell lumen. This seems hard to observe/conclude at this resolution. The authors may show a non-infected cell at higher magnification. __

We have added higher magnification images, uninfected cells are indicated with white arrows in S8 Fig.

Discussion: Some important points should be added to the discussion. In particular, what is the fate of intracellular salmonellae after cell shedding? Can the bacterium survive cell apoptosis and burst out of the cell to re-infect the epithelium or be transferred to phagocytic cells during the clearance of intraluminal apoptotic cells? Previous studies showed that cytosolic hyper-replication could fuel cell shedding. The importance of bacterial load in PMN-induced cell shedding could be discussed.

We have expanded the discussion to elaborate on what may happen to shed cells. One useful feature of the HIOs is that the enclosed lumen allows us to capture the cells to fully measure the extent of cell shedding, however in the intestine where there is flow these cells would be washed away and could help to reduce bacterial load in the intestine. This point is now made in lines 386-388 in the discussion.

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

Major concerns

1) The authors show that only ~5% of the neutrophils have migrated to the lumen, which is a barely noticeable increase compared to PBS treated organoids. Does this reflect that the mucosal layer of the organoids might not produce neutrophil chemoattractants and that neutrophil recruitment during Salmonella is a bystander effect from a different cell type?

This number indicates that PMNs are ~5% of total cells in the PMN-HIO (including epithelial and mesenchymal cells) during Salmonella infection (not that only 5% of PMNs added migrated). Moreover, PMNs were added to a well containing multiple HIOs. We also show that HIOs do produce neutrophil chemoattractants during infection (S1 Fig).

2) How quickly are neutrophils recruited to the HIOs? The authors show one time point of 8 hours. Related to the relatively low number of neutrophils seen in their HIOs, is this perhaps a result of the time point they chose? Will they see more neutrophils recruited if they go longer?

It is likely that 5% of total cells in the PMN-HIO represents a significant recruitment of PMNs, and our data clearly indicate a marked effect on the infected epithelium. PMNs can cause substantial tissue damage, and their recruitment and activation is known to be tightly regulated. Due to the short-lived nature of human PMNs it would be difficult to extend this experiment to later timepoints. We have experimentally characterized PMN migration at 24h and by that time, most of the PMNs that we observe are non-viable, thus we focused our studies earlier.

3) The authors show that PMNs did not kill STM in their organoids, but they do in pure culture. Is this simply because of the low levels of neutrophils present in their HIOs, which would result in lower concentrations of antimicrobials being produced in the HIO lumen? If the authors are able to get higher levels of neutrophils in their HIOs, would they see increased bacterial killing?

Neutrophils have both inflammatory signaling and microbicidal functions. For example, Cho, et al (PLoS Pathogens 2012) find that neutrophil-derived IL-1 beta is sufficient to support abscess formation in the innate immune response to Staphylococcus aureus soft tissue infection. Similarly, a recent study showed that activation of neutrophils by keratinocyte defensins in a S. aureus skin infection led to neutrophil IL1 beta and CXCL2 release that amplified antibacterial defenses (Dong, et al Immunity 2022). Moreover, in the native environment of the gut with extensive microbiome colonization, direct neutrophil microbicidal activity might be less effective against infection than signaling. Recruitment of higher levels of neutrophils in vivo or in the HIO might exacerbate damage of the epithelial barrier. In the discussion, we speculate there may be proteins, like Elafin, that are upregulated during infection and inhibit some neutrophil functions as a trade-off to control host tissue damage. We reason that our data strongly support an inflammatory signaling role for neutrophils to promote innate immune responses of the intestinal epithelium.

4) Related to the above point, if the authors treat their HIOs with known neutrophil chemoattractants, can they increase the number of neutrophils that migrate into their organoids?

High levels of chemoattractants are already being produced in the HIO in response to infection (S1 Fig). The most effective number of neutrophils in the context of intestinal infection may not be the highest number, given that neutrophils can cause tissue damage. Since we see a marked phenotype with the neutrophils that are recruited, we propose that this PMN-HIO model reveals important inflammatory signaling roles for PMNs to promote intestinal epithelial immune function.

5) The authors speculate that Salmonella may "employ specific mechanisms to overcome PMN effector functions in the HIO luminal environment". Are any such mechanisms known? If so, the authors could test this hypothesis by repeating these experiments with Salmonella mutants in which these mechanisms are ablated. In this case, they should see increased killing of Salmonella by PMNs in the HIO lumen.

The focus of this study was to test how PMNs contribute to the host response against wildtype Salmonella. In the PMN-HIO model, we find that neutrophils direct a robust epithelial cell extrusion response, impacted intracellular bacterial numbers, and that Salmonella luminal colonization is not affected by PMNs. Thus, our data are pointing to an important inflammatory role for neutrophils in the infected intestine. Indeed, reliance on direct bactericidal mechanisms in the intestinal lumen which in vivo would be colonized with the microbiota might be a losing strategy for neutrophils, which would be hugely outnumbered.

6) Furthermore there is no information of the activation status of the neutrophils. How does the surface expression of CD16 CD62L, CD66 and CD11b look between the migrated and non-migrated and between infected and uninfected controls? Did the neutrophils de-granulate? Are they CD63+ or is the high levels of NGAL and S100 proteins an effect of lysis? The authors should also be careful in claiming that there is NETosis as the image in the supplement look more like an artifact than actual NETs.

Our new findings suggest that IL-1 production by PMNs is the biggest factor in driving the cell death phenotype. We have also added a figure with CD63 staining. We were able to visualize some localization of CD63 to the cell surface of PMNs, consistent with degranulation (S4 Fig).

7) Why does ASC translocate to the nucleus? Is the IL-1b cleavage mediated through Caspase-1 or Caspase-11? The neutrophils stained positive in the lumen appear to be intact, does this mean that pyroptosis does not occur, or does the IL-1b come from cells that did not migrate through the mucosal membrane? Staining for IL-1 and the different caspases might help resolve this question.

ASC does not appear to be translocating to the nucleus. In Fig 3D the green signal (ASC) is primarily excluded from the DAPI-stained area. In this human model, Caspase-11 is not present, and inhibition of Caspase-1 is sufficient to block the cell shedding phenotype (Fig. 5A,B and Fig. 6B,C). We are unable to distinguish whether IL-1 is being produced by intact PMNs or PMNs that are undergoing pyroptosis. Unfortunately, there are not suitable antibodies for fixed immunofluorescence staining for cleaved Caspase-1, and as a secreted protein, IL-1 beta likely will not remain localized with the producer cell.

8) The authors comment that there is substantial TUNEL staining in the mesenchyme independent of STM or PMNs, however, there is no explanation for why this happens. Does this have any downstream effects on the neutrophils that doesn't migrate towards the lumen?

TUNEL positivity in the mesenchyme is likely an artifact of culturing and we have noted this in the text (line 169-172). The extent of TUNEL+ mesenchymal cells appears to be dependent on the batch of HIOs as not all HIOs exhibit this phenotype (for example Figs 4A and 6B). In contrast, the extent of TUNEL+ luminal cells is significantly dependent on the presence of PMNs and Salmonella.

Minor comments

1) The authors should remove that MPO is neutrophil-specific, monocytes are known to have higher MPO expression than neutrophils.

In this controlled co-culture system there are no monocytes, therefore we have modified our text to indicate that MPO is used as a neutrophil marker in the PMN-HIOs (line 161).

2) If the authors performed flow cytometry as they say, they should provide the flow plots and the gating strategy they used in the supplement.

Representative flow plots for the data presented in Fig 1A are now included in S2 Fig. The data shown in Figs. 1A and S2 Fig are not gated.

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

Major Comments

1.Overall the study is convincing and it is well-conducted. This reviewer found it surprising that the PMNs did not alter the total levels of STM in the HIOs as neutrophils are expected to control the infection. Can the authors elaborate on if the intraepithelial numbers are reduced, what happens to STM in the lumen? It would be convincing if the authors can extend the infection timeline to see if the neutrophils are capable of killing luminal STM. *

One of the limitations of the HIO model is the lack of flow in the lumen. It is likely that shed cells would be removed from the body following extrusion in vivo. In the HIOs, since the cells are trapped in the lumen, Salmonella could then reinvade and so this phenotype might be even stronger in a model that incorporates flow. We have added this point to the discussion (lines 387-390). Due to the short-lived nature of PMNs, it is difficult to extend the infection beyond 8h. While in vitro experiments with just neutrophils and STM as we and others have performed might set the expectation that neutrophils would alter luminal bacterial levels, there is little to no direct evidence that neutrophil bactericidal activity is critical in the context of the intestinal environment (vs. releasing ROS or inflammatory signals that may have complex indirect effects). Indeed, an advantage of the HIO model is that we are able to test the function of neutrophils in a multi-component system, but one that is still sufficiently simplified that we can do some mechanistic analysis.

2-It would be powerful to conduct the caspase inhibition on neutrophils prior to HIO co-culturing to convincingly show that the effects of caspase inhibition effect neutrophils which in turn effect the epithelium disrupting the epithelial load of STM.

We appreciated this suggestion. We pretreated the PMNs with a Caspase-1 inhibitor for 1h prior to co-culture with infected HIOs. We found that this was sufficient to block TUNEL cell accumulation in the lumen of infected PMN-HIOs. These results are now presented in Fig 6B,C.

3- While other caspases are well-established to be involved in Salmonella-related cell death and epithelial shedding, why did the authors picked caspase 3 but not caspase 4/5 to show activation in Fig 2?

We have now also tested the role of Caspase-4 on cell shedding using z-LEVD-fmk inhibitor. Consistent with prior published studies, we found that Caspase-4 inhibition reduced the accumulation of TUNEL-positive cells in the PMN-HIO lumen. These results are presented in Fig 5. There are no detectable levels of Caspase-5 in the HIOs (S9 Fig).

Minor comments

Fig 1C It is not clear how the total bacterial burden was determined. Please include details such as the timepoint and sufficient details of the technique both in the results section and the legend.

These details have been added in the figure legend (line 605-607). Briefly, HIOs were washed with PBS and homogenized in PBS at 8hpi. CFU/HIO were enumerated by serial dilution and plating on LB agar.

• Fig S2. Authors claim that the PMNs form NETs in the lumen, however, the marker used in the immunostaining is MPO. Although a NETting is seen in the images, MPO staining is not sufficient to claim these are NETs. Additional staining is required to show if the neutrophils in the lumen are intact or formed NETs*.

