Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

This manuscript is in revision at eLife.

Summary:

The manuscript addresses a fundamental problem: the organisation of epithelial polarity determinants at the apical domain of human epithelial cells. Mangeol et al investigate this question using super-resolution microscopy approaches (STED) in polarised intestinal epithelial cells. Using immunofluorescence labeling of endogenous proteins, they provide a careful characterization of Par3-Par6-aPKC and Patj-Pals1-Crb3a localization relative to tight junctions. They find that each protein localizes in the near vicinity of the tight junction, in a clustered organization. Through pairwise colocalization analyses, they observe significant separation of polarity proteins that are generally considered to be part of the same molecular complex based on biochemical assays. Specifically, PAR3 is not associated with aPKC or PAR6, and CRB3a colocalizes poorly with all other polarity proteins, raising interesting questions for future analyses.

The imaging performed in this study is skillful and beautifully presented and, achieving an isotropic resolution of about 80nm, is impressive. However, because of this great gain in resolution compared to other studies of similar components, the major concern of all three reviewers is that the process of fixation and immunostaining may introduce artefacts that are causing the segregated dots to appear. Variable antibody quality and insufficient validation of antibody specificity raise additional concerns about the observed patterns of localization.

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Reply to the reviewers

RESPONSE TO REVIEWER #1

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

In this manuscript, Ishihara et al. investigate and compare microtubule polymerization/depolymerization dynamics inside vs. at the periphery of microtubule asters in a cell-free Xenopus egg extract system. By tracking EB comets, which localize to growing microtubule ends, they find that the microtubule growth rates and EB comet lifetimes (interpreted as an indicator of microtubule catastrophe rates) are similar between the two spatially-distinct microtubule populations. However, using a tubulin-intensity-difference image analysis, the authors are also able to measure local microtubule depolymerization rates, and they find a significant difference in depolymerization rates of the two populations. Specifically, the authors report that the microtubule depolymerization rates measured within asters are faster than those measured at the periphery.

\*Specific comments:***

Figure 2.

In the text, the authors report: "The depolymerization rate was 36.3 {plus minus} 7.9 μm/min (mean, std) in the aster interior, compared to 29.2 {plus minus} 8.9 μm/min (mean, std) at the aster periphery." This difference is certainly not two-fold (as stated in the abstract). It would also be useful to mark the mean rates on the graph in 2B.

We removed the words ‘almost two-fold’ in the abstract. In the revision, we will mark the mean rates on Fig. 2B (using vertical lines).

The bimodal shape of the depolymerization rate distributions in 2B is very interesting. This definitely warrants further investigation. At the minimum, the depolymerization rates should be determined at 50 um- intervals, as done for other parameters in Figure 1. Could it be that there are two coexisting populations of microtubules at the same location? Or is there a clear spatial compartmentalization of the two that is not obvious here because of the too large of a distance interval used for the measurements. This is a very important distinction for the claims of the paper.

We understand the reviewer’s concern. There are some technical limitations that make the depolymerization measurement more challenging. While we use widefield imaging of EB1-GFP comets to obtain polymerization rates from a field of view spanning 500 microns, we may only use TIRF imaging for depolymerization measurements. In this method, we are limited to observing microtubules very close to the cover slip in a small field of view of 80x80 microns at 500 ms time intervals (movies span 1-2 minutes). One would need to move the TIRF field every 1-2 minutes at 50 micron intervals, but the aster periphery would be changing during this time, so the exact location of the measurement is hard to define. Thus, we opted to image the two spatial extremes: interior (close to the MTOCs) and the very periphery (where MT density is still sparse.)

Perhaps, the largest limitation of this approach is the choice of peripheral regions based on the apparent sparsity of MTs in the TIRF field of view. Indeed, when we examine the depolymerization rate distributions for individual movies separately (see figure below, periphery #1-3 are three individual movies), we observe that some movies have rates as low as 20 µm/min, while others have higher values with a center around 36 µm/min. The depolymerization rates for the interior also vary from the mean values of 34.8-43.2 µm/min (interior #1-3 are three individual movies). In general, the spread of depolymerization rate within a field of view as well as across different fields of view is much larger than for polymerization. It is possible that this is partly explained by the lack of precise definition of interior vs. periphery in this TIRF-based measurement approach.

Our data still supports the spatial regulation of depolymerization rate. However, there is no clear evidence for a bimodal distribution of depolymerization rate in any given field of view (80x80 micron square region). To clarify this point, we have removed the language “bimodal” in the main text. In the revisions, we will provide this figure as a supplement.

We thank the critical feedback from reviewer #1 and #2 that allowed us to clarify this issue of apparent bimodality of the depolymerization rates.

The authors make a point here that the distribution of measured polymerization rates is fairly narrow. This appears to be in contrast with Figure 1B, where polymerization rates take on a wide range of values. How do the two distributions of polymerization rates obtained by these two methods compare?

To address this point, we directly compare the standard deviation of the polymerization rate measurements. For Fig. 1B EB1 tracking measurements, std ranges from 7.7-10.5 µm/min for a given spatial bin (as stated in Fig. 1B legend), while for Fig. 2A TIRF measurements std is 4.0 (periphery) and 4.5 µm/min (interior) as stated in the main text. Given that the mean values of polymerization rates are similar, this suggests that the TIRF measurements are less noisy. This further highlights the relative pros and cons of the two measurement methods. To discuss these issues, we have added a new paragraph in the discussion section.

Figure 3.

The laser ablation figure and movies are beautiful, but don't seem to add support to the story. Importantly, the authors do not confirm any spatial variability in depolymerization rate with these experiment. As a matter of fact, although the laser ablation experiments are only performed in the aster interior, the measured depolymerization rates appear to be just as consistent with the periphery rates in Figure 2. as they are with the interior rates in Figure 2. (They span quite a large range of values with the average right in the middle between what was measured for the two areas in Figure 2).

Indeed, the values obtained with laser ablation are quite variable, even compared to the physiological depolymerization rate measured via TIRF microscopy. This perhaps reflects the variability of biology as well as the nature of the laser ablation which measures depolymerization rate at the level of microtubule populations. We hope our paper will increase interest in this rarely measured parameter, and perhaps invention of new probes to measure it more accurately and conveniently.

Given the variability of our measurements, we conclude that the results between the TIRF based approach vs. laser ablation based approach of depolymerization rates are indistinguishable. We agree with the reviewer that the data does NOT argue that laser ablation results are more consistent with the interior TIRF measurements than peripheral TIRF measurements.

To clarify this point, we remove the following clause “, which was comparable to the modal value of the depolymerization rates in the aster interior (Fig. 2).”

We change the concluding sentence of our laser ablation paragraph from

“Overall, these observations suggest that depolymerization dynamics are similar for plus ends following a natural catastrophe vs. ablation in the aster interior.”

to

“Overall, these observations confirm that depolymerization rates are variable, and we find no statistical distinction of rates between plus ends following a natural catastrophe vs. ablation.”

Although the authors report they don't see any correlation between the distance and depolymerization rate, they should still plot the rate as a function of initial cut positions (Figures 3D, 3E).

To address this concern, we plan to provide a supplemental figure in the revision. Please see the preliminary figure below. Due to technical limitations with the laser ablation system (field of view for 60x magnification), we only have measurements that span 15-100 microns from the center..

From the single decaying inward wave the authors conclude that microtubules depolymerize fully to their minus ends which are distributed throughout the aster. Can the possibility that depolymerization is stopped by microtubule lattice defects/islands be excluded by these observations?

The existence of microtubule lattice/defects is a recent development in the field and much is not known. If we assume that defects are structurally unstable, we predict that the episode of depolymerization will continue even when reaching a defect. If defects are stable and lead to instantaneous rescue of plus ends, we cannot distinguish the defects from minus ends. In this latter scenario, the interpretation of the decaying inward wave requires caution.

What are the effects of the local increase in tubulin concentration due to the subunit release by depolymerization? What about the release of other lattice-binding MAPs (stabilizers)?

We are interested in these questions as well. Soluble GDP-bound tubulin, released by depolymerization, is thought to exchange its nucleotide to GTP without need of a GEF, and no GEF is known. The dissociation rate of GDP is ~0.1 [1/sec], for a half-life of ~5 sec (Brylawski and Caplow, 1983, J. of Biol. Chem.), so we believe the tubulin subunits are recycled relatively quickly. It is not entirely obvious whether this necessarily results in a significant increase in ‘soluble’ tubulin concentration given tubulin diffusive transport. We hypothesize the main effect of stabilizing MAPs is on the depolymerization rate as discussed in our model in Fig. 5.

Figure 4.

Is the local depletion of tubulin/EB1 thought to be only within the narrow annulus at ~100 um distance, or is it not measurable on the inside due to the polymer signal? Can the two be separated? Such a sharp transition within a discrete annular region doesn't speak to the relative effects on the inside vs. the outside of the aster?!

Yes, we also believe the soluble tubulin levels are even lower in the more inner regions of the aster. However, polymerized tubulin accounts for a large part of the fluorescence intensity in these inner regions, and our method does not faithfully reflect the soluble fraction. It will be important for future studies to employ specific methods that may unequivocally distinguish polymer vs. soluble tubulin concentrations (see below).

More importantly, the local depletion of either tubulin or EB1 is not a good representation of a depletion of a MAP component that associates with the microtubule lattice. Both tubulin and EB1 bind preferably to microtubule ends, not lattice. Thus showing a profile of slight local tubulin and/or EB depletion does not seem to be relevant for the proposed model. Rather, overall microtubule polymer mass/density as a function of distance may be more relevant?

Reviewer #1 makes a valid point that tubulin and EB1 are specifically incorporated to plus ends and not to the entire lattice as we assume for the MAPs in our theoretical model. To address this issue, we analyzed the fluorescence intensity of images obtained for a MAP that associates with the MT lattice, Tau-mCherry (Mooney et al. 2017). This quantification shows a depletion pattern similar to tubulin and EB1. Thus, we believe the local depletion is a general feature. For the revision, we plan to incorporate this Tau-mCherry data in Fig. 4.

Figure 5.

The toy model is intuitive and clear, but not sufficient without any experimental investigation. An attempt to quantify the actual distributions of at least one or a few selected proposed MAPs is needed. Is the depletion strongest where microtubule density is highest? What is the ratio of a MAP intensity to microtubule polymer density as a function of distance? How does that relate to local depolymerization rates? What are other testable model predictions that can show support for the proposed mechanism?

We understand that our proposal is rather speculative, and the goal of this manuscript was to propose a hypothesis that may inspire others working on assembly on intracellular organelles. Although Tau is not an endogenous component of the egg extract system, we believe that our new quantification of Tau-mCherry depletion adds more credibility to our general proposal.

Microtubule density is roughly uniform within the interior of the aster according to our current understanding (Ishihara et al. 2016 eLife). So the MAP:MT ratio is relatively uniform throughout the aster except at the very periphery where there are very few MTs assembled (i.e. “depletion is weakest where MT density is lowest.”)

In the future, we may perform (1) FCS measurements of candidate MAPs to directly measure the concentration profile of the candidate MAP in soluble form and (2) depletion/addback to show which MAP most affects depolymerization rate. Although these experiments are appealing, this requires generation of new molecular reagents as well as calibration of a highly specialized optical method. Therefore, we decided to limit this paper to focus on the unusual observation of the variation of depolymerization rate and speculate the underlying mechanism.

Also, the table is insufficiently described. Are any or all of these MAPs known to be specific regulators of microtubule depolymerization rates, but not other dynamics parameters?

There are a large number of MAPs in Xenopus eggs, as there are in all cells, and the degree to which their effects on microtubules has been characterized is variable. To address this comment we include in the revised ms a list of known MAPs that are present in Xenopus egg extract, along with their estimated concentration from a published proteomic study. We annotate each MAP as to whether it increases or decreases microtubule stability, acknowledging that these data are very incomplete, in some cases there is disagreement in literature, and that we are combining pure protein and whole cell analysis. This table illustrates the challenge of associating dynamics regulation with any one MAP, since the behavior of microtubules is regulated by all these factors operating in parallel. That said, certain MAPs jump out as candidate depolymerization regulators that have been little studied for effects on dynamics, for example, MAP7.

In the revision, we suggest to add this expanded table as a supplementary Table in addition to Table 1.

Protein Description

Gene Symbol

Est. Conc. (nM)

MT polymerization/nucleation/rescue?

MT depolymerization/catastrophe?