As noted in response to Reviewer #1, although we commented on NETs in our original manuscript, our conclusions do not rely on the presence or absence of NETs and our new data implicates PMN IL-1 as necessary and sufficient for the cell shedding phenotype. We have therefore removed the NET data and the reference to NETs. While NETs are potentially interesting in the context of intestinal infection, we understand the reviewer's concern about NETs and anticipate that a more quantitative characterization of NETs may be challenging given the structure and variability of the PMN-HIOs.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Lawrance et al investigates a novel human intestinal organoid (HIO) model to elucidate the mechanisms of STM infection especially at the epithelium level. Previously, several studies had identified that epithelial cell death and extrusion of S. enterica infected cells regulate the infection outcome by reducing epithelial bacterial burden and restricting the infection to the intestine. However the mechanisms that drive this phenotype is not well understood. In this study authors use HIOs to investigate these interactions. HIOs were microinjected with STM and then seeded with primary human polymorphonuclear leukocytes (PMN-HIOs), specifically neutrophils and analyzed for bacterial growth and host cell survival. Authors made the critical observation that adding PMNs to infected HIOs lead to epithelial shedding and reduced bacterial burden that could be blocked by Caspase-1 or Caspase-3 inhibition. Overall, this is a novel study and establishes a novel model to study the PMN-epithelium interactions in the context of pathogens.

Major Comments

1. Overall the study is convincing and it is well-conducted. This reviewer found it surprising that the PMNs did not alter the total levels of STM in the HIOs as neutrophils are expected to control the infection. Can the authors elaborate on if the intraepithelial numbers are reduced, what happens to STM in the lumen? It would be convincing if the authors can extend the infection timeline to see if the neutrophils are capable of killing luminal STM.
2. It would be powerful to conduct the caspase inhibition on neutrophils prior to HIO co-culturing to convincingly show that the effects of caspase inhibition effect neutrophils which in turn effect the epithelium disrupting the epithelial load of STM.
3. While other caspases are well-established to be involved in Salmonella-related cell death and epithelial shedding, why did the authors picked caspase 3but not caspase 4/5 to show activation in Fig 2?

Minor comments

1. Fig 1C It is not clear how the total bacterial burden was determined. Please include details such as the timepoint and sufficient details of the technique both in the results section and the legend.
2. Fig S2. Authors claim that the PMNs form NETs in the lumen, however, the marker used in the immunostaining is MPO. Although a NETting is seen in the images, MPO staining is not sufficient to claim these are NETs. Additional staining is required to show if the neutrophils in the lumen are intact or formed NETs.

Significance

see above

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Referee #2

Evidence, reproducibility and clarity

The authors have submitted a manuscript aiming to distinguish the role of neutrophils during the onset of Salmonella infection. In contrast to the expected results, the authors propose that the neutrophils have a regulatory role in mediating intestinal integrity rather than antimicrobial effects. However, the data supporting this statement are not provided. Although the authors provide some very interesting findings there are some flaws that need to be addressed.

Major concerns

1. The authors show that only ~5% of the neutrophils have migrated to the lumen, which is a barely noticeable increase compared to PBS treated organoids. Does this reflect that the mucosal layer of the organoids might not produce neutrophil chemoattractants and that neutrophil recruitment during Salmonella is a bystander effect from a different cell type?
2. How quickly are neutrophils recruited to the HIOs? The authors show one time point of 8 hours. Related to the relatively low number of neutrophils seen in their HIOs, is this perhaps a result of the time point they chose? Will they see more neutrophils recruited if they go longer?
3. The authors show that PMNs did not kill STM in their organoids, but they do in pure culture. Is this simply because of the low levels of neutrophils present in their HIOs, which would result in lower concentrations of antimicrobials being produced in the HIO lumen? If the authors are able to get higher levels of neutrophils in their HIOs, would they see increased bacterial killing?
4. Related to the above point, if the authors treat their HIOs with known neutrophil chemoattractants, can they increase the number of neutrophils that migrate into their organoids?
5. The authors speculate that Salmonella may "employ specific mechanisms to overcome PMN effector functions in the HIO luminal environment". Are any such mechanisms known? If so, the authors could test this hypothesis by repeating these experiments with Salmonella mutants in which these mechanisms are ablated. In this case, they should see increased killing of Salmonella by PMNs in the HIO lumen.
6. Furthermore there is no information of the activation status of the neutrophils. How does the surface expression of CD16 CD62L, CD66 and CD11b look between the migrated and non-migrated and between infected and uninfected controls? Did the neutrophils de-granulate? Are they CD63+ or is the high levels of NGAL and S100 proteins an effect of lysis? The authors should also be careful in claiming that there is NETosis as the image in the supplement look more like an artifact than actual NETs.
7. Why does ASC translocate to the nucleus? Is the IL-1b cleavage mediated through Caspase-1 or Caspase-11? The neutrophils stained positive in the lumen appear to be intact, does this mean that pyroptosis does not occur, or does the IL-1b come from cells that did not migrate through the mucosal membrane? Staining for IL-1 and the different caspases might help resolve this question.
8. The authors comment that there is substantial TUNEL staining in the mesenchyme independent of STM or PMNs, however, there is no explanation for why this happens. Does this have any downstream effects on the neutrophils that doesn't migrate towards the lumen?

Minor comments

1. The authors should remove that MPO is neutrophil-specific, monocytes are known to have higher MPO expression than neutrophils.
2. If the authors performed flow cytometry as they say, they should provide the flow plots and the gating strategy they used in the supplement.

Significance

The addition of neutrophils to human intestinal organoids in the context of infection with a bacterial pathogen is an advance in the field. The findings would be of interest to many fields of research including host-pathogen interactions, innate immunity and neutrophil experts. Based on my expertise in innate immunity and bacterial pathogenesis, I believe that i can offer appropriate suggestions for improving the study.

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Referee #1

Evidence, reproducibility and clarity

Summary:

To address the question of the role of neutrophils in controlling epithelial cell response during bacterial infection, the authors developed an ambitious model of human intestinal organoid (HIO) micro-injected with Salmonella and co-cultured with polymorphonuclear leukocytes (PMNs). They could observe the transmigration of PMNs within the HIO lumen upon infection, associated with an increased epithelial cell extrusion and a decreased association of extracellular salmonellae with the epithelium. The authors analyzed the specific transcriptomic signature of PMN-HIOs during infection as well as the cytokine release. They further linked the cell shedding phenotype with Caspase 1 and Caspase 3 cleavage, the decreased intraluminal bacteria burden with Caspase-1 activity, and the decreased Salmonella association with the epithelium with Caspase 3 activity.

Major comments:

Some important links are missing to fully support the mechanistic model proposed:

1- PMN activity

The authors may strengthen their evidence of PMN activities presented in lines 135 to 143 and in Fig.S2 and S3. In particular, the authors claim that PMNs form NETs in PMN-HIOs but the evidence displayed are limited. In fact, Fig S2 shows the same condition and same staining as Fig 1B but the MPO-positive structures are different. Clarification in the text or the figure would be welcome. Besides, as the authors insist on the relevance of NETs in the discussion, it seems that a clear demonstration and characterization of these structures in the PMN-HIO model would highly benefit the manuscript.

Regarding the analyses of the culture supernatants (Fig.S3), only 3 out of the 5 displayed datasets are commented on in the text. The data obtained for BD2 and N-Gal should be either commented or removed from the figure. The author further suggests that Elafin expression in presence of PMN may restrict PMNs' ability to kill Salmonella. Repeating the experiment displayed in Fig S1 in the presence of Elafin as well as in the presence of the supernatant extracted from HIOs and PMN-HIOs would clarify the potential inhibition of PMN killing capacity in the PMN-HIO model.

The author proposed that infected and uninfected cells are extracted from the epithelium due to PMN activation, suggesting that Salmonella infection of epithelial cells is only indirectly involved in cell shedding. This is an interesting hypothesis that could be tested by measuring cell shedding in a non-infected but PMN-activated (for instance with PMA) PMN-HIO model. This would clarify further the role of PMN in controlling epithelial response to the infection.

2- Specificity of RNA-seq profiling:

The authors analyzed the transcriptomic profiling of PMN-HIOs and HIOs infected or not. While these experiments bring to light an interesting difference in inflammasome/cell death transcriptomic programs at the scale of the co-culture model, it is not possible to conclude from which cell type these transcriptomic shifts emerge. To clarify this, the authors stain the co-culture for ASC and observe that ASC-positive cells are PMNs. They conclude that PMNs are most likely the primary site of caspase-1 dependent production of IL1. While their model is theoretically consistent, more direct proofs are necessary to conclude on the cell-type specific transcriptomic program during infection of PMN-HIO and could be obtained by FACS sorting of the cells prior to RNA-seq, for instance using MPO to detect PMNs and E-cadherin to detect epithelial cells.

3- Roles of cytokine

After showing an increased expression/release of IL1 and IL1RA in infected PMN-HIOs, the authors move on to testing the role of caspases on cell shedding. Yet, they do not test the impact of IL1 and IL1RA on cell shedding. As, according to their proposed model, IL1 is acting upstream of caspase-1 to promote cell shedding, testing cell shedding in infected PMN-HIOs in the presence of an IL1 inhibitor would clarify that link. The author also proposed that the decrease of IL33 in PMN-HIOs compared to HIOs could be due to PMN processing, which would give an additional role to PMNs in controlling the epithelial response to infection. In the context of this manuscript, it would be highly relevant to test this hypothesis by measuring the rate of cleaved IL-33.

4- Roles of caspase

The interpretations of the role of Caspases to restrict bacteria burden are unclear and should be revised (see also minor comment). It appears that both Caspase-1 and Caspase-3 are necessary for efficient cell shedding (Fig4B), Caspase-1 (but not Caspase-3) decreases intraluminal bacteria burden (Fig4C) and Caspase-3 (but not Caspase-1) decreases epithelium-associated bacteria (Fig4D). To reconcile these observations with the hypothesis that cell shedding is responsible for the decrease of intraluminal and epithelium-associated bacterial burden, one may propose that caspase-3 (but not caspase-1) induces cell shedding of mainly non-infected cells (possibly bacteria-associated) and caspase-1 (but not caspase-3) induced cell shedding of infected cells. This could be tested by measuring the % of infected extruded cells upon caspase inhibitor treatments. In addition, these data don't allow to propose that Caspase-3 activation happens downstream of Caspase-1 as suggested by the authors in their abstract figure.

Minor comments:

The majority of the points listed below can be addressed with further analyses of pre-acquired data sets:

Fig1E/1F/4D: each green dot is not likely to be individual bacteria but rather a cluster of bacterium (based on their size). So the y-axis in Fig 1E and Fig4D should not be #STM.

Fig2A: Variations in organoid size and epithelial thickness can be observed between figures. In particular, in Fig 2A, the HIO seems much younger than the other ones displayed in the manuscript. Line 176 to 178, the authors mentioned the TUNEL+ cells in the mesenchyme but rule out the possibility that this phenotype could be infection or PMN-dependent because it is observed in the different conditions. As the picture displayed in Fig2A suggests high differences in the number of TUNEL+ cells in the mesenchyme under the 4 tested conditions, the authors should still quantify this phenomenon (possibly in the supplementary). "DAPI" should be written in blue.

Fig2C: Could the authors comment on the % of E-cadherin cells that are also TUNEL+? Is it 100%?

Fig 2D: The point made on lines 182 to 186 that HIOs contain TUNEL + cells retained in the epithelial lining in the absence of PMNs is not very strongly supported by Fig 2D. Quantification of the number of intraepithelial TUNEL+ cells in the 4 compared conditions would make a more solid case.

Fig2E: This experiment should be completed with a quantification of the percentage of TUNEL+ cells that are also cleaved caspase3-positive. The data, as currently displayed, do not prove that the cells negative for cleaved caspase 3 are apoptotic cells and thus do not support the sentence "suggesting that multiple forms of cell death were occurring in the PMN-HIO" (line 194).

Fig3A: "IL1RN" should be changed for "IL1RA (IL1RN)" for consistency with Fig 3B.

Fig 4C: The authors should provide the percentage of infected cells rather than the number of bacteria per cell (this information can be included in supplementary).

FigS2: The different thicknesses of the epithelial layer observed between PBS and STM panels suggest a difference in scale. This may be double-checked by the authors. Line 197-199, the authors claimed that uninfected cells may be observed in the cell lumen. This seems hard to observe/conclude at this resolution. The authors may show a non-infected cell at higher magnification.

Discussion: Some important points should be added to the discussion. In particular, what is the fate of intracellular salmonellae after cell shedding? Can the bacterium survive cell apoptosis and burst out of the cell to re-infect the epithelium or be transferred to phagocytic cells during the clearance of intraluminal apoptotic cells? Previous studies showed that cytosolic hyper-replication could fuel cell shedding. The importance of bacterial load in PMN-induced cell shedding could be discussed.

Significance

The manuscript is very clearly written and easy to follow for a broad audience. The model developed is cutting-edge and allows both testing previously established knowledge in a more physiological model and addressing new questions. In addition, this model may be adapted to other pathogens and is thus widely relevant to the fields of host-pathogen interactions and immunity. Using this model, the authors could investigate the cross-talk between the epithelium and neutrophils during Salmonella infection.

Yet, the mechanisms proposed by the authors remain at a speculative level and are not clearly/fully demonstrated by the data. In particular, the mechanistic investigation of caspase signaling linked to PMN-induced epithelial cell shedding is limited.

In conclusion, the model put in place by the authors opens many interesting opportunities, some of which are addressed by the authors but not investigated in-depth within this manuscript. Addressing the major points aforementioned would however extend the mechanical understanding of PMN implication in epithelial defense, making the manuscript more suited for mechanism-oriented journals with broad audience.

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Reply to the reviewers

This is already a full revision, not a revision plan. All points were carefully addressed. TMF

July 28, 2022

RE: Review Commons Refereed Preprint #RC-2022-01555

Dear Dr. Fuchs,

Thank you for sending your manuscript entitled "Dissecting the invasion of Galleria mellonella by Yersinia enterocolitica reveals metabolic adaptations and a role of a phage lysis cassette in insect killing" to Review Commons. We have now completed the peer review of the manuscript. Please find the full set of reports below.

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

In this manuscript Saenger et al. concentrate on the pathophysiological details of insect larvae infection by Yersinia enterocolitica. The authors studied the colonisation, proliferation, tissue invasion, and killing activity of the bacteria in Galleria mellonella larvae. Their study provides valuable evidence for the biological relevance of Tc toxins and a neighboring holin-endolysin cassette during establishment of Y. enterocolitica infection in Galleria mellonella larvae through the oral route. The findings of the authors provide important novel insights, that can be used for the development of Tc toxins as biopesticides.

In general, this is a nice study. The data and the methods are presented well so that they can be reproduced and the key conclusions convincing.

Unfortunately, the manuscript is sloppily written in some places, including grammatical and formatting errors. Citations regarding the structure and mechanism of action of Tc toxins are arbitrarily chosen, often taking the wrong ones and important aspects are left out. I highly recommend that the authors read the review of Roderer and Raunser 2019 that nicely describes and summarizes the molecular mechanism of Tc toxins.

Answer: We have now improved the writing of the manuscript and corrected several errors and typos. In particular, the review by Roderer and Raunser, as well as other literature in the field, is now considered and cited in the text.

The abstract ends with a speculation: "Suggesting that this dual lysis cassette is an example for a phage-related function that has been adapted for the release of a bacterial toxin" - this is likely true, but not proven in this work. What if it is used for the release of something else like extracellular DNA needed for biofilm formation (see https://doi.org/10.1038/ncomms11220)?

Answer: This sentence was carefully written as a hypothesis strengthened by the data obtained in our study. Experimental evidence for this assumption is the strong correlation of toxin and HE cassette phenotypes of mutants (see abstract), the highly conserved localisation of the cassette within Tc loci of distinct bacterial genera (see discussion for literature), and the synchronic regulation of both the toxin and the lysis genes (manuscript in preparation). Moreover, strain W22703 is unable to form biofilms in contact with invertebrates (Spanier et al., AEM 2010). There, also in accordance with other reviewers, we would like to keep this statement in the text. However, to address this interesting point, we now mention the finding of Turnbull et al. in the discussion (see last paragraph).

In addition to that, several outstanding issues must be addressed:

1. Line 45 3-D structural analysis of the tripartite Tc suggests a 4:1:1 stoichiometry of the A, B and C subunits, with the A subunit forming a cage-like pentamer that associates with a tightly bound 1:1 sub-complex of B and C. This is wrong. The stoichiometry is 5:1:1 and the structure is not a cage. The statement was taken from citation 3. However, citation 3 should not be used, since the stoichiometry as well as the structure that was determined there is wrong. Use Landsberg et al. 2012 PNAS, Gatsogiannis et al. 2013 Nature instead.

Answer: We apologize for misunderstanding the literature. Reference Lee et al. was removed here, and the two papers plus Meusch et al. (Nature, 2014) are now cited. The stoichiometry was corrected, “cage” was removed.

"Few bacteria are known to successfully colonize and infect invertebrates" - needs a reference.

Answer: This was modified to “Several bacteria…”, and we cite the recent paper by Weber and Fuchs (in press) that in Table 7g lists more than 40 bacterial species pathogenic towards insects.

"Their oral insecticidal activity is comparable to that of the Bacillus thuringiensis- (Bt)- toxin" - reference missing.

Answer: The reference is now cited (Bowen et al., Science 1998). Please see the last paragraph of the paper.

"Type a, type b and type c" subunits is not usual for the literature. Please use TcA, TcB, TcC. A-, B-, and C-components should be abbreviated as TcA, TcB and TcC respectively in order to be in line with recent literature on the topic.

Answer: This was corrected accordingly.

Is TccC an ADP-ribosyltransferase or does it have a different biochemical activity?

Answer: This is unknown with respect to the Tc of Y. enterocolitica. In the introduction, we now refer on P. luminescens and do not further attribute such a function to the TcC of Y. enterocolitica. In the abstract, we replaced “ADP-ribosylating” with “toxic”.

"The toxic and highly variable carboxyl-terminus of TccC that has recently been demonstrated to ADP-ribosylate actin and Rho-GTPases" - this is only certain for TccC3 and TccC5 from P. luminescens. There are many such C-termini, called HVRs which have not had their activities determined yet, see here: https://doi.org/10.1371/journal.ppat.1009102

Answer: We agree and cite this article. See also the response to comment 5 above.

"is probably followed by receptor-mediated endocytosis" - more recent references exist for the receptor binding of Tc toxins.

Answer: We added two references pointing to glycans as receptors of the Tc (line 52).

"A pH decrease then triggers the injection of a translocation channel formed by the pentameric TcaA subunits into the endosomal vacuole, followed by the subsequent release of the BC subcomplex into the cytosol of the target cell" - this again is incorrect. Please read the above mentioned review and correct this passage accordingly.

Answer: We agree. This phrase was rewritten to “The attachment of the Tc to the host cell membrane is either followed by receptor-mediated endocytosis or release of the ADP-ribosyltransferase into the target cell {Landsberg, 2011 #738;Sheets, 2011 #742}{Meusch, 2014 #788}. In a pH-dependent manner, the TcA translocation channel injected into the membrane of the host cell. Conformational changes then allow the toxic component to be released into the translocation channel of TcA and from there into the cytosol {Meusch, 2014 #788}{Roderer, 2019 #871}.” (Lines 51-56)

What is meant by "environmental Yersinia species"?

Answer: This was corrected to “…and in Y. mollaretii.”

In the relevant W22703 pathogenicity island sequence (https://www.ncbi.nlm.nih.gov/nuccore/AJ920332) previously submitted by the same group, something odd is going on with the TcA component: it appears to be split into three polypeptides (tcaA, tcaB1, tcaB2). In the manuscript you state TcA is made up from only tcaA and tcaB. Could you please address this?

Answer: Shotgun sequencing was performed 15 years ago, and mapping revealed a frameshift within tcaB that resulted in the split annotation of tcaB. Even if this frameshift is not the result of a sequencing error, it obviously does not result in Tc inactivation. As this frameshift was not identified in most other Tc-PAI of yersiniae, we assume our statement to be correct.

"And their products were recently shown to act as a holin and an endolysin, respectively" - missing reference.

Answer: The reference is now cited (Springer et al., JB 2018).