Lead reference

Microtubule-associated protein RP/EB family member 1

MAPRE1

1800

Increase

Decrease

PMID: 18364701

Stathmin

STMN1

1600

Decrease

Increase

PMID: 11792540

MAP4

MAP4

960

Increase

Decrease

PMID: 7962090

Echinoderm microtubule-associated protein-like 2

EML2

580

Decrease

Increase

PMID: 11694528

EML4 protein

EML4

500

Increase

Decrease

PMID: 17196341

Disks large-associated protein 5

DLGAP5

380

Increase

Decrease

PMID: 16631580

Cytoskeleton-associated protein 5

CKAP5

300

Increase

Increase

PMID: 23666085

Kinesin-like protein KIF2C

KIF2C

200

Decrease

Increase

PMID: 12620232

CAP-Gly domain-containing linker protein 1

CLIP1

190

na

na

Cytoskeleton-associated protein 4

CKAP4

160

Increase

Decrease

PMID: 9799226

Echinoderm microtubule-associated protein-like 1

EML1

140

na

na

Ensconsin

MAP7

91

na

Decrease

PMID: 31391261

Targeting protein for Xklp2

TPX2

91

Increase

Decrease

PMID: 26414402

Microtubule-associated protein 1B

MAP1B

85

Increase

Decrease

PMID: 7664878

MAP1S

MAP1S

66

Decrease

Decrease

PMID: 25300793

Hyaluronan mediated motility receptor

HMMR

61

na

na

MAP7 domain-containing protein 1

MAP7D1

47

na

na

Cytoskeleton-associated protein 2

CKAP2

46

Increase

Decrease

PMID: 15504249

Microtubule-associated tumor suppressor 1

MTUS1

43

na

na

Kinesin-like protein KIF2A

KIF2A

37

Decrease

Increase

PMID: 29980677

CLIP-associating protein 1

CLASP1

30

Decrease

Decrease

PMID: 29937387

Microtubule-associated protein RP/EB family member 3

MAPRE3

21

Increase

Decrease

PMID: 20850319

MAP7 domain containing 2 protein variant 2 (Fragment)

MAP7D2

8

na

na

CAP-Gly domain-containing linker protein 4

CLIP4

2

na

na

\*Minor comments:***

Figure 1.

typo in the figure legend: "interior (distance>300 μm) vs. periphery (50 μmThere appears to be a clear dip in EB1 density at 100 um (Figure 1C). What could be the cause of that?*

Thank you for catching the typo. We corrected this to “periphery (distance>300 µm) vs. interior (50 µmFigure 2.

Note that the distances used in Figure 2. to define 'interior' and 'periphery' are completely different than those in Figure 1. (Interior in Figure 1 is defined to be between 50 and 280 um from the MTOC, and exterior larger than 300 um. However, in Figure 2. interior is defined as less than 100 um, and exterior as larger than 200 um.) Given that the asters are actively growing, it would be good to clearly explain how these intervals were defined in each case.

For both experiments, we had clearly stated the definitions of interior and periphery, either in the figure legends or in the methods section. We have added a new paragraph explaining why we could not choose exactly the same quantitative definitions for these two methods (please also see our reply to Reviewer #2 comment 1).

In the periphery movie, there are several notable examples of apparent minus-end depolymerization and treadmilling. The authors state these are very rare - perhaps a quantification would be useful here?

Thank you for pointing this out. We modified the sentence to reflect the outward depolymerization events in the periphery. “We observed few outward-moving depolymerization events (Reviewer #1 (Significance (Required)):

The observation of distinct depolymerization rates within vs. at the periphery of microtubule asters is novel and interesting. However, the manuscript in its current form is rather preliminary. The observation can be significantly strengthened by additional experiments/analysis that would characterize the effect in more detail. Even more importantly, the authors propose a highly speculative (although compelling) mechanism, but make no attempt to test it in any way. This is a major deficiency of the current manuscript that should be addressed prior to publication.

REFEREES CROSS COMMENTING

I agree with Reviewer #2 that our comments are both overlapping and complementary. I also find Reviewer #2's comments fair and reasonable and see no need for further adjustments.

RESPONSE TO REVIEWER #2

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

\*SUMMARY ***

This paper reports measurements of microtubule dynamics in interphase asters nucleated in Xenopus egg extracts. Dynamics are measured using two methods. First tracking of GFP tagged EB1 protein forming comets at the tips of growing microtubules, as used in other studies, which can only measure growth rates. Second using a recently developed automated tracking based on subtractive difference images of fluorescently labelled microtubules, which can measure both growth and shrinkage rates. The main and novel observation of this paper, using difference image tracking, is that the MT shrinkage rate is ~2 fold faster in the interior of the aster compared with the periphery of the aster, whilst rates of MT polymerisation and catastrophe vary only slightly, if at all. The authors speculate that this might be due to a reduced MAP concentration and occupancy in the aster interior. They also discuss the role of a depletion-dependent increased shrinkage rate as a feedback mechanism to maintain a low MT polymer density in the aster interior.

\*MAJOR COMMENTS***

The movies are startling in their beauty and clarity and the key conclusion that the shrinkage rate is significantly faster in the interior compared to the periphery of the aster is convincing.

The observation that the rate of net MT plus end growth rate is ~10% faster at the periphery compared to interior of the aster is only supported by EB1 tip tracking method. The difference imaging method shows no significant difference in rates. The authors need to discuss this discrepancy between the established and new methods of analysis. It is insufficient to state that the growth rates obtained by the two methods are "consistent".

This comment prompts the comparison of the two methods (EB1 vs. TIRF difference imaging). On one hand, EB1 tracking is more sensitive in detecting plus ends, and allows large N observations so it is likely to show statistical significance. On the other hand, EB1 tracking method is noisier (higher standard deviation) than the TIRF based measurements (see our response to Reviewer #1). In the TIRF difference imaging, the exact location of the periphery (relative to the center as well as the overall microtubule density profile) is hard to evaluate.

What is consistent between the two methods is the approximate mean value of polymerization rates. The 10% faster polymerization velocity is only suggested by the EB1 tracking method, calling for caution/further investigation. However, the potential relatively small difference in polymerization rate is not the main point of this paper.

We deleted the sentence in the results section for the TIRF method: “These values of polymerization rates are consistent with EB1 comet tracking (Fig. 1). ” We have added a new paragraph discussing the discrepancies between the methods in reporting polymerization rate.

The discussion proposing MAP depletion-dependent increased shrinkage rate as a feedback mechanism to limit MT polymer density is reasonable.

The model and discussion of the role of MAPs might be criticised as highly speculative and unsupported by any experimental data. The authors do acknowledge this. Whether the ratio of data to speculative interpretation is appropriate will be an editorial decision for whichever journal ultimately hosts this.

Thank you. This is exactly the kind of comments that we wanted to hear from an initiative like Review Commons. This helps us gauge how our work is received and decide which journal to submit our work.

In particular since the aster forms by growth from the nucleating bead, early in its formation the final interior MTs must have first formed the peripheral MTs and could therefore enter fresh media and bind MAPs. The authors show by calculation that as the aster expands, these MTs and MAPs become isolated from mixing with the external media. This isolation would then suggest that any MAPS released by dissociation or MT depolymerisation must remain in the interior, and are therefore available to rebind to newly formed MTs. So, it is unclear why the MAPs should be depleted in the interior compared to the periphery, unless expansion of the Aster is slowed in which case additional MAPs could diffuse into the stationary periphery from the surrounding media. The kinetics of MT growth, MAP binding and aster expansion would then also be expected to have an effect on the outcome beyond a simple "depletion" of the internal MAP concentration.

We use the term “depletion” to mean a significant decrease of MAP from the cytoplasm. As outlined in our toy model, more MTs lead to more MAP binding and depletion of soluble MAPs. Note that the total local abundance of MAP is constant unless there is significant diffusive transport of MAP from one region to another. We argue this transport is ineffective for the large length scale of interphase asters.

It is also not clear how the authors preferred model would account for the suggestion of bimodal shrinkage rates. It is not clear if this is a simplification (binning things in to external and internal) applied for the purposes of discussion.

Please see our comment to Reviewer #1. We now believe there is no evidence for bimodality of depolymerization rates. The spread of the data reflects the variability of depolymerization rates in a given a field of view as well as the variability across multiple fields of view.

\*MINOR COMMENTS***

Line 71

Authors reference Gardner et al 2011, when discussing depolymerisation as a zero order process, as showing a free tubulin dimer concentration effect on shrinkage rates. However, the results in Gardner refer to the off rate during MT polymerisation, and measurements of rapid small scale events during overall growth phases and would be applicable to GTP-heterodimers, whereas the extended shrinkage events measured in this paper would presumably apply to post-catastrophe GDP-heterodimer dissociation and may not be comparable. The reference should be omitted or a further explanation given.

Thanks, good point. We wanted to cite Gardner et al (2011) to make the point that classic assembly models may not always hold, but the reviewer is correct, that paper only looked at concentration dependence of depolymerization at growing ends. The text was changed to:

“This assumption has been questioned for growing ends (Gardner 2011)​, but not for shrinking ends to our knowledge.”

Line 89

States "density of plus ends is approximately homogenous within interphase asters"

However, in results section it is stated Line 111 that "the plus end density is lower at the periphery compared to the aster center".

Please clarify

The plus end density is approximately homogenous from the center to the periphery of the aster. However, only at the most peripheral region, where there are few microtubules, the density drops.

Line 135

The distances given for the interior and periphery appear to be mixed up.

Thank you, we corrected this.

Line277

"approximately consistent with our Peclet number estimate". 50µm gives a Pe value of 2.8. The Peclat number "significance" is earlier given in terms of "Pe>>1" (Line255). Please clarify what range of experimental values is required for the argument to hold.

Our statement was unclear. We modified the sentence in the following way to clarify our point: “The half-width of the depleted zone extended ~50 microns beyond the growing aster periphery, which is smaller than the typical aster radius. This analysis indicated that soluble protein levels may vary between subregions of growing asters due to subunit consumption.”

Line 404

needs details of the GFP-EB1 and fluorescent tubulin used in this experiment.

The detailed concentrations are described for each method in the subsequent sections. To avoid confusion, we removed the sentence in line 404, which omitted details.

The tubulin depletion measurements detect a 4% reduction in tubulin concentration in the interior versus the exterior, and the same for eGFP-EB1 (Fig.4B). This observation provides important support for the depletion proposal. But the experiments apparently lack a control for potential reduction of fluorescence excitation intensity with depth in these deep specimens (equivalent to the inner filter effect in spectroscopy). Is there a component whose apparent concentration (fluorescence emission intensity) does not decrease by 4% in the interior of the aster?

Indeed, fluorescent intensity measurements require special attention. Our samples are made by squashing 4 ul of extract under a 18 mm x 18 mm coverslip and the resulting thickness is 10 micron, which we believe is a distance that is too small to result in an inner filter effect.

In response to Reviewer #2’s request for an example of a component whose fluorescence intensity is uniform, we provide the intensity profile of the inert 10kDa Dextran labeled with Alexa568. This serves as a control for the reviewer’s specific concern with our method. We will incorporate this as a supplementary figure in the revision.

There is no direct discussion of the relative lifetime of MTs in the interior compared to the exterior of the aster. Catastrophe rates and growth rates are essentially invariant, I think this implies that MT lifetimes are essentially the same in the interior versus the exterior? Please confirm and estimate the lifetime. This could exclude a maturation process whereby one set of MAPs got replaced by another over time?

Indeed, MT lifetime is a function of four rates: polymerization, depolymerization, catastrophe, and rescue. The figure below shows the MT lifetime as a function of depolymerization rate, assuming other parameters are fixed at what we found in our previous report Ishihara et al. 2016. In regions of fast depolymerization rate 40 µm/min, the microtubule lifetime is 0.98 min. As the depolymerization rate decreases to 30 and 25 µm/min, the lifetime increases to 1.5 and 2.4 min. This implies that the microtubules at the aster periphery are longer lived than those in the interior.

Association and dissociation rate constants have not been measured for most MAPs, but in general we expect them to be fast compared to the timescale of MT lifetime of ~1 minute. Most MAPs bind in the low micromolar or high nM regime, which implies dissociation rates of seconds or less. MAP4 and MAP7 were both shown to bind and dissociate rapidly in living cells (PMID: 16714020, PMID: 11719555)

Reviewer #2 (Significance (Required)):

This paper is significant as it is the first observation of spatial variation in MT shrinkage rates in an aster. It proposes the broad shape of an underlying mechanism (depletion of stabilising MAPS in the aster interior) and presents sound quantitative arguments, but the experiments do not directly test this mechanism. Aster formation in Xenopus egg extracts is widely used as a model system, and if indeed the spatial variation turns out to be due to spatial depletion of components then this will become a landmark paper. The paper may promote wider use of this method of automated analysis and encourage study of shrinkage rate mechanisms in other systems.

REFEREES CROSS COMMENTING

In my opinion the comments of reviewer #1 are fair and reasonable and overlap with and complement my own. In my opinion there is zero conflict requiring adjustment.

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

SUMMARY

This paper reports measurements of microtubule dynamics in interphase asters nucleated in Xenopus egg extracts. Dynamics are measured using two methods. First tracking of GFP tagged EB1 protein forming comets at the tips of growing microtubules, as used in other studies, which can only measure growth rates. Second using a recently developed automated tracking based on subtractive difference images of fluorescently labelled microtubules, which can measure both growth and shrinkage rates. The main and novel observation of this paper, using difference image tracking, is that the MT shrinkage rate is ~2 fold faster in the interior of the aster compared with the periphery of the aster, whilst rates of MT polymerisation and catastrophe vary only slightly, if at all. The authors speculate that this might be due to a reduced MAP concentration and occupancy in the aster interior. They also discuss the role of a depletion-dependent increased shrinkage rate as a feedback mechanism to maintain a low MT polymer density in the aster interior.

MAJOR COMMENTS

The movies are startling in their beauty and clarity and the key conclusion that the shrinkage rate is significantly faster in the interior compared to the periphery of the aster is convincing.

The observation that the rate of net MT plus end growth rate is ~10% faster at the periphery compared to interior of the aster is only supported by EB1 tip tracking method. The difference imaging method shows no significant difference in rates. The authors need to discuss this discrepancy between the established and new methods of analysis. It is insufficient to state that the growth rates obtained by the two methods are "consistent".

The discussion proposing MAP depletion-dependent increased shrinkage rate as a feedback mechanism to limit MT polymer density is reasonable.

The model and discussion of the role of MAPs might be criticised as highly speculative and unsupported by any experimental data. The authors do acknowledge this. Whether the ratio of data to speculative interpretation is appropriate will be an editorial decision for whichever journal ultimately hosts this.

In particular since the aster forms by growth from the nucleating bead, early in its formation the final interior MTs must have first formed the peripheral MTs and could therefore enter fresh media and bind MAPs. The authors show by calculation that as the aster expands, these MTs and MAPs become isolated from mixing with the external media. This isolation would then suggest that any MAPS released by dissociation or MT depolymerisation must remain in the interior, and are therefore available to rebind to newly formed MTs. So, it is unclear why the MAPs should be depleted in the interior compared to the periphery, unless expansion of the Aster is slowed in which case additional MAPs could diffuse into the stationary periphery from the surrounding media. The kinetics of MT growth, MAP binding and aster expansion would then also be expected to have an effect on the outcome beyond a simple "depletion" of the internal MAP concentration.

It is also not clear how the authors preferred model would account for the suggestion of bimodal shrinkage rates. It is not clear if this is a simplification (binning things in to external and internal) applied for the purposes of discussion.

MINOR COMMENTS

Line 71 Authors reference Gardner et al 2011, when discussing depolymerisation as a zero order process, as showing a free tubulin dimer concentration effect on shrinkage rates. However, the results in Gardner refer to the off rate during MT polymerisation, and measurements of rapid small scale events during overall growth phases and would be applicable to GTP-heterodimers, whereas the extended shrinkage events measured in this paper would presumably apply to post-catastrophe GDP-heterodimer dissociation and may not be comparable. The reference should be omitted or a further explanation given.

Line 89 States "density of plus ends is approximately homogenous within interphase asters" However, in results section it is stated Line 111 that "the plus end density is lower at the periphery compared to the aster center". Please clarify

Line 135 The distances given for the interior and periphery appear to be mixed up.

Line277 "approximately consistent with our Peclet number estimate". 50µm gives a Pe value of 2.8. The Peclat number "significance" is earlier given in terms of "Pe>>1" (Line255). Please clarify what range of experimental values is required for the argument to hold.

Line 404 needs details of the GFP-EB1 and fluorescent tubulin used in this experiment.

The tubulin depletion measurements detect a 4% reduction in tubulin concentration in the interior versus the exterior, and the same for eGFP-EB1 (Fig.4B). This observation provides important support for the depletion proposal. But the experiments apparently lack a control for potential reduction of fluorescence excitation intensity with depth in these deep specimens (equivalent to the inner filter effect in spectroscopy). Is there a component whose apparent concentration (fluorescence emission intensity) does not decrease by 4% in the interior of the aster?

There is no direct discussion of the relative lifetime of MTs in the interior compared to the exterior of the aster. Catastrophe rates and growth rates are essentially invariant, I think this implies that MT lifetimes are essentially the same in the interior versus the exterior? Please confirm and estimate the lifetime. This could exclude a maturation process whereby one set of MAPs got replaced by another over time?

Significance

This paper is significant as it is the first observation of spatial variation in MT shrinkage rates in an aster. It proposes the broad shape of an underlying mechanism (depletion of stabilising MAPS in the aster interior) and presents sound quantitative arguments, but the experiments do not directly test this mechanism. Aster formation in Xenopus egg extracts is widely used as a model system, and if indeed the spatial variation turns out to be due to spatial depletion of components then this will become a landmark paper. The paper may promote wider use of this method of automated analysis and encourage study of shrinkage rate mechanisms in other systems.

REFEREES CROSS COMMENTING

In my opinion the comments of reviewer #1 are fair and reasonable and overlap with and complement my own. In my opinion there is zero conflict requiring adjustment.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Ishihara et al. investigate and compare microtubule polymerization/depolymerization dynamics inside vs. at the periphery of microtubule asters in a cell-free Xenopus egg extract system. By tracking EB comets, which localize to growing microtubule ends, they find that the microtubule growth rates and EB comet lifetimes (interpreted as an indicator of microtubule catastrophe rates) are similar between the two spatially-distinct microtubule populations. However, using a tubulin-intensity-difference image analysis, the authors are also able to measure local microtubule depolymerization rates, and they find a significant difference in depolymerization rates of the two populations. Specifically, the authors report that the microtubule depolymerization rates measured within asters are faster than those measured at the periphery.

Specific comments:

Figure 2. In the text, the authors report: "The depolymerization rate was 36.3 {plus minus} 7.9 μm/min (mean, std) in the aster interior, compared to 29.2 {plus minus} 8.9 μm/min (mean, std) at the aster periphery." This difference is certainly not two-fold (as stated in the abstract). It would also be useful to mark the mean rates on the graph in 2B.

The bimodal shape of the depolymerization rate distributions in 2B is very interesting. This definitely warrants further investigation. At the minimum, the depolymerization rates should be determined at 50 um- intervals, as done for other parameters in Figure 1. Could it be that there are two coexisting populations of microtubules at the same location? Or is there a clear spatial compartmentalization of the two that is not obvious here because of the too large of a distance interval used for the measurements. This is a very important distinction for the claims of the paper.

The authors make a point here that the distribution of measured polymerization rates is fairly narrow. This appears to be in contrast with Figure 1B, where polymerization rates take on a wide range of values. How do the two distributions of polymerization rates obtained by these two methods compare?

Figure 3. The laser ablation figure and movies are beautiful, but don't seem to add support to the story. Importantly, the authors do not confirm any spatial variability in depolymerization rate with these experiment. As a matter of fact, although the laser ablation experiments are only performed in the aster interior, the measured depolymerization rates appear to be just as consistent with the periphery rates in Figure 2. as they are with the interior rates in Figure 2. (They span quite a large range of values with the average right in the middle between what was measured for the two areas in Figure 2).

Although the authors report they don't see any correlation between the distance and depolymerization rate, they should still plot the rate as a function of initial cut positions (Figures 3D, 3E).

From the single decaying inward wave the authors conclude that microtubules depolymerize fully to their minus ends which are distributed throughout the aster. Can the possibility that depolymerization is stopped by microtubule lattice defects/islands be excluded by these observations?

What are the effects of the local increase in tubulin concentration due to the subunit release by depolymerization? What about the release of other lattice-binding MAPs (stabilizers)?

Figure 4. Is the local depletion of tubulin/EB1 thought to be only within the narrow annulus at ~100 um distance, or is it not measurable on the inside due to the polymer signal? Can the two be separated? Such a sharp transition within a discrete annular region doesn't speak to the relative effects on the inside vs. the outside of the aster?!

More importantly, the local depletion of either tubulin or EB1 is not a good representation of a depletion of a MAP component that associates with the microtubule lattice. Both tubulin and EB1 bind preferably to microtubule ends, not lattice. Thus showing a profile of slight local tubulin and/or EB depletion does not seem to be relevant for the proposed model. Rather, overall microtubule polymer mass/density as a function of distance may be more relevant?

Figure 5. The toy model is intuitive and clear, but not sufficient without any experimental investigation. An attempt to quantify the actual distributions of at least one or a few selected proposed MAPs is needed. Is the depletion strongest where microtubule density is highest? What is the ratio of a MAP intensity to microtubule polymer density as a function of distance? How does that relate to local depolymerization rates? What are other testable model predictions that can show support for the proposed mechanism?

Also, the table is insufficiently described. Are any or all of these MAPs known to be specific regulators of microtubule depolymerization rates, but not other dynamics parameters?

Minor comments:

Figure 1. typo in the figure legend: "interior (distance>300 μm) vs. periphery (50 μm<distance<280 μm)" There appears to be a clear dip in EB1 density at 100 um (Figure 1C). What could be the cause of that?

Figure 2. Note that the distances used in Figure 2. to define 'interior' and 'periphery' are completely different than those in Figure 1. (Interior in Figure 1 is defined to be between 50 and 280 um from the MTOC, and exterior larger than 300 um. However, in Figure 2. interior is defined as less than 100 um, and exterior as larger than 200 um.) Given that the asters are actively growing, it would be good to clearly explain how these intervals were defined in each case.

In the periphery movie, there are several notable examples of apparent minus-end depolymerization and treadmilling. The authors state these are very rare - perhaps a quantification would be useful here?

Significance

The observation of distinct depolymerization rates within vs. at the periphery of microtubule asters is novel and interesting. However, the manuscript in its current form is rather preliminary. The observation can be significantly strengthened by additional experiments/analysis that would characterize the effect in more detail. Even more importantly, the authors propose a highly speculative (although compelling) mechanism, but make no attempt to test it in any way. This is a major deficiency of the current manuscript that should be addressed prior to publication.

REFEREES CROSS COMMENTING

I agree with Reviewer #2 that our comments are both overlapping and complementary. I also find Reviewer #2's comments fair and reasonable and see no need for further adjustments.

Reviewer #3:

This manuscript reports a series of unique experiments with a single human participant, using an electrode array implanted in the left posterior parietal cortex several years after high-level spinal cord injury. There is a small but increasing number of groups capable of performing this type of research in humans. Most of this work has been focused on the motor system, but studies like this one, characterizing the somatosensory system (touch, in particular), have been increasingly common in the past five years. However, this is the only group focusing on this higher-level, multimodal association area of the cortex.

Most of the recorded neurons were activated bilaterally, which is consistent with earlier monkey work from this lab. Probably the most important component of the work is the analysis of the modest activation in this area that occurs simply when the participant imagines different places on her body being touched - even the insensate arm. This work is virtually impossible to do in monkeys. There are extensive and overlapping analyses of the relation between actual and imagined activation, and the activation arising from inputs (or imagined inputs) from the two sides of the body. Eliminating a number of these and clarifying the remainder may improve the impact.

1) 63: in a tetraplegic human subject recorded with an electrode array implanted in the left PPC I am curious why the array was placed in the left PPC, given the clinical evidence for the greater role of the right side in the formation of internal, multi-modal maps. Some comments would be useful.

2) Fig 1: It would be good to show a panel of representative spikes, perhaps with their single-trial raster responses. This could be in a new figure that includes panel 1D, which is presented in a bit of an odd order as it now stands, coming in the midst of higher-level analyses. Indicate how many trials went into the averages in 1D.

3) 146: we computed a cross-validated coefficient of determination (R^2 within) to measure the strength of neuronal selectivity for each body side. Even after reading the methods (further comments below) it is difficult to figure out what all these related measures reveal. At this point in the text it is very difficult to intuit how R^2 would measure selectivity.

4) Fig 4: Several panels would be more effective if plotted as a function of distance rather than a category. 4E: This panel is borderline too small 4F: definitely too small. Enlarge, perhaps with fewer examples The curves drawn on the panels do not appear to be Gaussian, but neither are they just connected points. Show whatever it was you actually used. The Gaussian assumption does not appear to be very good for the edge cases (first two, last two) which is not terribly surprising.

5) What is added by including both classification and Mahalanobis distance?

6) 354: information coding evolves for a single unit. Two complementary analyses were then performed. In what sense are they complementary? What is added (besides complexity) by including both cluster analysis and PCA?

7) Fig 8C: Despite my best efforts, I have no idea what this is showing

8) 753: Classification was performed using linear discriminant analysis with the following assumptions:

One, the prior probability across tested task epochs was uniform; It is not clear what prior probability this refers to. Just stimulus site?

Two, the conditional probability distribution of each unit on any epoch was normal; Is this a reference to firing rate probability conditioned on stimulus site?

Three, only the mean firing rates differ for unit activity during each epoch (covariance of the normal distributions are the same for each);

Four, firing rates for each input are independent (covariance of the normal distribution is diagonal).

Does this refer to independent firing rates of neurons across stimulus sites? This seems very unlikely, given everything we know about dimensionality of cortex. Perhaps it refers to something else. Cannot all of these assumptions be tested? Were they?