"Its Tc proteins are produced at environmental temperatures, but silenced at 37{degree sign}C." versus "Remarkably, HolY and ElyY lyse Y. enterocolitica at body temperature, but not at 15{degree sign}C". Please address the issue that HolY/ElyY lyse the bacteria at temperatures where Tc proteins are not produced.

Answer: In the absence of in vitro conditions activating the HE gene cassette, we used the pBAD system to artificially overexpress the two genes and showed cell lysis at 37°C, but not at 15°C (Springer et al., JB, 2018). This finding points to a lack of cell lysis as prerequisite for TC release and strengthens the hypothesis of a new secretion system as now corroborated in the last paragraph of the discussion. To avoid confusion of readers, the sentence was removed from the manuscript.

"Nematodes, which are easily maintained in the laboratory without raising ethical issues, have successfully been used to identify virulence-related genes in a broad set of bacterial pathogens" - what is the relevance of this for the current manuscript?

Answer: Invertebrates are introduced here as infection models. Nematodes are mentioned here for two reasons: yersiniae are nematocidal due to the Tc, and their immune system is less elaborated than that of G. mellonella, thus explaining its preferred use as insect model. We shortened the sentence by deleting the phrase in commas.

Fig. 1C - no description is given for the labels 1-8.

Answer: This is given below figures 1E-H. The labels are valid for all figure panels to ease reading.

"The hemolymph of these cadavers was found full of Y. enterocolitica cells" - injected CFUs are provided here, but not final CFUs in the cadavers (although referred to in a later section). Please address this.

Answer: These were preliminary experiments to identify the optimal infection dose. Hemolymph content was plated, but cell numbers in the hemolymph were not enumerated. This sentence therefore now reads: “…and the hemolymph of these cadavers contained Y. enterocolitica cells.” (lines 113-114).

What is the inducing agent used for pACYC-tcaA and pACYC-HE? Why would "slight leakiness of the pBAD-promoter" make pBAD-tccC non-inducible? Were colonies taken from the cadavers to verify that the bacteria still contained these plasmids?

Answer: Within pACYC, the genes tcaA and hlyY/elyY (HE) are under control of their own promoters as indicated in Table S2. In general, pACYC vectors are often and successfully used for complementation due to middle copy number.

This now reads “Due to the slight leakiness of the pBAD-promoter, arabinose was not added to further induce tccC transcription.” (lines 133-134).

The presence of the plasmids in vivo was confirmed by periodic plating on selective and non-selective plates, not revealing differences in cell numbers.

Can the authors please address the TD50 of 1.83 days for W22703 ΔHE/pACYC-HE versus 3.67 days for WT bacteria? This would mean that the former kill larvae twice as fast as usual. I would not call this "did not significantly differ in their insecticidal activity".

Answer: This statement is indeed not very intuitive given the variations of the TD50-values. However, the significance here (and elsewhere in the text) is based on a statistical calculation. For the Kaplan-Meier-plot, we used an application (K.T.Bogen, Advances in Molecular Toxicology, 2016; Exponent Health Sciences, Oakland, CA, United States; Johann Kummermehr, Klaus-Rüdiger Trott, Stem Cells, 1997; Academic Press, London, San Diego) based on all data of a graph. However, to consider this point and to not confuse the readers, the phrase was modified to “…did not significantly differ in their insecticidal activity from that of the parental strain W22703 after one week, demonstrating…” (lines 135-138).

Fig. 2 is missing survival data for larvae infected with tcaA, HE, and tccC KO bacteria.

Answer: These data are shown and are equal to the LB-control, e. g. the survival rate of larvae infected with strains W22703 lacking HE, tcaA, or tccC were 100%.

"And a slight colouring of some of the larvae from one h p.i. on (data not shown)" - best show the data or remove this statement.

Answer: Although we observed this phenomenon regularly, monitoring and documentation cannot be provided and would not substantially strengthen the manuscript. We therefore deleted this phrase.

The infection of larvae by W22703 ΔtccC/pBAD-tccC is missing, the other bacterial variants are present. Please address this.

Answer: Infections with W22703 DtccC are not shown to not overload the figure, please see the panel below. W22703 DtccC/pBAD-tccC infections have not been documented by photos. Figure legend 3 now reads “Infections with W22703 DtccC and DtccC/pBAD-tccC are not shown.”

"initially proliferated from an application dose of 4.0 × 105 CFU and 4.0 × 105 CFU, respectively, to 2.2 × 106 CFU and 2.8 × 106 CFU, but could not be detected from day three on. This finding strongly suggests that TcaA is involved in adherence to epithelial cells and thus in midgut colonization". Please address the "initially proliferated" (which day post-infection?), their elimination from the larvae (how, why?), why the tccC KO bacteria were more virulent than tcaA KO bacteria, and where the suggestion about TcaA involvement specifically in adherence comes from.

Answer: “initially proliferated” was rewritten to “proliferated within the first day p.i.”. (line 163)

Elimination: This now reads “…was completely absent six days p.i., probably due to passage through the gut followed by excretion”. (lines 161-162)

In our view, the tccC knockout mutant is not more virulent than W22703 DtcaA (se Fig. 2), but replicates during the first day post infection, whereas the cell numbers of the tcaA KO mutant strongly decrease already within the first 24 h p.i.. This prompted us to speculate that Tc is involved in two infection steps, e.g. adherence and hemocyte inactivation. For clarity, this sentence was modified to: “This discrepancy suggests that TcaA is involved in adherence to epithelial cells and thus in midgut colonization, without requiring TccC.” (lines 165-166)

In Fig. 4, the CFUs for W22703 ΔtccC/pBAD-tccC are essentially the same as for the other rescued KOs and WT, while in the text a point about weaker growth is made. Is this justified? Also, even though the CFU data is present here, data on infection of larvae by W22703 ΔtccC/pBAD-tccC is missing unlike the other bacterial variants. Please explain.

Answer: We agree that this part of the results is misleading. We want to stress that the complementation very well restores the phenotype of the wildtype. The weaker growth of DtccC may be due to the distinct vector system used here. This part was there shortened and rephrased to: “When larvae were infected with 4.0 × 105 CFU of the DtcaA and DHE mutants, and with 1.4 × 106 CFU of strain W22703 DtccC/pBAD-tccC, all of which carrying the deleted genes on recombinant plasmids, the bacterial burden at days one to six p.i. increased approximately to that of the parental strain W22703 applied with 9.0 × 105 CFU, indicating a successful complementation of the gene deletions.”

” (lines 166-170).

Missing data on W22703 ΔtccC/pBAD-tccC infection in Fig. 3, please the answer to point 20 above.

Fig. 6b - The presence of an anti-RFP signal is not obvious in any of the bottom row images. The top row images are missing the same kind of annotation provided for Fig. 6a, without which non-histologists will find understanding the figure difficult.

Answer: The anti-RFP signal is visible only on the left photo of the bottom panel, and not in the other three photos as explained in the text. We understand that the signals are not very strong, but they are visible on the screen.

"In the absence of the lysis cassette, however, TcaA::Rfp was not detected despite the presence of W22703 ΔHE tcaA::rfp cells." + "To test whether or not the promoter of the lysis cassette is active in vivo, we infected G. mellonella larvae with strain W22703 PHE::rfp. Although Y. enterocolitica cells densely proliferated within the hemolymph (FIG. 6B), no staining signal that would point to the presence of TcaA was obtained, possibly due to no or weak PHE activity." Does this mean that without HE, tcaA does not express?

Answer: No, we performed Western Blots showing that TcaA is detected in cells lacking HE. Therefore, a negative feedback regulation (e. g. increasing intracellular amounts of TcaA repress its own transcription) can be excluded. This is also in line with the low transcriptional activity of the lysis cassette in vivo (new Fig. S1B).

"These data suggest that the HE cassette is responsible for the extracellular activity of the insecticidal Tc." Please explain how the preceding paragraph leads to this conclusion.

Answer: This was poorly written and now reads “…for the transport…” (line 224).

"As expected, bacterial cells, e.g. Y. enterocolitica, are visible in the hemolymph obtained from W22703-infected animals, but not in all other preparations." - which figure are the authors referring to?

Answer: We have indeed identified, but not immunostained, bacterial cells in those preparations, but they are not visible in Fig. 7. This sentence was removed. However, the presence of W22703, but not its tc-PAIYe-mutants, in the hemolymph is demonstrated in Fig. 6A.

"To delineate the transcriptional profile of Y. enterocolitica during infection of G. mellonella, we applied immunomagnetic separation to isolate Y. enterocolitica from the larvae 12 h and 24 h after infection" - do the authors store the bacteria for up to 24 h at 4 {degree sign}C, as indicated in the methods section?

Answer: Yes, the probes were stabilized with RNAlater and then stored up to 24 h to synchronize all samples of one experiment.

"The endolysin located within Tc-PAIYe was significantly up-regulated after 24 h, but not after 12 h, pointing to its possible role in the release of the Tc" - I could not find the endolysin in Table S1. Could the authors mark it clearly? Also, why is the holin also not upregulated?

Answer: The endolysin gene is lacking in Table S1 due to its FC=1.02. We now added a table to Fig. S1 that shows the FC values of all genes from Tc-PAIYe. The FC-value of holin gene is 0.87, thus pointing to a very slight transcription of this lysis gene as discussed, thus preventing cell death.

"This is in line with the fact that a T3SS is lacking in strain W22703" - Is a complete genomic sequence available for this strain, so readers could validate this statement?

Answer: The genome sequence is available, and the reference is now cited (line 358). The common virulence plasmid of yersiniae, pYV that encodes the T3SS, is missing in this strain. We do not mention here the presence of a second, but probably incomplete, chromosomally encoded T3SS in strain W22703 do not overload the manuscript.

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

This is a very, very nice study as it actually describes the role of different Tc toxin components in a model infection system using an important bacterium- really for the first time in a properly controlled manner. The mutants lacking either the syringe (AB) or the bullet (C) make 'sense' for a loss of function perspective. The description of the phage cassette in loss of function is also interesting and could do with some more speculation? For example, some groups of Photorhabdus bacteria release their oral toxicity (Tc's) into their bacterial supernatants- whereas in others it remains cell associated. The likely role of this phage cassette in this process should be discussed (is cell suicide required for release?).

Answer: We now discuss the possibly role of the lysis cassette in more detail, including the possibility that a subpopulation commits cell suicide (see lines 375-396).

Reviewer #2 (Significance (Required)):

This is highly significant finding as despite all of the very elegant structural studies done on these important toxins there is still very little work in vivo. These studies clearly show the role of the different components of these ABC toxins in vivo. It should be published with priority.

Congratulations to the authors.

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

Summary: The authors analyze the phases of infection of Galleria mellonella by Yersinia enterocolitica following forced oral feeding. They study different phases of infection, including survival within the gut and invasion of the hemolymph. By analyzing differences in the genes up- and down regulated, they show that for example transporters for food sources from the hemocoel are regulated for making those sources available for the bacteria.

Major comments: This is an interesting paper demonstrating genes of Y. enterocolitica dependent for colonization, growth and crossing of the epithelial gut barrier in G. mellonella.

Major points which have to be addressed:

Introduction: line 54: the BC subcomplex is not released into the cytosol! It is only the hypervariable region (enzymatic part) which enters the cytosol. This has to be corrected.

Answer: This has been corrected accordingly.

Fig.2/3: Why have different CFU been used for the distinct bacterial strains? This does not allow a direct comparison of their toxicity. For me the dead larvae shown in Fig. 3 are not represented in Fig 2 (data are not concordant), because of the loss before day one depicted in Fig. 2: The curves should be normalized to the same starting point (should be 100 %)?

Answer: We would like to stress here that infection doses are hard to reproduce if frozen and diluted stocks are used. We decided for overnight culture to better mimic natural conditions and controlled each culture for its viable cell numbers by plating. Moreover, we choose the infection doses in a conservative manner, e.g. the number of mutants was higher than that of the parental strain.

The data of Fig. 3 are concordant with Fig. 2 for two reasons: First, this experiments was performed in replicates with a total of 36 larvae per strain (see Fig. 2 legend), so that representative photos are shown. Second, larvae were considered dead if they failed to respond to touch, and many larvae without strong sign of melanisation were already killed.

We analysed the algorithmus of the Kaplan-Meier-plot. All graphs start at 100%, this is now mentioned in the legend. There are no data between day 0 and day 1, and a stepwise graph is essential for this plot.

Fig. 3: Why is the strain W22703 delta tccC/pBAD - tccC missing in the data set?

Infections with W22703 DtccC are not shown to not overload the figure, please see the panel below. Answer: W22703 DtccC/pBAD-tccC infections have not been documented by photos. Figure legend 4 now reads “Infections with W22703 DtccC and DtccC/pBAD-tccC are not shown.”

Minor: line 221: "the" is doubled

Answer: This has been corrected accordingly.

Reviewer #3 (Significance (Required)):

The manuscript shows the use of G. mellonella as a straight foreward method to study gene functions of pathogenic bacteria, a significant knowledge for scientists of the field.

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

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

Answer: There are already three sections that summarize the results and the methods applied, namely the abstract, the last paragraph of the introduction, and the conclusion following the discussion. In our view, a further summary would overload the manuscript. Nevertheless, depending on the journal the manuscript will be published in, an additional authors´ summary would be provided.

Outlines proposed role of lysis cassette in oral infection of Galleria as a model insect for host pathogen interaction, data which is fortified through use of histology and RNAseq.

Introduction could extend to additional background eg Aleniz et al and other entomopathogen transcriptome data, more so other studies using Yersinia and Galleria as a model (refer references provided in the below comments)

Answer: We again carefully screened PubMed for studies in the field and added few papers. However, in vivo transcriptome analyses are still rare, as indicated by a lack of a respective investigations with the highly relevant entomopathogen Photorhabdus luminescens. The literature suggested by the reviewer is now cited in the introduction and the discussion (see below for details).

The strength of the paper lies in understanding the progression of the disease in the insect host as mentioned L316-317 and clearance of the bacteria via in TcaA mutant

Major comments: - Are the key conclusions convincing? Yes for mode of action Fig 5 could have additional panels -this is a strength of the paper

Answer: We agree that this time course is a strength of the paper, and we carefully selected representative photos. There are several to be shown, but to our view, they are rather illustrative than providing a substantial additional value.

Fig 6 legend could better describe the observed insect components

Answer: The insect components are now indicated in Fig. 6B and in Fig. 5.

Figure 7 may be lost in PDF conversion -the figure appears un resolved? are there more high resolution photos

Answer: Fig. 7 was present in the merged PDF provided by the publisher. We used the photos with the best resolution.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? the data provided is in places rudimentary (i.e. validation of the role of the lysis cassette in virulence) and could be bolstered with the construction and use of a lysis translational reporter etc I was left unsure how the HE::rfp and TcA::rfp constructs were made. I had assumed red florescent protein however it appears an antibody is used. This needs to be clarified as I then found it hard to interpret the results.

Answer: The transcriptional PHE::rfp fusion is mentioned in the results section, but immunostaining failed probably due to a very low promoter activity (line 223). This is well in line with the transcriptome data. Please see a detailed answer how the HE::rfp and tcaA::rfp were constructed below. We applied the RFP-antibody for two reasons: first, fluorescence microscopy did not reveal clear red fluorescence in the tissue sections, and second, a TcaA antibody failed to match quality criteria for this purpose.

It appear l114-125 that their may be enough data to derive a LD50 values and or LT value at a fixed dose - if so reporting this data of interest. It may also allude as to why a 10e5 dose was selected for subsequent expts

Answer: This is an interesting point. The LD50 (dose of cells that kills 50% of all larvae) is usually not calculated in publications in this field of research, because its calculation requires a very huge separate data set that cannot be used to answer the questions addressed here. Such a dat set is not available. We published the dose-dependent toxicity of Y.enterocolitica W22703 upon subcutaneous injection, and from these data, we determined a LD50 for this strain of approximately 2 x 104 cells. The paper is cited in our manuscript. The 10E05 dose was selected due to our preliminary work and the reproducibility of the experimental phenotypes.

• 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. Use of lysis the reporter - discuss commonalties of the in host transcriptome with other Yersinia Galleria systems eg Paulson etc al (refer below). Are there any thoughts on the host range of this Yersinia and can this be placed in a pathogen host evolutionary context?

Answer: Paulson et al. are now cited twice in the text. The host range of Yersinia enterocolitica has not been investigated to our knowledge. However, its nematocidal activity has been described by Spanier et al., and Manduca sexta larvae, the tobacco hornworm, is also killed by W22703 (see references). Moreover, there are two copies of tccC in the genome of strain W22703 encoding the cytotoxic Tc subunit with its hypervariable C-terminus that is assumed to contribute to host specificity. This is discussed in very detail by Song et al. (see references).

Evolution: Yes, this has been addressed by Waterfield et al. 2004 (see references) where insects are hypothesized as a source of emerging pathogens. We placed our findings in the context of this article in lines 91-94 and 305-310.

• 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. Yes

• Are the data and the methods presented in such a way that they can be reproduced? yes but I think some vector construction methodology is missing e.g. ::rfp (refer above)

Answer: The plasmids used to construct the two strains W22703 tcaA::rfp and W22703 PHE::rfp are listed in Table S2. References for details are given (Starke et. al., 2013, Starke and Fuchs, 2014). Briefly, we used a suicide vector (pUTs) carrying the gene encoding the red fluorescent protein (RFP). This vector replicates in E. coli helper strains such as SM10, but not in Y. enterocolitica. Strain SM10 is now listed in Table 2. Following conjugation, the construct is chromosomally inserted upon recombination via the fragments cloned into the plasmid. In case of tcaA, we cloned the 3´-end of the gene to generate a translational fusion, and in case of HE its promoter, resulting in a transcriptional fusion with the reporter RFP.

Fig 2 I am a little lost mortality seems quick on day 0 is this a result of aberrant injection damage mortality or are the authors observing a different effect across mutants through the initial 24 hours? If data available could this time plot be extended out 0-24 hours. The dash used for W222703 tcaA /TccC look similar can a different symbol be used.

Answer: The reviewer is right that the mortality is high on the first day. However, larvae monitoring for up to nine days is a standard in the literature. No data are available for a better resolution of the first 24 h that, however, were investigated in more detail in the time course of Fig. 5. Moreover, we observed changes in motility and colouring of some of the larvae from one h p.i. on (data not shown). Aberrant injection damage was avoided, and damaged larvae or larvae that not completely took up the infection solution were not further considered in the experiment. This is mentioned in lines 107-109.

A different symbol is now used for W222703 DtccC /pBAD-tccC.

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

Minor comments: - Specific experimental issues that are easily addressable. - Are prior studies referenced appropriately? Other entomopathogenic transcriptome studies could be compared to and or cross referenced (I have provided references in the response

Answer: Repetition of our answer above: We again carefully screened PubMed for studies in the field and added few papers. However, in vivo transcriptome analyses are still rare, as indicated by a lack of a respective investigations with the highly relevant entomopathogen Photorhabdus luminescens. The literature suggested by the reviewer is now cited in the introduction and the discussion (see below for details).

I am unsure on the use of immuno pulldown and efficiency of recovering the Yersinia using this method as opposed to direct sequencing total RNA has this method been used in other systems,

Answer: Isolating RNA from in vivo probes of infected insects encounters two challenges: first, a possible contamination with commensal bacteria, and a too high amount of host RNA that reduces the number of sequence reads. This might be the reason for the relatively low sequence depth found in related papers in the field of in vivo transcriptomics. We overcame these problems by immunomagnetic separation that is easily applicable and enriches the samples with respect to Yersinia cells, this is now mentioned in the results. We also cite a study (Prax et al., in which we established the protocol of IMS.

• Are the text and figures clear and accurate? Yes though in places better naming of insect components could be listed

Answer: This was done, see above.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

As listed above potential use of reporters and or comparison and transcriptome analysis to other systems and an evolutionary pathogen host context (refer comments above) would strengthen the manuscript

Answer: Please see answer to comments above. We explained the use of the reporter fusions, and put the transcriptome analysis into the context of related studies.