9) 768: we computed the cross-validated coefficient of determination (R2 within) to measure how well a neuron's firing rate could be explained by the responses to the sensory fields. This needs a better description, and I may be missing the point entirely. I assume it is an analysis of mean firing rate (which should be stated explicitly) and that it uses something like the indicator variable of the linear analysis of individual neuron tuning above. In this case is this a logistic regression? As it is computed for each side independently, it would appear that there are only four bits to describe the firing of any given neuron. This would seem to be a pretty impoverished statistic, even if the statistical model is accurate.

10) 786: The purpose of computing a specificity index was to quantify the degree to which a neuron was tuned to represent information pertaining to one side of the body over the other. This is all pretty hard to follow. The R2 metric itself is a bit mysterious, as noted above. Within and across R2 is fairly straightforward, but adds to the complexity, as does SI, which makes comparisons of three different combinations of these measures across sides. Aside from R2 itself, the math is pretty transparent. However, a better high-level description of what insight all the different combinations provide would help to justify using them all. As is, there is no discussion and virtually no description of the difference across these three scatter plots. The critical point apparently, is that, "nearly all recorded PC-IP neurons demonstrate bilateral coding". There should be much a more direct way to make this point.

11) Computing response latency via RF discrimination is rather indirect and assumes that there is significant classification in the first place. I suspect it will add at least some delay beyond more typical tests. Why not a far simpler and more direct test of means in the same sliding window? Alternatively, a change point analysis?

Reviewer #2:

General assessment:

The study by Chivukula et al., explored a unique (n=1) dataset of multi-unit neuron recordings collected in the postcentral-intraparietal area (PC-IP) of a tetraplegic human subject taking part in a brain machine interface clinical trial. The recordings were collected across a set of tasks designed to investigate neuronal responses to both experienced and imagined touch.

Overall I found the manuscript to be well-written, the study to be interesting, and the analysis reasonable. I do, however, think the manuscript would benefit by addressing two main, and a number of minor, issues.

Major comments:

1) The methods would benefit from additional rationale / supporting references throughout. Whereas it is generally clear what was done, it is sometimes less clear why certain choices were made. Perhaps some of the choices are "standard practice" when working with single unit recordings, but I was left in want of a bit more reasoning (or at least direction to relevant literature). Some examples are below:

For the population correlation (line 723): why was the correlation computed 250 times or why were the two distributions shuffled together 2000 times?

For the decode analysis (line 752): consider providing a reference for those interested in better understanding the "peeking" effects mentioned.

Response latency (line 798): how were window parameters determined (for both visualization and the latency calculation). And what was the rationale for them being different - especially given that the data used for the response latency calculation was still visualized (at least in part)? Relatedly, I'd be curious to see the entire time-course for that data rather than just the shaded region of the "visualization" data. Also, it would be nice if a comment (or some data) could be provided regarding how much the latency estimates change based on these parameter choices.

Temporal dynamics of population activity (line 830): why use a 500 ms window, stepped at 100 ms intervals instead of something else?

Temporal dynamics of single unit activity (line 887): it is stated that the neurons were restricted to those whose 90th percentile accuracy was at least 50% to ensure only neurons with some degree of significant selectivity were used for the cluster analysis. But why these particular values? Are the results sensitive to this choice? In this section, I'd also suggest providing references for those interested in better understanding the use of Bayesian information criteria. Similarly, it is stated that PCA is a "standard method for describing the behavior of neural populations" - as such it would be nice to provide some relevant references for the reader.

2) The manuscript would benefit from additional context in the intro as well as a more thorough discussion - particularly with respect to the imagination aspect of the experiment.

Intro: The second paragraph did well in establishing why one might be interested in examining somatosensory processing in the PPC. It was however, less clear why the particular questions at the end of the paragraph were being posed. Perhaps an extra paragraph could be added to bridge the notion that a sizeable body of literature has been developed around somatosensory representation within the PPC and the several "fundamental" questions remaining that are of interest here.

Discussion: The manuscript would benefit from a more thorough discussion of "imagination per se" and the various top-down processes that might be involved - as well as better positioning with respect to previous studies investigating top-down modulation of the somatosensory system. The authors state that the cognitive engagement during the tactile imagery may reflect semantic processing, sensory anticipation, and imagined touch per se - which I would not argue. But I would also expect some explicit mention of processes like attention and prediction. Perhaps these are intended to be captured by "sensory anticipation" - but, for example, attention can be deployed even if no sensation is anticipated. Importantly, it seems that imagining a sensation at a particular body site might well involve attending to that body part. That is, one may first attend to a body part before "imagining" a sensation there - and then even continue to attend there the entire time the imagining is being done. Because of this, perhaps the authors are considering attention to be a part of "imagination per se". But since attention has been shown to modulate somatosensory cortex without imagination, how can one exclude the possibility that the neuronal activity measured here simply reflects this attention component? Regardless, I think the discussion would benefit from a more explicit treatment of these top-down processes - especially given the number of previous studies showing that they are able to modulate activity throughout the somatosensory system. Some literature that may be of interest include:

Roland P (1981) Somatotopical tuning of postcentral gyrus during focal attention in man. A regional cerebral blood flow study. Journal of Neurophysiology 46 (4):744-754

Johansen-Berg H, Christensen V, Woolrich M, Matthews PM (2000) Attention to touch modulates activity in both primary and secondary somatosensory areas. Neuroreport 11 (6):1237-1241

Hamalainen H, Hiltunen J, Titievskaja I (2000) fMRI activations of SI and SII cortices during tactile stimulation depend on attention. Neuroreport 11 (8):1673-1676. doi:10.1097/00001756-200006050-00016

Puckett AM, Bollmann S, Barth M, Cunnington R (2017) Measuring the effects of attention to individual fingertips in somatosensory cortex using ultra-high field (7T) fMRI. Neuroimage 161:179-187. doi:10.1016/j.neuroimage.2017.08.014

Yu Y, Huber L, Yang J, Jangraw DC, Handwerker DA, Molfese PJ, Chen G, Ejima Y, Wu J, Bandettini PA (2019) Layer-specific activation of sensory input and predictive feedback in the human primary somatosensory cortex. Sci Adv 5 (5):eaav9053. doi:10.1126/sciadv.aav9053

Reviewer #1:

In this study Chivukula, Zhang, Aflalo et al. report on an extensive set of neural recordings from human PPC. It is found that many neurons are responsive to touch in specific locations. Interestingly, a considerable fraction of the neurons displayed symmetric bilateral receptive fields. Furthermore, these neurons also became active during imagined touches. The study paves the way for a deeper understanding of the role of the human PPC.

The paper presents a wealth of analysis on an extensive set of recordings. It is generally well written and the analyses are well thought out. My main concerns are regarding missing information and unclear descriptions of some of the analyses undertaken, which are detailed below.

1) At the start of the results section it is stated that the recordings were from "well-isolate and multi-unit neurons". This seems to contradict the Methods section, which only talks about "sorted" neurons. This needs to be clarified, and if multi-units were included, it should be stated which sections this concerns as it will have implications for the results (e.g. for selectivity for different body parts). In any case, the number of neurons included in different analyses should be evident. There are some numbers in the Methods and sprinkled throughout the Results section, but for some of the analyses (e.g. clustering analysis, which was run only on a responsive subset of neurons) no numbers are provided.

2) The linear analysis section needs further details. The coefficients are matched to "conditions" but it is not explained how. I am assuming that each touch location is assigned to a condition c, however the way the model is described suggests that the vector X can in principle have multiple conditions active at the same time. Additionally, could the authors confirm whether it is the significance of the coefficients that determined whether a neuron was classed as responsive as shown in Figure 1? This analysis states a p-value but does give no further information on which test was run and on what data.

3) Figure 1 C could be converted into a matrix that lists all combinations of RF numbers on either side of the body to highlight whether larger RFs on one side of the body generally imply larger RFs on the other side.

4) I am confused about the interpretation of the coefficient of determination as shown in Figure 2A. In the text this is described as testing the "selectivity" of the neurons. To clarify, I am assuming that the "regression analysis" is referring to the linear model described in a previous section. The authors then presumably took the coefficients from this model for a single side only and tested how well they could predict the responses to the opposite side, as assessed by R^2 (Fig 2C,E). Before that in Fig 2A, they tested how well each single-side model could predict the responses. This is all fine, but the "within" comparison then simply tests how well a linear model can explain the observed responses, and has nothing to do with the selectivity of the neuron. For example, the neuron might be narrowly or broadly selective, but the model might fit equally well.

5) Regarding the timing analysis, it is not clear to me how the accuracy can top out at 100% as shown in the figure, when the control conditions were included. Additionally, the authors should state the p value and statistic for the comparison of latencies.

6) Spatial analysis. Could the authors provide the size of the paintbrush tip that was used in this analysis. Furthermore, as stimulation sites were 2 cm apart, it is not appropriate to specify receptive fields down to millimeter precision.

7) Imagery: how many neurons were responsive to both imagery and real touch? Were all neurons that were responsive to imagery also responsive to actual touch? This is left vague and Figure 5 only includes the percentages per condition, but gives no indication of how many neurons responded to several conditions. Whether and how many neurons were responsive to both conditions also determines the ceiling for the correlation analysis in Figure 5D (e.g. if the most neurons are responsive only to actual but not imaginary touch, this will limit the population correlation).

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript. Tamar R Makin (University College London) served as the Reviewing Editor.

Summary:

Chivukula and colleagues report an extensive set of multi-unit neural recordings from PPC of a tetraplegic patient taking part in a brain machine interface clinical trial. The recordings were collected across a set of tasks, designed to investigate neuronal responses to both experienced and imagined touch. It was found that many neurons are responsive to touch in specific locations. Most of the recorded neurons were activated bilaterally, which is consistent with earlier monkey work from this lab. Probably the most important component of the work is the analysis of the modest activation in this area that occurs simply when the participant imagines different places on her body being touched - even the insensate arm. This work is virtually impossible to do in animals, and as such offers a unique opportunity to describe neural properties for higher-level representation of touch. The study therefore paves the way for a deeper understanding of the role of the human PPC in the cognitive processing of somatosensation.

Overall, we found the manuscript to be well-written, the study to be interesting, and for the most part the analyses are well thought out. But at the same time, the reviewers raised multiple main concerns regarding missing information and unclear descriptions of some of the analyses undertaken, which are detailed below over many major and minor comments. In addition, it was felt that there was unnecessary overlap across analyses - the first part especially contains a number of analyses that seem to make very similar points repeatedly or where it is not entirely clear what the point is in the first place. As such, there is a need to identify and cut a lot of the duplicative analyses/results and explain both the essential methods and the interpretation of the remaining results more succinctly and clearly. The key analyses could then be streamlined and better justified, ideally with an eye towards a consistent approach in both parts of the paper. here are also some major considerations regarding the contextualisation and interpretation of the key imagery results, as detailed in the first major comment below.

Reviewer #3:

The manuscript by Schonhaut et al. presents novel analysis on an impressive dataset of more than 1200 neurons across diverse brain areas in the human brain to investigate their modulation by hippocampal theta oscillations. They found a substantive proportion of cells phase-locked to hippocampal activity, mainly in the theta frequency band, in several areas known to be functionally related to the hippocampus, some of them receiving monosynaptic hippocampal inputs but other only indirect ones. These results extend previous reports in humans showing hippocampal interactions with these structures but at the level of mesoscopic activity and highlight the ubiquity of spike-theta timing and the importance of single-unit studies in humans. Additional analysis, detailed below, will contribute to give a better description of the data, provide stronger support for some of the authors' claims and clarify some issues.

1) I assume that the dataset also includes hippocampal units, why then excluding them from the analysis? Although the main novelty is in the coupling of cells in other structures with hippocampal LFPs, it would be useful to also compare it with the coupling of local hippocampal cells.

2) Include average power spectrum of hippocampal LFPs. Additional examples of raw LFP traces overlaid to spectrograms (perhaps in Supplementary) will help to illustrate the nature of hippocampal oscillations.

3) The authors compared fractions of significantly modulated units and their preferred frequencies across regions. While very informative, these analyses are not sufficient to capture the richness of spike-LFP interactions likely existing in the dataset. Were there differences in the strength of phase-locking across regions? (this analysis could be added to Figure 2). Studies in rodents have shown that theta phase-locked units in different structures have characteristics preferred firing phases (when hippocampal LFP is used as a reference). Authors can easily look if this is also the case in their data. They should include both pooled data statistics of mean phases across regions and single neuron examples of firing probability by LFP phase (such examples could be added to the single unit plots in Figure 1).

4) Did phase-locked and non phase-locked units have different properties? The authors can compare if they differ in basic properties such as mean firing rate, waveform width, inter-spike intervals, burstiness, etc., as it has been reported in other studies in non-human primates and rodents. These analyses could be extended to show if units with different properties also differ in their preferred phase-locking frequency, or phase. It would be very interesting if these analyses reveal the existence of heterogeneous cellular populations with different relation to hippocampal theta, even if the single-unit isolation quality is limited due to the low density recordings. In relation to this, authors should also plot unit auto-correlograms. ACGs can be computed for all the spikes, but also only for the strongly phase-locked spikes, to show if, at least during periods of strong oscillatory activity, some units show rhythmicity.