Minor comments as per below When first mentioned good to state the larval instar used

Answer: We used larvae of instar 5-6 according to Jorjao et al. (2018), this is now mentioned and cited in the M&M section, line 434.

l 78 lon protease? what type? this is an important SOS protease affecting many regulatory systems please clarify

Answer: This is a Lon A endopeptidase, and its function for the temperature-dependent activity of the lysis cassette has ben described (Springer et al. 2021, see references). Its relevance for the thermodependent regulation of Yersinia virulence has been documented by Herbst et al. (PMID: 19468295) and Jackson et al. (https://doi.org/10.1111/j.1365-2958.2004.04353.x).

l103-113 an description of the elemental tract which is depicted, perhaps this could be placed in the Fig. 1 figure legend

Answer: We agree and substantially shortened the first paragraph of the results. Relevant aspects are now mentioned in Figure legend 2, redundancies with the figure legend were removed.

l 133 use of the word larvae in place of the word animals might be more appropriate

Answer: This was corrected accordingly.

l 133 clarify delta HE mutant description when first mentioned

Answer: The abbreviation HE is now introduced in the introduction in line 74.

Lines 220-234 hard to follow mainly as I am unsure how then strains are constructed, perhaps clarify what rfp is how was it made :: demotes and insertion but yet then they seek to detect TcaA? I could not find the methodology on its or HE::rfp construction

Answer: The plasmids used to construct the two strains W22703 tcaA::rfp and W22703 PHE::rfp are listed in Table S2. References for details is given (Starke et. Al., 2013, Starke et al. 2014). Briefly, we used a suicide vector (pUTs) carrying the gene encoding the red fluorescent protein (RFP). Following conjugation, the construct is chromosomally inserted upon recombination via the fragments cloned into the plasmid. In case of tcaA, we cloned the 3´-end of the gene to generate a translational fusion, and in case of HE its promoter, resulting in a transcriptional fusion with the reporter RFP.

Please see above why we used RFP-antibodies to detect TcaA.

l247 immuno-magnetic separation to isolate Yersinia - is there an efficiency behind this method, might be good to mention (I am unfamiliar with this technique)

Answer: We here repeat our answer to the point above: Isolating RNA from in vivo probes of infected insects encounters two challenges: first, a possible contamination with commensal bacteria, and a too high amount of host RNA that reduces the number of sequence reads. This might be the reason for the relatively low sequence depth found in related papers in the field of in vivo transcriptomics. We overcame these problems by immunomagnetic separation that is easily applicable and enriches the samples with respect to Yersinia cells, this is now mentioned in the results. We also cite a study (Prax et al., in which we established the protocol of IMS.

l313 alludes to role of Tca in hemoceol which contradicts an earlier statements in l 130 please clarify

Answer: The reviewer is right. The sentence in former line 130 (now lines 123-124) was corrected to “…suggesting that the Tc plays a main role in the initial phases of infection”. This statement does not exclude its activity towards hemocytes. Moreover, subcutaneous infection is very artificial and was therefore replaced by oral application in our study to mimic natural routes of infection. This is now elaborated in more detail in the discussion (Lines 305-310).

For clarity table 1 could colour highlight (different colours) tc and lysis genes

Answer: We now added a table to Fig. S1 that shows the FC values of all genes from Tc-PAIYe.

CROSS-CONSULTATION COMMENTS I am in agreement with all points of reviewer 1 who has a clear understanding on Tc toxin composition TcA pentamer etc. Being familiar to the field I regret I did not pick up on these errors

Answer: This has been corrected according to R1.

Point 13 agree and should possibly bring in other researchers who have used Galleria as a model. It also needs to be kept in mind that the target host for many Tcs has yet to be determined hence the importance of oral activity of this isolate

Answer: This has been corrected according to R1.

I am similarly in agreement with comments of reviewer 3

Reviewer 4 I over looked the LT50 data -- apologies but agree with reviewer 1 where WT should be the more potent strain --I still think if possible LD50 for WT would be of value more so to define its oral activity

Answer: We repeat our answer from above. This is an interesting point. The LD50 (dose of cells that kills 50% of all larvae) is usually not calculated in publications in this field of research, because its calculation requires a very huge separate data set that cannot be used to answer the questions addressed here. Such a dat set is not available. We published the dose-dependent toxicity of Y.enterocolitica W22703 upon subcutaneous injection, and from these data, we determined a LD50 for this strain of approximately 2 x 104 cells. The paper is cited in our manuscript. The 10E05 dose was selected due to our preliminary work and the reproducibility of the experimental phenotypes.

Reviewer #4 (Significance (Required)):

SECTION B - Significance ========================

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Extends from work of Fuchs - research group Extends from work of Palmer et al on lysis cassettes as potential T10SS Extends from work off Vesga Pseudomonas and Paulson Yersinia(refs provided below) on insect transcriptomics

Of interest and possibly understated is the oral activity of enterocolitica in the insect host as mentioned L316-317 and how this might relate to the lifestyle/evolution of this microbe further elaboration here would be of interest

Answer: We agree that this is an important aspect. Therefore, we added the following sentences here: “In contrast to subcutaneous injection in the use of insect larvae as model for bacterial virulence properties towards mammals, oral application mimics natural routes of infection that in particular take place during the bioconversion of animal cadavers by bacteria, fungi, and larvae {Carter, 2007 #879}. Together with the broad cytocidal host spectrum of bacterial toxins {Mendoza-Almanza, 2020 #880}, investigation of yet neglected natural infections of invertebrates will contribute to a better understanding of microbial pathogenicity {Waterfield, 2004 #480}.” (lines 305-310)

• Place the work in the context of the existing literature (provide references, where appropriate).

Relevant Transcriptome papers which could be referred to in the discussion i.e. are similar genes in play or is their a point of difference? https://doi.org/10.1093/g3journal/jkaa024;https://doi.org/10.1038/s41396-020-0729-9; https://doi.org/10.1099/mic.0.000311

Answer: Paulson et al. mainly address virulence factors, whereas metabolism is not uncovered. We now cite similarities with respect to hemolysis and iron scavenging. The focus of Vesga et al. is on the interaction of a plant pathogen with wheat and two insect hosts, including their transcriptome. Although metabolic details are missing, there is an interesting overlap with the paper by Vesga et al. (hemocoel as permissive environment for proliferation) and a difference (upregulation of chitinases was not observed) that are now cited in the discussion. The Alenzi paper mainly investigated the general virulence of Y. enterocolitica strain. We cite its finding on the importance of motility, thus confirming our transcriptome analysis.

• State what audience might be interested in and influenced by the reported findings. The oral activity of enterocolitica towards Galleria of interest and an evolutionary context insect vs mammalian activity in the discussion could be provided. Potential role of TcaA in gut association For the targeted journal I feel additional technical data is required and a broader context to other global systems (bacterial species) provided

Answer: All points were addressed carefully and in detail. We refer to our answers to points detailed above.

• 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. Reviewers expertise entomopathogens, their toxins and pathogen ecology

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Referee #4

Evidence, reproducibility and clarity

Summary:

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

Outlines proposed role of lysis cassette in oral infection of Galleria as a model insect for host pathogen interaction, data which is fortified through use of histology and RNAseq. Introduction could extend to additional background eg Aleniz et al and other entomopathogen transcriptome data, more so other studies using Yersinia and Galleria as a model (refer references provided in the below comments) The strength of the paper lies in understanding the progression of the disease in the insect host as mentioned L316-317 and clearance of the bacteria via in TcaA mutant

Major comments:

• Are the key conclusions convincing?

Yes for mode of action

Fig 5 could have additional panels -this is a strength of the paper

Fig 6 legend could better describe the observed insect components

Figure 7 may be lost in PDF conversion -the figure appears un resolved? are there more high resolution photos - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

the data provided is in places rudimentary (i.e. validation of the role of the lysis cassette in virulence) and could be bolstered with the construction and use of a lysis translational reporter etc I was left unsure how the HE::rfp and TcA::rfp constructs were made. I had assumed red florescent protein however it appears an antibody is used. This needs to be clarified as I then found it hard to interpret the results. It appear l114-125 that their may be enough data to derive a LD50 values and or LT value at a fixed dose - if so reporting this data of interest. It may also allude as to why a 10e5 dose was selected for subsequent expts - 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.

Use of lysis the reporter - discuss commonalties of the in host transcriptome with other Yersinia Galleria systems eg Paulson etc al (refer below). Are there any thoughts on the host range of this Yersinia and can this be placed in a pathogen host evolutionary context? - 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.

Yes

• Are the data and the methods presented in such a way that they can be reproduced? yes but I think some vector construction methodology is missing e.g. ::rfp (refer above)

Fig 2 I am a little lost mortality seems quick on day 0 is this a result of aberrant injection damage mortality or are the authors observing a different effect across mutants through the initial 24 hours? If data available could this time plot be extended out 0-24 hours. The dash used for W222703 tcaA /TccC look similar can a different symbol be used. - Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.
• Are prior studies referenced appropriately?

Other entomopathogenic transcriptome studies could be compared to and or cross referenced (I have provided references in the response

I am unsure on the use of immuno pulldown and efficiency of recovering the Yersinia using this method as opposed to direct sequencing total RNA has this method been used in other systems,<br /> - Are the text and figures clear and accurate?

Yes though in places better naming of insect components could be listed - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

as listed above potential use of reporters and or comparison and transcriptome analysis to other systems and an evolutionary pathogen host context (refer comments above) would strengthen the manuscript

Minor comments as per below

When first mentioned good to state the larval instar used l 78 lon protease? what type? this is an important SOS protease affecting many regulatory systems please clarify

l103-113 an description of the elemental tract which is depicted, perhaps this could be placed in the Fig. 1 figure legend

l 133 use of the word larvae in place of the word animals might be more appropriate

l 133 clarify delta HE mutant description when first mentioned

Lines 220-234 hard to follow mainly as I am unsure how then strains are constructed, perhaps clarify what rfp is how was it made :: demotes and insertion but yet then they seek to detect TcaA? I could not find the methodology on its or HE::rfp construction

l247 immuno-magnetic separation to isolate Yersinia - is there an efficiency behind this method, might be good to mention (I am unfamiliar with this technique)

l313 alludes to role of Tca in hemoceol which contradicts an earlier statements in l 130 please clarify

For clarity table 1 could colour highlight (different colours) tc and lysis genes

Referees cross-commenting

I am in agreement with all points of reviewer 1 who has a clear understanding on Tc toxin composition TcA pentamer etc. Being familiar to the field I regret I did not pick up on these errors

Point 13 agree and should possibly bring in other researchers who have used Galleria as a model. It also needs to be kept in mind that the target host for many Tcs has yet to be determined hence the importance of oral activity of this isolate

I am similarly in agreement with comments of reviewer 3

Reviewer 4 I over looked the LT50 data -- apologies but agree with reviewer 1 where WT should be the more potent strain --I still think if possible LD50 for WT would be of value more so to define its oral activity

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Extends from work of Fuchs - research group

Extends from work of Palmer et al on lysis cassettes as potential T10SS

Extends from work off Vesga Pseudomonas and Paulson Yersinia(refs provided below) on insect transcriptomics

Of interest and possibly understated is the oral activity of enterocolitica in the insect host as mentioned L316-317 and how this might relate to the lifestyle/evolution of this microbe further elaboration here would be of interest - Place the work in the context of the existing literature (provide references, where appropriate).