5) To better interpret the results in Figure 4, it would be important to know if the recording sites in both hippocampi were from the same sub-region and similar location along the longitudinal hippocampal axis in each subject and if the degree of synchrony between the LFP in both hemispheres. Coherence or phase-locking between LFPs across hemispheres should be computed and also power spectrum for both of them shown.

6) In Figure 4C-D it seems that phase-locking strength across hemispheres was not correlated but preferred frequency was. This should be quantified and mentioned in text before moving to the correlation in Figure 4E.

7) The analysis in Figure 5D should be complemented by also checking the LFP-LFP phase-locking between the local region and the hippocampus. Were periods of high LFP power correlation also reflect enhanced phase-phase coupling? Were the structures also more phase-synchronous during periods of stronger spike-LFP coupling? These analyses could provide a more direct support for the interpretation of the authors in line with the CTC hypothesis.

8) Was there any relation of the "strongly phase-locked" periods with global variables reflecting brain state (e.g. drowsiness versus attention to the task, etc.) or with the firing dynamics of the units (instantaneous firing rate or inter-spike intervals)?

Reviewer #2:

In this study, Schonhaut et al., describe the phase locking statistics of cortical and subcortical neurons with respect to hippocampal local field potential (LFP) recorded in 18 epilepsy patients undergoing seizure monitoring. Nearly 30% of extrahippocampal neurons showed phase locking to some bandpassed hippocampal signal. Amygdalar and entorhinal neurons were more likely to be phase locked, as compared to neurons recorded in other neocortical sites. Most neurons showed the strongest phase locking to hippocampal theta (2-8 Hz), though neocortical and amygdalar neurons tended to phase lock to lower theta bands. Spikes that were phase locked to hippocampal rhythms occurred during local LFP-states that showed moderate correlations with the spectral patterns observed in the hippocampus. These data are interpreted within the broader "communication through coherence" hypothesis.

Large N, multi-region, single unit studies from humans are rare and the kind of mesoscopic descriptive analyses provided here serve as an important bridge between the large rodent literature on hippocampal physiology and human physiology and cognition. That said, there are some weaknesses in the analyses that could be addressed. Also, a deeper discussion of the biological origin of human theta is merited in the discussion to address alternate explanations - beyond communication through coherence - of the data.

A similar statistical mistake was made several times. The author's logic goes like this: find the argmax in one sample, take the argument that generated that max, and use that to sample in another condition, and report that the max is higher in the first condition than the second. For example, on pg. 6 "This is difficult to reconcile with our results, in which 248/362 neurons (68.5%) phase-locked more strongly to hippocampal LFPs than to locally-recorded LFPs at their preferred hippocampal phase-locking frequency." The same flaw can be seen in Figure 5, where the spikes are sub-sampled to occur during strong phase locking in one condition, thus almost guaranteeing high power in the frequency bands that generated that strong phase locking (which was observed). This is a case in which cross-validating the data may be useful. The authors could take a subset of the hippocampal data to define the preferred frequency, and then test phase locking on the held out data from the hippocampus and cortex.

The relationship between power and phase locking is not fully controlled in this paper. The phase seems to be calculated irrespective of whether there is any instantaneous power at that frequency band, introducing noise. This will bias away from finding significant phase locking to frequency bands that occur transiently. Therefore, I recommend defining some threshold of the existence of the spectral signal prior to using that signal to calculate phase.

A related point has to do with the nature of the theta rhythm in the human. There has been considerable controversy over the years as to whether this is a comparable signal to that studied in the rodent. Based on the citations in this manuscript, and the nomenclature of the spectral band, the authors seek to make explicit the commonality of the underlying physiology, or function. Rodent theta is a sustained rhythm, while primate theta seems to come in bouts, perhaps even related to sampling statistics, such as saccades, leading to the suggestion that the apparent theta may be better thought of as semi-rhythmic evoked responses. How long were the bouts of high theta power? Was eye movement tracked? If so it would be important to relate the signal to eye movements. If the low frequency signal is phase locked to eye movement and potentially reflects semi-rhythmic information arriving to (from?) the hippocampus, then a stronger case could be made that hidden "third parties" synchronize the apparent communication through coherence observed here, and in fact there may be no communication at all.

The authors dedicate much of their discussion to relating the current result to the communication through coherence analyses. Oddly, LFP coherence was never addressed. A strong prediction of the current framing would be that: when coherence is high, phase locking should be high, and higher than other moments when power in either region is high but coherence is not observed. The authors should directly measure how phase locking is modulated by coherence.

The authors also lump together biological entities that should have different phase locking behaviors. The amygdala is not a monolithic region, does phase locking differ by nucleus? Also, do fast spiking inhibitory cells differ from excitatory cells? The authors should relate their phase locking measure to mean firing rate to show that it is insensitive to lower level cell statistics. This is important since the conclusions of the study would be quite different if neurons in the entorhinal cortex had high rates which artifactually drove up phase locking values.

Reviewer #1:

Hippocampal theta oscillations are among the most prominent rhythms in the mammalian brain. Extensive research in rodents has shown that neurons not only within the hippocampus but in widespread cortical areas can be phase-locked to hippocampal theta. Such cross-regional communication within theta frames has been postulated to be the foundation of many hippocampal operations. While previous studies in humans have documented the relationship between LFP theta and spiking in the hippocampus, coupling between hippocampal LFP and more remote cortical areas have not been demonstrated in human subjects. This is the topic of the present work. The authors show that spikes of single (and mostly multi-unit) neurons in multiple cortical regions both in the same and opposite hemispheres are phase locked to transient occurrence of hippocampal theta LFP in the 2-6 Hz range. However, phase-locking is stronger in structures known to be part of the 'limbic system', such as the amygdala and entorhinal cortex. Theta phase locking was stronger to hippocampal than to local LFP and the magnitude of spike phase locking increased when the power of theta increased, associated with increased high frequency power. The results are straightforward and the analysis methods are reliable. The novel information is limited but informative and documents a missing aspect of theta communication in the human brain.

Comments:

1) Given the simple message, the text is a bit long with many repetitions and loose ends. This applies to both Introduction and Discussion. Potential implications to learning, etc are interesting but the findings do not provide additional clues, thus those aspects of the discussion are mainly distractions. Instead, perhaps the authors would like to discuss potential mechanisms of remote unit entrainment. They are talking about multi-synaptic pathways but these are unlikely to be a valid conduit. Instead, the septum, entorhinal cortex or retrosplenial cortex, with their widespread projections, may be responsible for coordinating both hippocampal and neocortical areas.

2) Arguably, the weakest part of the manuscript is the lack of hippocampal neurons. The authors refer to their own previous papers, but in a story which compares hippocampal theta oscillations with remote unit activity, it is strange that the magnitude of theta phase-locking to local hippocampal neurons is not available for comparison.

3) How was the hippocampal LFP reference site chosen and did it vary substantially from subject to subject? Anterior or posterior locations?

4) The authors list 1233 single neurons but in the discussion they make it clear that most of them were multiple neurons. This should be emphasized up front and may be used as an excuse why the authors did not attempt to separate pyramidal cells from interneurons (interneurons have a much higher propensity to be entrained by projected rhythms).

5) Given that units were mixed, a logical extension would be to examine how hippocampal theta phase modulates high gamma in neocortical areas. This could potentially yield a much larger data base, targeting the same question.

6) In the Discussion, the authors suggest that cross-regional theta phase coupling could be related to learning and other cognitive performance. However, spike-LFP coupling and coherence is confounded by LFP power increase and the authors cite Herweg et al., 2020 which did not find a relationship between theta power and memory performance. Is it then not logical to assume that cross-regional coupling may also not be related to memory?

7) Line 36. "Long-term potentiation and long-term depression in the rodent hippocampus are also theta phase-dependent (Hyman et al., 2003)." Pavlides et al. (Brain Res 1988) or Huerta and Lisman (Neuron 1995) are perhaps more relevant references here.

8) Line 82: "significant neocortical and contralateral phase-locking suggests". This is a strange phase. Perhaps significant phase locking of neurons in the neocortex in both hemispheres or similar would be a better formulation.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

Summary:

This is a very intriguing paper showing how hippocampal local field potentials couple with the activity of other cortical regions. This mechanism has been and continues to be extensively studied in other mammals, and thus its existence and relevance in humans is exciting.

Reviewer #2:

This human psychophysics study claims to provide more evidence in support of the popular notion that visual processing of faces may involve partially independent processes for the analysis of static information such as facial shape versus dynamic information such as facial expression. In this respect the scientific hypotheses and conclusions are not novel, although some of the methods (parametric variation of facial expression dynamics using computer-generated animations) and analyses (Bayesian generative modeling of expression dynamics) are relatively new. Although the science is rigorously conducted, the paper currently feels heavy on statistics and technical details but light on data, compelling results and clear interpretation. However, the main problem is that the study fails to provide sufficient controls to support its central claims as currently formulated.

Concerns:

1) A central claim of the paper and the first words in the title are that the behavior studied (categorization of facial expression dynamics) is "shape-invariant". However, the lack of variation in facial shapes (n = 2) used here limits the strength of the conclusions that can be drawn, and it certainly remains an open question whether representations of facial expression dynamics are truly "shape-invariant". A simple control would have been to vary the viewing angle of the avatars, in order to dissociate 3D object shapes from their 2D projections (images). The authors also claim that "face shapes differ considerably" (line 49) amongst primate species, which is clearly true in absolute terms. However, the structural similarity of simian primate facial morphology (i.e. humans and macaques used here) is striking when compared to various non-primate species, which naturally raises questions about just how shape-invariant facial expression recognition is. The lack of data to more thoroughly support the central claim is problematic.

2) As the authors note, macaque and human facial expressions of 'fear' and 'threat' differ considerably in visual salience and motion content - both in 3D and their 2D projections (i.e. optic flow). Indeed, the decision to 'match' expressions across species based on semantic meaning rather than physical muscle activations is a central problem here. Figure 1A illustrates clearly the relative subtlety of the human expression compared to the macaque avatar's extreme open-mouthed pose, while Fig 1D (right panels) shows that this is also true of macaque expressions mapped onto the human avatar. The authors purportedly controlled for this in an 'optic-flow equilibrated' experiment that produced similar results. However, this crucial control is currently difficult to assess since the control stimuli are not illustrated and the description of their creation (in the supplementary materials) is rather convoluted and obfuscates what the actual control stimuli were.

The results of this control experiment that are presented (hidden away in supplementary Fig S3C) show that subjects rated the equilibrated stimuli at similar levels of expressiveness for the human vs macaque avatars. However, what the reader really needs to know is whether subjects rated the human vs macaque expression dynamics to be similarly expressive (irrespective of avatar)? My understanding is that species expression (and not species face shape) is the variable that the authors were attempting to equilibrate for.

In short, the authors have not presented data to convince a reader that their equilibrated stimuli resolve the obvious confound in their original stimuli (namely the correlation between low level visual salience - especially around the mouth region- and the species of the expression dynamics).

3) This paper appears to be the human psychophysics component of work that the authors have recently published using the macaque avatar. The separate paper (Siebert et al., 2020 - eNeuro) reported basic macaque behavioral responses to similar animations, while the task here takes advantage of the more advanced behavioral methods that are possible in human subjects. Nevertheless, the emphasis of the current paper on cross-species perception begs the question - how do macaques perceive these stimuli. Do the authors have any macaque behavioral data for these stimuli (even if not for the 4AFC task) that could be included to round this out? If not, I recommend rewording the title since it's current grammatical structure implies that the encoding is "across species", whereas encoding of species (shape and expression) was only tested in one species (humans).

Reviewer #1:

Overall assessment:

The strengths of this paper are the novel cross species stimuli and very interesting behavioural findings, showing sharper tuning for recognising human expression sequences compared to monkey expressions. Technically, the paper is of a very high quality, both in terms of stimulus creation, but also in terms of analysis. Appropriate control experiments have been run, and in my view, the only concern is the way the results are presented, which I believe can be dealt with by restructuring the text. Other than that, I feel this would make a very nice contribution to the field.

Concerns:

The only major concern that I have is that the main take-home messages do not come through clearly in the way the Results section is currently structured. I found there was still too much technical detail - despite considerable use of Supplementary Information (SI) - which made extracting the empirical findings quite hard work. The details of the multinominal regression, the model comparisons (Table 1) and even the Discriminant Functions (Fig 2), for example, could all be briefly mentioned in the main text, with details provided in Methods or SI. These are all interesting, but I feel the focus should be on the behavioural findings, not the methods.

I would suggest using the Discussion as a guide (this clearly states the key points) making sure the focus is more on Figure 3 and then working through the points more concisely.

Obviously, this can be achieved simply by re-writing and does not take away from the significance of the work in any way. While the quality of the English is generally very high, some very minor wording issues could also be dealt with at this stage.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The paper employs novel cross species stimuli and a well-designed psychophysical paradigm to study the visual processing of facial expression. The authors show that facial expression discrimination is largely invariant to face shape (human vs. monkey). Furthermore, they reveal sharper tuning for recognising human expressions compared to monkey expressions, independent of whether these expressions were conveyed by a human or a monkey face. Technically, the paper is of a very high quality, both in terms of stimulus creation, but also in terms of analysis.

Reviewer #3:

This paper investigates the role of Sox2 in early hippocampal development. Previously the authors investigated conditional knockout mice using a Nestin-Cre line and found few phenotypes. The authors hypothesised that Sox2 may have greater impact on earlier developmental stages. The authors used a similar approach in a previous paper (Ferri et al., 2003) studying the ventral forebrain. To test this in the dorsal telencephalon they generated conditional knockout mice using both Emx1-Cre and FoxG1Cre driver lines. These lines displayed more significant phenotypes in the hippocampus, particularly in the cortical hem and dentate gyrus, and were most severe in the FoxG1Cre cross.

The study is well executed and carefully thought through. Appropriate controls have been included for all experiments.

In Figure 6, the data on Gli3 has been verified with additional luciferase data. The data on Cxcr4 has been previously published and has not been further verified with luciferase analysis. Including panel C in the figure may not be justified unless additional data is included to verify the result. It could be referred to in the discussion.

In addition, related to Figure 6, Bertonlini et al., 2019, identified a number of Sox2 responsive enhancers, expressed in the dorsal telencephalon but it is not clear why these are not incorporated into the model. Further justification in the discussion would be helpful. The authors may also consider discussing how Emx2 in their model since they previously showed it was a negative regulator of Sox2 (Mariani et al 2012) and is required for hippocampal development (eg: Pellegrini et al., 1996; Yoshida et al 1997; Zhao et a la 2006).

Regarding the interpretation of the results in Figure 7, previous work by the authors showed that early deletion of Sox2 using a Bf1Cre driver line resulted in severe developmental defects of the ganglionic eminences and therefore GABAergic interneurons. Are the development of GABAergic interneurons affected in the FoxG1Cre cross? It would be preferable to include some analysis of this, or at least a discussion of this issue in the context of the electrophysiology results.

The authors use an eYFP reporter line in Figure 1- supplement. If they have similar data demonstrating Cre activity with the eYFP reporter crossed into the FoxG1CreXSox2flox/flox and Emx1CreXSox2 flox/flox it would be good to add this. It would demonstrate cell autonomous knockout versus non-cell autonomous knockout of Sox2 and may help with the interpretation of Sox2 function.

Reviewer #2:

This study examines the phenotype of early deletion of Sox2 and shows that there is a major dentate phenotype when fl-Sox2 mice are crossed to Foxg1-Cre when compared to Emx1-Cre or Nestin-Cre. This is a novel phenotype, but I don't think the authors have addressed the basis of this phenotype adequately to understand the basis of the phenotype. In addition, I am concerned about a major confounding issue (see below). I believe significant additional studies are needed to establish the specific role of Sox2 here. Below I list the major concerns.

1) The authors rely on Foxg1-Cre for their main evidence that very early deletion of Sox2 leads to near loss of the dentate. However, it doesn't appear that the authors are aware that Foxg1 het mice have a fairly significant dentate phenotype (see this paper). The Foxg1-Cre line generated by Hebert and used by the authors is a knock-in allele that inactivates the endogenous Foxg1 gene. The authors need to address whether the phenotype they observe is actually due to loss of Sox2 alone at E9.5 vs the combined loss of Sox2 and a copy of Foxg1. In particular, could this explain the difference between Emx1-Cre and Foxg1-Cre lines? If this is the explanation for the difference, it isn't clear to me that the story really holds together without bringing in far more complex compound mutant explanations.

2) The phenotype as described by the authors appears to be most compatible with the published Wnt3a mutant phenotype - perhaps a hypomorphic version makes the most sense or a near phenocopy of the Lef1 mutant. Given this, it appears to me this is really a hem phenotype and is likely explained by the loss of Wnt3a predominantly. Yet the authors don't show direct regulation of Wnt3a by Sox2 - the study would be dramatically enhanced by addressing the mechanism of loss of Wnt3a expression. In addition, examining the expression of Lef1 might reveal the more proximal mechanism of loss of DGC than simply less Wnt3a. This might also be another potential direct target of Sox2 since Lef1 expression is regulated by Wnt signaling but also by other morphogenic signals and could be a Sox2 target.

3) The authors provide little specific analysis of hippocampal subfield specific markers. Their assumption is that the cells that are in the malformed dentate are granule neurons but they don't use any specific markers of DGC (eg Prox1). Instead they rely on cell position and expression of NeuroD (which is nonspecific). Similarly, it would make sense to examine other markers of mossy cells and CA3, which are also in the same region as DGC and made by adjacent neuroepithelium.

4) Much of the study relies on the assumption that Nestin-Cre is an efficient deleter in the entire hippocampus yet there is no direct evidence of this. The authors could easily determine when Sox2 expression is lost in the various Cre-deleter lines using antibodies.

5) I think the electrophysiology section isn't very useful or important. We know that mice with major developmental defects in the DG and hippocampus will have changes in circuit physiology. There is nothing specific about this phenotype, nor does it shed light on the important biology here.

6) The only two direct targets they find don't seem likely to be important players in the phenotypes they describe, thus, it seems that they don't necessarily address the biology here. The Gli3 phenotypes that have been published are quite distinct from this.

7) Some of the dentate phenotype is no doubt due to defects in CR cell production or development and this indirect effect has been seen in many other mutants that affect CR cell production (ie a disorganized dentate). It is hard to see how this part of the phenotype, which is likely due to the hem defects (the neuroepithelium that makes the CR cells) is helping us to understand the fundamental aspects of this phenotype.

Reviewer #1:

In the paper by Mercurio et al, the authors examine the role of SOX2 in the development of mouse hippocampal dentate gyrus. Using conditionally mutant SOX2 mice the authors show that early, but not late, deletion of SOX2 leads to developmental impairments of the dentate gyrus. A drawback of their study is that these findings have been reported previously by the group (Favaro et al. 2009; Ferri et al. 2013). In the current study the authors show additional examples of SOX2 target genes, which are dysregulated in the cortical hem upon early SOX2 deletion. However, as no mechanistic insights how this may affect dentate gyrus development are provided, the general novelty of the study is limited.

Comments:

1) The language of the manuscript needs to be improved.

2) Using different Cre-drivers the authors aim to delete SOX2 at different developmental stages. What references demonstrate that EMX-Cre first deletes SOX2 after E10.5? I don't find where in Tronche et al. 1999 is it shown that Nes-Cre is deleting after E11.5?

3) At line 149 the authors state "...remarkably, in the FoxG1-Cre cKO, the DG appears to be almost absent (Figure 2A).". The question is why this finding is remarkable as it already was published in (Ferri et al. 2013).

4) Line 154 "In the FoxG1-Cre cKO, Reelin expression (marking CRC) is greatly reduced, and a HF is not observed (Figure 2D);...". This statement has no support from Figure 2D.

5) Some of the images presented in Figure 4 are of such poor quality that they are hard to evaluate.

6) In Figure 6 the authors show that SOX2 interacts with the promoter region of the Cxcr4 gene and that the SOX2 bound enhancer is active in the developing Zebrafish brain. These data can be removed as they have been published previously in Bertolini et al. 2019.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript. Joseph G Gleeson (Howard Hughes Medical Institute, The Rockefeller University) served as the Reviewing Editor.

Summary:

The positive aspects of the paper are the examination of the role of SOX2 in the development of mouse hippocampal dentate gyrus. Using conditionally mutant SOX2 mice the authors show that early, but not late, deletion of SOX2 leads to developmental impairments of the dentate gyrus. There were substantial criticisms of the work, most importantly that the work does not advance the field as much as is expected for a high-ranking journal, considering prior publications, and that there could be some difficulties interpreting the data as presented.

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

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Reply to the reviewers

We would like to express our appreciation for both the Editors’ and Reviewers’ efforts as essential contributions to the peer review process. We highly value the Reviewers’ constructive critique of our manuscript#RC-2020_00434R entitled “A drug repurposing screen identifies hepatitis C antivirals as inhibitors of the SARS-CoV2 main protease.__” __

We appreciate the Reviewers’ thoughtful consideration of our work and feel their critiques and recommendations have significantly improved our manuscript. Taken together, we believe the additional data, clarification of data presentation, and revised discussion address the heart of the Reviewers’ previous concerns. Thus we feel the work is ready for reconsideration and will be an impactful addition to the literature appropriate for publication. Below we provide a breakdown and a point by point response to previous review critiques.

Thank you for your attention. We look forward to your response.

Best Wishes,

Brian Kraemer, PhD ▪ Associate Director for Research Geriatric Research Education and Clinical Center ▪ Veterans Affairs Puget Sound Health Care System ▪ Research Professor ▪ Departments of Medicine, Psychiatry and Behavioral Sciences, and Pathology ▪ University of Washington ▪ 1660 South Columbian Way ▪ Seattle, WA 98108 ▪ Phone 206-277-1071 ▪ www.kraemerlab.uw.edu

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

In this manuscript, Baker et al. report the screening of a collection of ~6,070 drugs for their inhibitory activity against the enzymatic activity of the SARS-SoV-2 Mpro protein in vitro using two peptide substrates. 50 compounds with activity against Mpro were identified and tested for their dose-dependent effect in the same assay. Several hits were identified, among which are approved drugs that target the HCV protease.

Indeed, there is an urgent need for effective drugs for SARS-CoV-2 infection, and high throughput screenings can discover novel candidates. However, the novelty of this work is quite limited, as former screens have been published with the same target using the same substrates. Moreover, as discussed below the translational impact of the hits discussed is also quite limited, particularly in the absence of antiviral data. Lastly, there are several overstatements in the write up and it will require major editing.

**Major comments:**

1. Were there any positive controls previously shown to potently inhibit the SARS-CoV-2 Mpro included in the screen (e.g. ebselen)? How did these perform in this assay? When first designing our protease assay, we did use ebselen as the initial control. Ebselen showed low potency in all our in our assays and was not considered as a positive control subsequently. It should be noted that Ebselen failed to work against multiple substrates. It is possible that our buffer conditions prevented Ebselen activity. See data plotted below. After identifying boceprevir as a potent inhibitor, it was used in all subsequent assays as a positive control.

It will be helpful if the authors would provide info re the 50 hits from prior screens conducted with this library of compounds - how promiscuous are they across screens? How toxic in cell based assays?

We have updated the table to provide additional useful information as well as a footnote explaining statuses. The compounds in the Broad repurposing library are generally non-toxic and information about them can be found here: https://clue.io/repurposing

The translational potential of the findings appears to be limited. The calculated IC50s for these drugs in the Mpro assay are very high (10-1000 fold higher) relative to their IC50 in an enzymatic assay involving the HCV protease (Boceprevir: IC50 = 0.95 μM vs. 0.084 μM in HCV), Ciluprevir (IC50 = 20.77 μM vs. 0.0087 in HCV), Telaprevir (IC50 = 15.25 μM vs.0.050 μM in HCV) (https://aac.asm.org/content/aac/57/12/6236.full.pdf ). In the absence of antiviral data, the main statement of the manuscript that "the work presented here supports the rapid evaluation of previous HCV NS3/4A inhibitors for repurposing as a COVID-19 therapy." is thus an overstatement. Even is there is some activity, since likely to be limited, as with the HIV protease inhibitors, its chances to elicit a meaningful clinical effect is low. Moreover, when used in monotherapy, some of these protease inhibitors have a very low genetic barrier to resistance.

We have reworked the discussion to incorporate these concerns and limitations of our results.

There are additional inaccurate or overstatements - e.g. line 61 "Probably the most successful approved antivirals are protease inhibitors such as atazanavir for HIV-1 and simeprevir for hepatitis C. [reviewed in 10 and 11]."

We have reworded this statement: (Page 4, Lines 61-62)

“There is precedence for targeting the protease, as this approach has been successful in treating both HIV-1 and hepatitis C (10,11).”

The manuscript requires editing - e.g. structure of sentences, commas, spacing (including in the abstract) etc.

The manuscript has been re-proofed throughout (see tracked changes version of manuscript)

What is the take home message? The statement "Taken together this work suggests previous large-scale commercial drug development initiatives targeting hepatitis C NS3/4A viral protease should be revisited because some previous lead compounds may be more potent against SARS-CoV-2 Mpro than Boceprevir and suitable for rapid repurposing." is unclear.

The take home message of the manuscript is that HCV-targeting protease inhibitors have potential in blocking the SARS-Cov2 protease and a more thorough analysis of the space is needed. As the reviewer pointed out, the identified hits boceprevir and narlaprevir are less potent when targeting the SARS-Cov2 protease as compared to the HCV protease. However, we believe this work does show the potential for screening HCV-targeting protease inhibitors that may not have made it to the clinic. For instance, Boceprevir or Narlaprevir analogs may be even more potent against Mrpo. Further, we believe that these compounds would benefit from further optimization through medicinal chemistry.

We have expanded the discussion to incorporate issues brought up here and in point 3.