Relevant Transcriptome papers which could be referred to in the discussion i.e. are similar genes in play or is their a point of difference?

Amber R Paulson, Maureen O'Callaghan, Xue-Xian Zhang, Paul B Rainey, Mark R H Hurst, In vivo transcriptome analysis provides insights into host-dependent expression of virulence factors by Yersinia entomophaga MH96, during infection of Galleria mellonella, G3 Genes|Genomes|Genetics, Volume 11, Issue 1, January 2021, jkaa024, https://doi.org/10.1093/g3journal/jkaa024

Vesga, P., Flury, P., Vacheron, J. et al. Transcriptome plasticity underlying plant root colonization and insect invasion by Pseudomonas protegens. ISME J 14, 2766-2782 (2020). https://doi.org/10.1038/s41396-020-0729-9

Dhahi Alenizi, Tamara Ringwood, Alya Redhwan, Bouchra Bouraha, Brendan W. Wren, Michael Prentice, Alan McNally (2016) All Yersinia enterocolitica are pathogenic: virulence of phylogroup 1 Y. enterocolitica in a Galleria mellonella infection model https://doi.org/10.1099/mic.0.000311 - State what audience might be interested in and influenced by the reported findings.

The oral activity of enterocolitica towards Galleria of interest and an evolutionary context insect vs mammalian activity in the discussion could be provided. Potential role of TcaA in gut association

For the targeted journal I feel additional technical data is required and a broader context to other global systems (bacterial species) provided - 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.

Reviewers expertise entomopathogens, their toxins and pathogen ecology

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors analyze the phases of infection of Galleria mellonella by Yersinia enterocolitica following forced oral feeding. They study different phases of infection, including survival within the gut and invasion of the hemolymph. By analyzing differences in the genes up- and down regulated, they show that for example transporters for food sources from the hemocoel are regulated for making those sources available for the bacteria.

Major comments:

This is an interesting paper demonstrating genes of Y. enterocolitica dependent for colonization, growth and crossing of the epithelial gut barrier in G. mellonella.

Major points which have to be addressed: Introduction: line 54: the BC subcomplex is not released into the cytosol! It is only the hypervariable region (enzymatic part) which enters the cytosol. This has to be corrected.

Fig.2/3: Why have different CFU been used for the distinct bacterial strains? This does not allow a direct comparison of their toxicity. For me the dead larvae shown in Fig. 3 are not represented in Fig 2 (data are not concordant), because of the loss before day one depicted in Fig. 2: The curves should be normalized to the same starting point (should be 100 %)? Fig. 3: Why is the strain W22703 delta tccC/pBAD - tccC missing in the data set? Minor: line 221: "the" is doubled

Significance

The manuscript shows the use of G. mellonella as a straight foreward method to study gene functions of pathogenic bacteria, a significant knowledge for scientists of the field.

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Referee #2

Evidence, reproducibility and clarity

This is a very, very nice study as it actually describes the role of different Tc toxin components in a model infection system using an important bacterium- really for the first time in a properly controlled manner. The mutants lacking either the syringe (AB) or the bullet (C) make 'sense' for a loss of function perspective. The description of the phage cassette in loss of function is also interesting and could do with some more speculation?

For example, some groups of Photorhabdus bacteria release their oral toxicity (Tc's) into their bacterial supernatants- whereas in others it remains cell associated. The likely role of this phage cassette in this process should be discussed (is cell suicide required for release?).

Significance

This is highly significant finding as despite all of the very elegant structural studies done on these important toxins there is still very little work in vivo. These studies clearly show the role of the different components of these ABC toxins in vivo. It should be published with priority.

Congratulations to the authors.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript Saenger et al. concentrate on the pathophysiological details of insect larvae infection by Yersinia enterocolitica. The authors studied the colonisation, proliferation, tissue invasion, and killing activity of the bacteria in Galleria mellonella larvae. Their study provides valuable evidence for the biological relevance of Tc toxins and a neighboring holin-endolysin cassette during establishment of Y. enterocolitica infection in Galleria mellonella larvae through the oral route. The findings of the authors provide important novel insights, that can be used for the development of Tc toxins as biopesticides.

In general, this is a nice study. The data and the methods are presented well so that they can be reproduced and the key conclusions convincing.

Unfortunately, the manuscript is sloppily written in some places, including grammatical and formatting errors. Citations regarding the structure and mechanism of action of Tc toxins are arbitrarily chosen, often taking the wrong ones and important aspects are left out. I highly recommend that the authors read the review of Roderer and Raunser 2019 that nicely describes and summarizes the molecular mechanism of Tc toxins. The abstract ends with a speculation: "Suggesting that this dual lysis cassette is an example for a phage-related function that has been adapted for the release of a bacterial toxin" - this is likely true, but not proven in this work. What if it is used for the release of something else like extracellular DNA needed for biofilm formation (see https://doi.org/10.1038/ncomms11220)?

In addition to that, several outstanding issues must be addressed:

1. Line 45 3-D structural analysis of the tripartite Tc suggests a 4:1:1 stoichiometry of the A, B and C subunits, with the A subunit forming a cage-like pentamer that associates with a tightly bound 1:1 sub-complex of B and C. This is wrong. The stoichiometry is 5:1:1 and the structure is not a cage. The statement was taken from citation 3. However, citation 3 should not be used, since the stoichiometry as well as the structure that was determined there is wrong. Use Landsberg et al. 2012 PNAS, Gatsogiannis et al. 2013 Nature instead.
2. "Few bacteria are known to successfully colonize and infect invertebrates" - needs a reference.
3. "Their oral insecticidal activity is comparable to that of the Bacillus thuringiensis- (Bt)- toxin" - reference missing.
4. "Type a, type b and type c" subunits is not usual for the literature. Please use TcA, TcB, TcC. A-, B-, and C-components should be abbreviated as TcA, TcB and TcC respectively in order to be in line with recent literature on the topic.
5. Is TccC an ADP-ribosyltransferase or does it have a different biochemical activity?
6. "The toxic and highly variable carboxyl-terminus of TccC that has recently been demonstrated to ADP-ribosylate actin and Rho-GTPases" - this is only certain for TccC3 and TccC5 from P. luminescens. There are many such C-termini, called HVRs which have not had their activities determined yet, see here: https://doi.org/10.1371/journal.ppat.1009102
7. "is probably followed by receptor-mediated endocytosis" - more recent references exist for the receptor binding of Tc toxins.
8. "A pH decrease then triggers the injection of a translocation channel formed by the pentameric TcaA subunits into the endosomal vacuole, followed by the subsequent release of the BC subcomplex into the cytosol of the target cell" - this again is incorrect. Please read the above mentioned review and correct this passage accordingly.
9. What is meant by "environmental Yersinia species"?
10. In the relevant W22703 pathogenicity island sequence (https://www.ncbi.nlm.nih.gov/nuccore/AJ920332) previously submitted by the same group, something odd is going on with the TcA component: it appears to be split into three polypeptides (tcaA, tcaB1, tcaB2). In the manuscript you state TcA is made up from only tcaA and tcaB. Could you please address this?
11. "And their products were recently shown to act as a holin and an endolysin, respectively" - missing reference.
12. "Its Tc proteins are produced at environmental temperatures, but silenced at 37{degree sign}C." versus "Remarkably, HolY and ElyY lyse Y. enterocolitica at body temperature, but not at 15{degree sign}C". Please address the issue that HolY/ElyY lyse the bacteria at temperatures where Tc proteins are not produced.
13. "Nematodes, which are easily maintained in the laboratory without raising ethical issues, have successfully been used to identify virulence-related genes in a broad set of bacterial pathogens" - what is the relevance of this for the current manuscript?
14. Fig. 1C - no description is given for the labels 1-8.
15. "The hemolymph of these cadavers was found full of Y. enterocolitica cells" - injected CFUs are provided here, but not final CFUs in the cadavers (although referred to in a later section). Please address this.
16. What is the inducing agent used for pACYC-tcaA and pACYC-HE? Why would "slight leakiness of the pBAD-promoter" make pBAD-tccC non-inducible? Were colonies taken from the cadavers to verify that the bacteria still contained these plasmids?
17. Can the authors please address the TD50 of 1.83 days for W22703 ΔHE/pACYC-HE versus 3.67 days for WT bacteria? This would mean that the former kill larvae twice as fast as usual. I would not call this "did not significantly differ in their insecticidal activity".
18. Fig. 2 is missing survival data for larvae infected with tcaA, HE, and tccC KO bacteria.
19. "And a slight colouring of some of the larvae from one h p.i. on (data not shown)" - best show the data or remove this statement.
20. The infection of larvae by W22703 ΔtccC/pBAD-tccC is missing, the other bacterial variants are present. Please address this.
21. "initially proliferated from an application dose of 4.0 × 105 CFU and 4.0 × 105 CFU, respectively, to 2.2 × 106 CFU and 2.8 × 106 CFU, but could not be detected from day three on. This finding strongly suggests that TcaA is involved in adherence to epithelial cells and thus in midgut colonization". Please address the "initially proliferated" (which day post-infection?), their elimination from the larvae (how, why?), why the tccC KO bacteria were more virulent than tcaA KO bacteria, and where the suggestion about TcaA involvement specifically in adherence comes from.
22. In Fig. 4, the CFUs for W22703 ΔtccC/pBAD-tccC are essentially the same as for the other rescued KOs and WT, while in the text a point about weaker growth is made. Is this justified? Also, even though the CFU data is present here, data on infection of larvae by W22703 ΔtccC/pBAD-tccC is missing unlike the other bacterial variants. Please explain.
23. Fig. 6b - The presence of an anti-RFP signal is not obvious in any of the bottom row images. The top row images are missing the same kind of annotation provided for Fig. 6a, without which non-histologists will find understanding the figure difficult.
24. "In the absence of the lysis cassette, however, TcaA::Rfp was not detected despite the presence of W22703 ΔHE tcaA::rfp cells." + "To test whether or not the promoter of the lysis cassette is active in vivo, we infected G. mellonella larvae with strain W22703 PHE::rfp. Although Y. enterocolitica cells densely proliferated within the hemolymph (FIG. 6B), no staining signal that would point to the presence of TcaA was obtained, possibly due to no or weak PHE activity." Does this mean that without HE, tcaA does not express?
25. "These data suggest that the HE cassette is responsible for the extracellular activity of the insecticidal Tc." Please explain how the preceding paragraph leads to this conclusion.
26. "As expected, bacterial cells, e.g. Y. enterocolitica, are visible in the hemolymph obtained from W22703-infected animals, but not in all other preparations." - which figure are the authors referring to?
27. "To delineate the transcriptional profile of Y. enterocolitica during infection of G. mellonella, we applied immunomagnetic separation to isolate Y. enterocolitica from the larvae 12 h and 24 h after infection" - do the authors store the bacteria for up to 24 h at 4 {degree sign}C, as indicated in the methods section?
28. "The endolysin located within Tc-PAIYe was significantly up-regulated after 24 h, but not after 12 h, pointing to its possible role in the release of the Tc" - I could not find the endolysin in Table S1. Could the authors mark it clearly? Also, why is the holin also not upregulated?
29. "This is in line with the fact that a T3SS is lacking in strain W22703" - Is a complete genomic sequence available for this strain, so readers could validate this statement?