Reviewer #1 (Significance (Required)):

Limited. As discussed above

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

SARS-CoV-2 pandemic causing serious health crisis globally. There are no specific medicine or vaccines to contain this virus currently. To address this issue, the authors developed one efficient fluorescent Mpro assay system and screened ~6070 previous used drugs in this article. Several compounds with activity against SARS-CoV-2 Mpro in vitro were founded. Most hits are hepatitis C NS3/4A protease inhibitors with fair IC50 value. Besides, the authors found that most identified compounds in in silico screen lack activity against Mpro in kinetic protease assays.

These research results are well proved and reproducible. But there are two minor questions I present below:

1. In your Mpro assay optimization process you said substrate MCA-AVLQSGFR-K(Dnp)- K-NH2 had drastically lower rates of Mpro catalyzed hydrolysis and were not considered further in your assay development. And in your Fig.1 I saw extremely low RFU changes. But several nice inhibitors were screened using this substrate that was reported in April. Can you explain this result? The substrates used in our assay appear to be much more efficiently cleaved at least with our buffer conditions and Mpro concentrations tested. Variables including recombinant Mpro purity and activity, differences in assay buffer, reader sensitivity may all play a role, but our best guess is that the substrate identified by Marcin Drag’s group (https://doi.org/10.1101/2020.04.29.068890), is more readily cleaved by Mpro. Although screening with other reported substrates is feasible given previous results, we believe the Ac-Abu-Tle-Leu-Gln-AFC to be superior for use in high throughput screening because of its superior cleavage kinetics yielding an improved signal to background ratio for HTS.

To exclude inhibitors possibly acting as aggregators, a detergent-based control should do at the same time when you do IC50 value measurement.

Compound aggregation is a concern, and our assays were all run with detergent in the buffer. Our buffer composition was 20mM Tris pH 7.8, 150mM NaCl, 1mM EDTA, 1mM DTT, 0.05% Triton X-100.

Reviewer #2 (Significance (Required)):

Nice work but the significance of this article is losing now. Most screened hits are reported in the last serval months. Some inhibitor complex structures have been published or released on Protein Data Bank. The novelty is missing. I suggest the authors add more results and resubmit it again.

**Referees Cross-commenting**

I agree with the other two reviewers' comments. The significance of this work is losing but still has something interest. I think it can be published in the lower-impact journal if they complete our suggestions

We concur with both reviewers that demonstration of antiviral activity would strengthen the impact of the manuscript. However, this work remains outside of the scope of feasibility at our institution. We believe that our screen and hit identification can stand on their own until further translational work can be completed.

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

In this report, Baker et al. show that four inhibitors of hepatitis C virus (HCV) NS3/4 protease (ciluprevir, boceprevir, narlaprevir and telaprevir) are also effective inhibitors of the SARS-CoV-2 main protease (Mpro) in enzymatic assays, with lower IC50 values for narlaprevir and boceprevir (around 1 µM in their assay conditions). HCV NS3/4 inhibitors were identified after screening a library of >6,000 compounds of the Broad Institute, including approved drugs. Screening was done with fluorometric proteolytic assays.

Experiments have been apparently well-done and results are sound. The manuscript needs editing.

Reviewer #3 (Significance (Required)):

Experiments have been apparently well-done and results are sound. However, this is a limited study since there are no data obtained in cell culture and a comparison of IC50 values of the selected drugs against HCV and SARS-CoV-2 proteases is missing. It is difficult to infer whether the drugs would be equally effective against SARS-CoV-2 than against HCV, and otherwise, how much should the doses increase in order to have a therapeutic effect.

The manuscript needs editing (see below) and the Discussion is poor. The results reported by authors are not new, and a discussion of the effects of HCV inhibitors on SARS-CoV-2 replication, based on previous publications is necessary to provide the appropriate context for the study.

Here are some references on Covid-19 and HCV inhibitors, that in my opinion should be considered for discussion and proper citation. As correctly pointed out by Baker and co- workers, docking studies should be considered with caution, though.

We appreciate the feedback and have now reworked and expanded the discussion to incorporate reviewer #1 and #3 comments and suggestions.

1: Ghahremanpour MM, Tirado-Rives J, Deshmukh M, Ippolito JA, Zhang CH, de Vaca IC, Liosi ME, Anderson KS, Jorgensen WL. Identification of 14 Known Drugs as Inhibitors of the Main Protease of SARS-CoV-2. bioRxiv [Preprint]. 2020 Aug 28:2020.08.28.271957. doi: 10.1101/2020.08.28.271957. PMID: 32869018; PMCID: PMC7457600.

2: Sacco MD, Ma C, Lagarias P, Gao A, Townsend JA, Meng X, Dube P, Zhang X, Hu Y, Kitamura N, Hurst B, Tarbet B, Marty MT, Kolocouris A, Xiang Y, Chen Y, Wang J. Structure and inhibition of the SARS-CoV-2 main protease reveals strategy for developing dual inhibitors against Mpro and cathepsin L. bioRxiv [Preprint]. 2020 Jul 27:2020.07.27.223727. doi: 10.1101/2020.07.27.223727. PMID: 32766590; PMCID: PMC7402059.

3: Ma C, Sacco MD, Hurst B, Townsend JA, Hu Y, Szeto T, Zhang X, Tarbet B, Marty MT, Chen Y, Wang J. Boceprevir, GC-376, and calpain inhibitors II, XII inhibit SARS-CoV-2viral replication by targeting the viral main protease. Cell Res. 2020 Aug;30(8):678-692. doi: 10.1038/s41422-020-0356-z. Epub 2020 Jun 15. PMID: 32541865; PMCID: PMC7294525.

4: Ke YY, Peng TT, Yeh TK, Huang WZ, Chang SE, Wu SH, Hung HC, Hsu TA, Lee SJ, Song JS, Lin WH, Chiang TJ, Lin JH, Sytwu HK, Chen CT. Artificial intelligence approach fighting COVID-19 with repurposing drugs. Biomed J. 2020 May 15:S2319- 4170(20)30049-4. doi: 10.1016/j.bj.2020.05.001. Epub ahead of print. PMID: 32426387; PMCID: PMC7227517.

5: Elzupir AO. Inhibition of SARS-CoV-2 main protease 3CLpro by means of α-ketoamide and pyridone-containing pharmaceuticals using in silico molecular docking. J Mol Struct. 2020 Dec 15;1222:128878. doi: 10.1016/j.molstruc.2020.128878. Epub 2020 Jul 10.

PMID: 32834113; PMCID: PMC7347502.

Additional computational studies:

1: Hosseini FS, Amanlou M. Anti-HCV and anti-malaria agent, potential candidates to repurpose for coronavirus infection: Virtual screening, molecular docking, and molecular dynamics simulation study. Life Sci. 2020 Aug 8;258:118205. doi:10.1016/j.lfs.2020.118205. Epub ahead of print. PMID: 32777300; PMCID:PMC7413873.

2: Hakmi M, Bouricha EM, Kandoussi I, Harti JE, Ibrahimi A. Repurposing of known anti- virals as potential inhibitors for SARS-CoV-2 main protease using molecular docking analysis. Bioinformation. 2020 Apr 30;16(4):301-306. doi:10.6026/97320630016301.

PMID: 32773989; PMCID: PMC7392094.

3: Chtita S, Belhassan A, Aouidate A, Belaidi S, Bouachrine M, Lakhlifi T. Discovery of Potent SARS-CoV-2 Inhibitors from Approved Antiviral Drugs via Docking Screening. Comb Chem High Throughput Screen. 2020 Jul 30. doi:10.2174/1386207323999200730205447. Epub ahead of print. PMID: 32748740.

4: Alamri MA, Tahir Ul Qamar M, Mirza MU, Bhadane R, Alqahtani SM, Muneer I, Froeyen M, Salo-Ahen OMH. Pharmacoinformatics and molecular dynamics simulation studies reveal potential covalent and FDA-approved inhibitors of SARS-CoV-2 main protease 3CLpro. J Biomol Struct Dyn. 2020 Jun 24:1-13. doi:10.1080/07391102.2020.1782768. Epub ahead of print. PMID: 32579061; PMCID:PMC7332866.

5: Bafna K, Krug RM, Montelione GT. Structural Similarity of SARS-CoV2 Mpro and HCV NS3/4A Proteases Suggests New Approaches for Identifying Existing Drugs Useful as COVID-19 Therapeutics. ChemRxiv [Preprint]. 2020 Apr 21. doi: 10.26434/chemrxiv.12153615. PMID: 32511291; PMCID: PMC7263768.

6: Eleftheriou P, Amanatidou D, Petrou A, Geronikaki A. In Silico Evaluation of the Effectivity of Approved Protease Inhibitors against the Main Protease of the Novel SARS- CoV-2 Virus. Molecules. 2020 May 29;25(11):2529. doi:10.3390/molecules25112529.

PMID: 32485894; PMCID: PMC7321236.

7: Wang J. Fast Identification of Possible Drug Treatment of Coronavirus Disease-19 (COVID-19) through Computational Drug Repurposing Study. J Chem Inf Model. 2020 Jun 22;60(6):3277-3286. doi: 10.1021/acs.jcim.0c00179. Epub 2020 May 4. PMID: 32315171; PMCID: PMC7197972.

8: Chen YW, Yiu CB, Wong KY. Prediction of the SARS-CoV-2 (2019-nCoV) 3C-like protease (3CL pro) structure: virtual screening reveals velpatasvir, ledipasvir, and other drug repurposing candidates. F1000Res. 2020 Feb 21;9:129. doi: 10.12688/f1000research.22457.2. PMID: 32194944; PMCID: PMC7062204.

Minor comments:

We appreciate the time that the reviewer has taken to address grammatical changes and have addressed each throughout the manuscript with tracked changes.

p.2, line 26: > appears as an attractive

Manuscript edited

p.2, line 27: > we show that the existing

Manuscript edited

p.2, line 33: > separate numbers and units, eg. 1.10 µM (this is a persisting error that should be corrected throughout the whole ms)

Manuscript edited

p.4, line 44: SARS virus should be referred as to SARS-CoV-1 throughout the whole manuscript. MERS-CoV is the name of the virus causing MERS

Manuscript edited

p.4, lines 61-62: > the selection of the specific compounds seems to be arbitrary... why atazanavir and not darunavir or other? The sentence should be rewritten.

Rewritten as: “There is precedence for targeting the protease, as this approach has been successful in treating both HIV-1 and hepatitis C.”

p.6, line 100: Citing Fig. 2B before completing the description of Fig. 1 is distracting. Authors should think of a better way to describe their results.

This was a mistake and should have cited Fig 1B. Thank you for catching this.

p.7, line 116: It is not clear what "10m-20,810" means

This has been clarified to state: “ΔRFU at 10 minutes = 20,810 relative fluorescence units”

p.7, lines 125-126: These sentences belong to an introduction, not appropriate in results section.

We have removed these sentences.

Figure 2. Part A is not necessary in results (ok for introduction). Black and purple dots in part B is not a good choice since they are difficult to distinguish, maybe orange and black is better.

We have removed panel A, expanded the size of panel B and changed the color.

Table 1: Status should be explained in a footnote (i.e the distinction between launched, P2/P3, phase 2, preclinical is not clear).

The one compound indicated in P2/P3 development is now Phase 3 and the table has been updated. We have added a footnote:

*Launched = compound approved for humans, though may only be approved for veterinary use in some countries

Discussion. I think that subheadings are not necessary.

Subheadings have been removed from the discussion.

**Referees cross-commenting** I agree with reviewer no. 1 on the limited interest of the study. However, it could be published in a specialized lower-impact journal after addressing issues raised by reviewers 2 and 3 (likely to be completed in less than a month)

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Referee #3

Evidence, reproducibility and clarity

In this report, Baker et al. show that four inhibitors of hepatitis C virus (HCV) NS3/4 protease (ciluprevir, boceprevir, narlaprevir and telaprevir) are also effective inhibitors of the SARS-CoV-2 main protease (Mpro) in enzymatic assays, with lower IC50 values for narlaprevir and boceprevir (around 1 µM in their assay conditions). HCV NS3/4 inhibitors were identified after screening a library of >6,000 compounds of the Broad Institute, including approved drugs. Screening was done with fluorometric proteolytic assays.

Experiments have been apparently well-done and results are sound. The manuscript needs editing.

Significance

Experiments have been apparently well-done and results are sound. However, this is a limited study since there are no data obtained in cell culture and a comparison of IC50 values of the selected drugs against HCV and SARS-CoV-2 proteases is missing. It is difficult to infer whether the drugs would be equally effective against SARS-CoV-2 than against HCV, and otherwise, how much should the doses increase in order to have a therapeutic effect. The manuscript needs editing (see below) and the Discussion is poor. The results reported by authors are not new, and a discussion of the effects of HCV inhibitors on SARS-CoV-2 replication, based on previous publications is necessary to provide the appropriate context for the study. Here are some references on Covid-19 and HCV inhibitors, that in my opinion should be considered for discussion and proper citation. As correctly pointed out by Baker and co-workers, docking studies should be considered with caution, though.