Significance

See above

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Reply to the reviewers

We thank the both the reviewers for their constructive comments. Please see our point-by-point response to all the comments.

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

• 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. *__Reviewer comment: __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: *
2. Hui et al., (Nature, 2022) doi: https://doi.org/10.1038/s41586-022-04479-6*
3. Peacock et al., (bioRxiv) doi: https://doi.org/10.1101/2021.12.31.474653*
4. Lamers et al., (bioRxiv) doi: https://doi.org/10.1101/2022.01.19.476898 * Response: Previous reports including the citations indicated by the reviewer have shown that the Omicron variant replicates at a lower levels in lung tissue as compared to cells of bronchial origin or upper respiratory tract. In fact, Omicron variant was shown not to productively infect at all in alveolar type II cells. Omicron replication was severely compromised in Calu-3 cells grown in 96-well plates (https://doi.org/10.1080/22221751.2021.2023329) which is consistent with our observations.

*__Reviewer comment: __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. *

Response: Cells were grown in plastic multi-well plates for growth curve experiments shown in Figure 3. The cells in this condition are not polarized and the virus titers are the total amount of virus released into the culture supernatant. The infection conditions in Figure 5 is under air-liquid culture conditions, from polarized cells. Therefore, the virus titers are only from the basolateral chamber. The outcomes of figure 3 and figure 5 are not comparable due to these technical differences. We will add this explanation in the results section.

*__Reviewer comment: __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). *

Response: We performed confocal imaging of transwells from air-liquid interface model using a 20X objective and have obtained data to show that the percent of infected cells is similar between Omicron and Delta variant. We will include this data in the revised manuscript. In an in vitro system, once the infection is set in, the infected cells eventually die and the TEER reaches background levels. We are proposing a delay in disruption of barrier integrity most probably due to lower cytopathogenicity of the Omicron variant. As per the reviewer’s suggestion, we will discuss the possible limitation of the models and provide additional interpretations.

Minor comments *A) __Reviewer comment: __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..." *

Response: We will correct this.

*__B) Reviewer comment: __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. *

Response: We agree with the reviewer’s argument. Please note that the two vaccines used in India are against the ancestral virus (inactivated) or the spike protein expressed by the adenovirus vector backbone. As over 90% of the population in India have been fully vaccinated with these two vaccines and a majority of them may also have been infected with delta variant and now with omicron, it is practically impossible to compare primary delta cases vs primary omicron cases at this stage. As part of another study in mid 2021, after the second wave of COVID-19 infections due to the Delta variant in India, we randomly selected 55 samples which had a detectable FRNT50 value for the delta variant, to test for their ability to neutralize the Omicron variant. Only twenty of the 55 samples had detectable levels of neutralizing antibodies against the Omicron variant. By assigning a FRNT50 value of 10 for the samples which had no detectable levels of antibodies in the starting dilution (1:20) of the assay, we obtained a GMT of 22.5 (95% CI: 16, 31) for these 55 samples. This value was 20-fold lower than the GMT of Delta variant which was 404 (95% CI:248, 658). This clearly indicates that even during the peak of delta wave, there were barely any cross-reactive antibodies to the Omicron variant. This study was recently published [NATURE COMMUNICATIONS | https://doi.org/10.1038/s41467-022-31170-1]. It would be interesting to eventually compare the antibody responses in reinfections with other sub-lineages of Omicron variant which is beyond the scope of our manuscript. We will add this description in the results and discussion section of the revised manuscript.

*C) __Reviewer comment: __There appears to be no reference to Figure 6G, however this reference is most likely missing from line 306. *

Response: Thank you for bringing this to our notice. We will insert the reference to Figure 6G.

*D) __Reviewer comment: __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. *

Response: Please note that nine out of 15 samples had FRNT50 value above the level of detection after vaccination in June 2021. The number of samples positive for Omicron antibodies reduced to six out of 15 by Dec 2021 suggesting that relatively more people were without protective antibodies for Omicron variant by Dec 2021. Around 70% of the population was seropositive by Aug 2021 (https://doi.org/10.1016/j.ijid.2021.12.353) and most adults in India received both doses of their vaccine after June 2021 which would have boosted the humoral and cellular response to SARS-CoV-2. This is corroborated in a recently published report, where we showed that 36 out of 55 previously infected subjects had neutralizing antibodies for the Omicron variant after receiving a single dose of inactivated vaccine. Therefore, in the context of hybrid immunity in India, we speculate that waning antibody titers could have played a significant role in the emergence and spread of Omicron variant in addition to the ability of the Omicron variant to escape neutralization, replicate more efficiently in the upper respiratory tract etc., The fact that booster doses of vaccines developed against the ancestral virus/viral protein was capable of increasing the level of neutralizing antibodies to omicron variant suggests that the level of antibodies above a certain threshold may play a significant role in protecting against the omicron variant.

Reviewer #1 (Significance (Required)):

• __Reviewer comment: __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. *

Response: The study was conducted in the months of Jan-March 2022 and the first version of the results were uploaded on a preprint server in March 2022. The process of journals handling the manuscript and obtaining reviews is not under our control. We cannot argue to defend the comments on novelty when the Omicron variant is barely six months old and new variants continue to emerge. The deluge of publications should not result in reviewers branding most of the efforts as not novel or insignificant. We have been trying since three months to obtain primary cells but the distributors are unable to supply the same. We will continue to try to obtain cells from one or the other source. Transwells are back-ordered with expected delivery dates in three months. Meanwhile, we now have HBEC3-KT cells which are normal human bronchial epithelial cells immortalized with CDK4 and hTERT. We will perform the inhibition experiments in these cell lines to convince the reviewers.

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

*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. *

• __Reviewer comment: __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)? *

Response: We thank the reviewer for the comments. Over 90% of the population in India is vaccinated. All the participants of the study have been vaccinated in 2021. The participants were enrolled into the study almost 4 weeks after recovery from illness. We have enrolled participants who have reported to have had fever or COVID-19-like symptoms in the preceding weeks with or without confirmed RT-PCR test results. Testing is an individual and voluntary choice now. Therefore, it would be difficult to find RT-PCR confirmed cases. Our assumption about exposure is based on a nationwide sequencing effort of thousands of samples every week and this approach is reliable and credible. As indicated in the text and in the supplementary figure, Omicron lineages BA.1 followed by BA.2 were the circulating virus lineages since Jan 2021 in India.

*__Reviewer comment: __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. *

Response: Please note that the B.1.1.529 which was used at the beginning of the study is the BA.1 sub-lineage which has been compared with Kappa and Delta variants. BA.2 emerged at later stages and therefore we have compared the kinetics and neutralization titer between BA.1 and BA.2. It is unreasonable to expect to repeat all the comparisons with BA.2 considering the cost and challenges of working in a BSL-3 environment. The initial version of this data was uploaded on preprint server in March 2022 when only two sub-lineages of Omicron namely BA.1 and BA.2 existed. Our data from the national SARS-CoV-2 sequencing consortium clearly shows that there were no other sub-lineages circulating at that time.

Reviewer #2 (Significance (Required)):

*__Reviewer comment: __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. *

Response: We will revise the conclusions and claims of the paper as per the suggestions. Please see our response to reviewer 1 with regards to the novelty of our observations. The B.1.1.529 variant was later classified as the BA.1 variant. Our study was uploaded on the preprint server in March 2022 and the entire review process has taken four months. It is unfair to now demand comparison of BA.2 with Kappa or Delta variant which does not add any additional value to our observations.

*__Reviewer comment: __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. *

Response: Please see our comments above. Our efforts are continuing in this direction to further look at antibody responses and replication kinetics of newer variants which have emerged recently. However, the scarcity of positive clinical samples and lower probability of getting samples that would be suitable for virus isolation are the challenges we are dealing with. We think testing newer variants which have emerged during the review process is certainly valuable but is extremely difficult under the current circumstances. We will have to apply to seek import permits to obtain these sub-lineages or enrol patients with symptoms and keep testing them to isolate, culture the virus and obtain whole genome sequence. We will have to establish neutralization assays with newer sub-variants to test in parallel with other Omicron lineages. All this is beyond the scope of our manuscript and will take few months of paper work and experimentation.

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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.

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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.

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Reply to the reviewers

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

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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.

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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.

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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

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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.

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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.

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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.

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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.

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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

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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.

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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

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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.

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Reply to the reviewers

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

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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.

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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

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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.

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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).

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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.

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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.

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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.

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Reply to the reviewers

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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

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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

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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.

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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.

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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

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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.

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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.

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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.

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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.

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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

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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.

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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.

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

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SUMMARY:____

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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).

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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.

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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)):____

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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.

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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)):

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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)):

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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.

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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:

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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.

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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.

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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.

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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.

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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.

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