1: Ghahremanpour MM, Tirado-Rives J, Deshmukh M, Ippolito JA, Zhang CH, de Vaca IC, Liosi ME, Anderson KS, Jorgensen WL. Identification of 14 Known Drugs as Inhibitors of the Main Protease of SARS-CoV-2. bioRxiv [Preprint]. 2020 Aug 28:2020.08.28.271957. doi: 10.1101/2020.08.28.271957. PMID: 32869018; PMCID: PMC7457600.

2: Sacco MD, Ma C, Lagarias P, Gao A, Townsend JA, Meng X, Dube P, Zhang X, Hu Y, Kitamura N, Hurst B, Tarbet B, Marty MT, Kolocouris A, Xiang Y, Chen Y, Wang J. Structure and inhibition of the SARS-CoV-2 main protease reveals strategy for developing dual inhibitors against M^pro and cathepsin L. bioRxiv [Preprint]. 2020 Jul 27:2020.07.27.223727. doi: 10.1101/2020.07.27.223727. PMID: 32766590; PMCID: PMC7402059.

3: Ma C, Sacco MD, Hurst B, Townsend JA, Hu Y, Szeto T, Zhang X, Tarbet B, Marty MT, Chen Y, Wang J. Boceprevir, GC-376, and calpain inhibitors II, XII inhibit SARS-CoV-2 viral replication by targeting the viral main protease. Cell Res. 2020 Aug;30(8):678-692. doi: 10.1038/s41422-020-0356-z. Epub 2020 Jun 15. PMID: 32541865; PMCID: PMC7294525.

4: Ke YY, Peng TT, Yeh TK, Huang WZ, Chang SE, Wu SH, Hung HC, Hsu TA, Lee SJ, Song JS, Lin WH, Chiang TJ, Lin JH, Sytwu HK, Chen CT. Artificial intelligence approach fighting COVID-19 with repurposing drugs. Biomed J. 2020 May 15:S2319-4170(20)30049-4. doi: 10.1016/j.bj.2020.05.001. Epub ahead of print. PMID: 32426387; PMCID: PMC7227517.

5: Elzupir AO. Inhibition of SARS-CoV-2 main protease 3CLpro by means of α-ketoamide and pyridone-containing pharmaceuticals using in silico molecular docking. J Mol Struct. 2020 Dec 15;1222:128878. doi: 10.1016/j.molstruc.2020.128878. Epub 2020 Jul 10. PMID: 32834113; PMCID: PMC7347502.

Additional computational studies:

1: Hosseini FS, Amanlou M. Anti-HCV and anti-malaria agent, potential candidates to repurpose for coronavirus infection: Virtual screening, molecular docking, and molecular dynamics simulation study. Life Sci. 2020 Aug 8;258:118205. doi:10.1016/j.lfs.2020.118205. Epub ahead of print. PMID: 32777300; PMCID:PMC7413873.

2: Hakmi M, Bouricha EM, Kandoussi I, Harti JE, Ibrahimi A. Repurposing of known anti-virals as potential inhibitors for SARS-CoV-2 main protease using molecular docking analysis. Bioinformation. 2020 Apr 30;16(4):301-306. doi:10.6026/97320630016301. PMID: 32773989; PMCID: PMC7392094.

3: Chtita S, Belhassan A, Aouidate A, Belaidi S, Bouachrine M, Lakhlifi T. Discovery of Potent SARS-CoV-2 Inhibitors from Approved Antiviral Drugs via Docking Screening. Comb Chem High Throughput Screen. 2020 Jul 30. doi:10.2174/1386207323999200730205447. Epub ahead of print. PMID: 32748740.

4: Alamri MA, Tahir Ul Qamar M, Mirza MU, Bhadane R, Alqahtani SM, Muneer I, Froeyen M, Salo-Ahen OMH. Pharmacoinformatics and molecular dynamics simulation studies reveal potential covalent and FDA-approved inhibitors of SARS-CoV-2 main protease 3CL^pro. J Biomol Struct Dyn. 2020 Jun 24:1-13. doi:10.1080/07391102.2020.1782768. Epub ahead of print. PMID: 32579061; PMCID:PMC7332866.

5: Bafna K, Krug RM, Montelione GT. Structural Similarity of SARS-CoV2 M^pro and HCV NS3/4A Proteases Suggests New Approaches for Identifying Existing Drugs Useful as COVID-19 Therapeutics. ChemRxiv [Preprint]. 2020 Apr 21. doi: 10.26434/chemrxiv.12153615. PMID: 32511291; PMCID: PMC7263768.

6: Eleftheriou P, Amanatidou D, Petrou A, Geronikaki A. In Silico Evaluation of the Effectivity of Approved Protease Inhibitors against the Main Protease of the Novel SARS-CoV-2 Virus. Molecules. 2020 May 29;25(11):2529. doi:10.3390/molecules25112529. PMID: 32485894; PMCID: PMC7321236.

7: Wang J. Fast Identification of Possible Drug Treatment of Coronavirus Disease-19 (COVID-19) through Computational Drug Repurposing Study. J Chem Inf Model. 2020 Jun 22;60(6):3277-3286. doi: 10.1021/acs.jcim.0c00179. Epub 2020 May 4. PMID: 32315171; PMCID: PMC7197972.

8: Chen YW, Yiu CB, Wong KY. Prediction of the SARS-CoV-2 (2019-nCoV) 3C-like protease (3CL ^pro) structure: virtual screening reveals velpatasvir, ledipasvir, and other drug repurposing candidates. F1000Res. 2020 Feb 21;9:129. doi: 10.12688/f1000research.22457.2. PMID: 32194944; PMCID: PMC7062204.

Minor comments:

p.2, line 26: > appears as an attractive

p.2, line 27: > we show that the existing

p.2, line 33: > separate numbers and units, eg. 1.10 µM (this is a persisting error that should be corrected throughout the whole ms)

p.4, line 44: SARS virus should be referred as to SARS-CoV-1 throughout the whole manuscript. MERS-CoV is the name of the virus causing MERS

p.4, lines 61-62: > the selection of the specific compounds seems to be arbitrary... why atazanavir and not darunavir or other? The sentence should be rewritten.

p.6, line 100: Citing Fig. 2B before completing the description of Fig. 1 is distracting. Authors should think of a better way to describe their results.

p.7, line 116: It is not clear what "10m-20,810" means

p.7, lines 125-126: These sentences belong to an introduction, not appropriate in results section.

Figure 2. Part A is not necessary in results (ok for introduction). Black and purple dots in part B is not a good choice since they are difficult to distinguish, maybe orange and black is better.

Table 1: Status should be explained in a footnote (i.e the distinction between launched, P2/P3, phase 2, preclinical is not clear).

Discussion. I think that subheadings are not necessary.

Referees cross-commenting

I agree with reviewer no. 1 on the limited interest of the study. However, it could be published in a specialized lower-impact journal after addressing issues raised by reviewers 2 and 3 (likely to be completed in less than a month)

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Referee #2

Evidence, reproducibility and clarity

SARS-CoV-2 pandemic causing serious health crisis globally. There are no specific medicine or vaccines to contain this virus currently. To address this issue, the authors developed one efficient fluorescent Mpro assay system and screened ~6070 previous used drugs in this article. Several compounds with activity against SARS-CoV-2 Mpro in vitro were founded. Most hits are hepatitis C NS3/4A protease inhibitors with fair IC50 value. Besides, the authors found that most identified compounds in in silico screen lack activity against Mpro in kinetic protease assays.

These research results are well proved and reproducible. But there are two minor questions I present below:

1.In your Mpro assay optimization process you said substrate MCA-AVLQSGFR-K(Dnp)-K-NH2 had drastically lower rates of Mpro catalyzed hydrolysis and were not considered further in your assay development. And in your Fig.1 I saw extremely low RFU changes. But several nice inhibitors were screened using this substrate that was reported in April. Can you explain this result?

2.To exclude inhibitors possibly acting as aggregators, a detergent-based control should do at the same time when you do IC50 value measurement.

Significance

Nice work but the significance of this article is losing now. Most screened hits are reported in the last serval months. Some inhibitor complex structures have been published or released on Protein Data Bank. The novelty is missing. I suggest the authors add more results and resubmit it again.

Referees Cross-commenting

I agree with the other two reviewers' comments. The significance of this work is losing but still has something interest. I think it can be published in the lower-impact journal if they complete our suggestions

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Baker et al. report the screening of a collection of ~6,070 drugs for their inhibitory activity against the enzymatic activity of the SARS-SoV-2 Mpro protein in vitro using two peptide substrates. 50 compounds with activity against Mpro were identified and tested for their dose-dependent effect in the same assay. Several hits were identified, among which are approved drugs that target the HCV protease.<br> Indeed, there is an urgent need for effective drugs for SARS-CoV-2 infection, and high throughput screenings can discover novel candidates. However, the novelty of this work is quite limited, as former screens have been published with the same target using the same substrates. Moreover, as discussed below the translational impact of the hits discussed is also quite limited, particularly in the absence of antiviral data. Lastly, there are several overstatements in the write up and it will require major editing.

Major comments:

1.Were there any positive controls previously shown to potently inhibit the SARS-CoV-2 Mpro included in the screen (e.g. ebselen)? How did these perform in this assay?

2.It will be helpful if the authors would provide info re the 50 hits from prior screens conducted with this library of compounds - how promiscuous are they across screens? How toxic in cell based assays?

3.The translational potential of the findings appears to be limited. The calculated IC50s for these drugs in the Mpro assay are very high (10-1000 fold higher) relative to their IC50 in an enzymatic assay involving the HCV proteast (Boceprevir: IC50 = 0.95 μM vs. 0.084 μM in HCV), Ciluprevir (IC50 = 20.77 μM vs. 0.0087 in HCV), Telaprevir (IC50 = 15.25 μM vs. 0.050 μM in HCV) (https://aac.asm.org/content/aac/57/12/6236.full.pdf ). In the absence of antiviral data, the main statement of the manuscript that "the work presented here supports the rapid evaluation of previous HCV NS3/4A inhibitors for repurposing as a COVID-19 therapy." is thus an overstatement. Even is there is some activity, since likely to be limited, as with the HIV protease inhibitors, its chances to elicit a meaningful clinical effect is low. Moreover, when used in monotherapy, some of these protease inhibitors have a very low genetic barrier to resistance.

4.There are additional inaccurate or overstatements - e.g. line 61 "Probably the most successful approved antivirals are protease inhibitors such as atazanavir for HIV-1 and simeprevir for hepatitis C. [reviewed in 10 and 11]."

5.The manuscript requires editing - e.g. structure of sentences, commas, spacing (including in the abstract) etc.

6.What is the take home message? The statement "Taken together this work suggests previous large-scale commercial drug development initiatives targeting hepatitis C NS3/4A viral protease should be revisited because some previous lead compounds may be more potent against SARS-CoV-2 Mpro than Boceprevir and suitable for rapid repurposing." is unclear.

Significance

Limited. As discussed above

Reviewer #3:

This fMRI study examines an interesting question, namely how computer code - as a "cognitive/cultural invention" - is processed by the human brain. However, I have a number of concerns with regard to how this question was examined in terms of experimental design, including the choice of control condition (fake code) and the way in which localiser tasks were utilised. In addition, the sample size is very small (n=15) and there appear to be large inter-individual differences in coding performance (in spite of the recruitment of expert programmers). In summary, while promising in its aims, the study's conclusions are weakened by these considerations related to its execution.

1) The control condition

The experiment contrasted real Python code with fake code in the form of "incomprehensible scrambled Python functions". Real and fake code also differed in regard to the task performed (code comprehension versus memory) and were distinguished via colour coding. There is a lot to unpack here in regard to how processing might differ between the two different conditions. For example, the real code blocks required code comprehension as well as computational problem solving (which does not necessarily require the use of code), while the control task requires neither. As a result of the colour coding, it also appears likely that participants will have approached the fake code blocks with a completely different processing strategy than the real code blocks. These are just a few obvious differences between the conditions but there are likely many more given how different they are. This, in my view, makes it difficult to interpret the basic contrast between real and fake code.

2) Use of localiser tasks

A similar concern as for point 1 holds in regard to the localiser tasks that were used in order to examine anatomical overlap (or lack thereof) between code comprehension and language, maths, logical problem solving and multiple-demand executive control, respectively. I am generally somewhat sceptical in regard to the use of functional localisers in view of the assumptions that necessarily enter into the definition of a localiser task. This concern is exacerbated by the way in which localisers were employed in the present study. Firstly, in addition to the definition of the localiser task itself, this study used localiser contrasts to define networks of interest. For example, the contrast language localiser > maths localiser served to define the "language network". Thus, assumptions about the nature of the localiser itself are compounded with those regarding the nature of the contrast. Secondly, particularly with regard to language, the localiser task was very high level, i.e. requiring participants to judge whether an active and a passive sentence had the same meaning (with both statements remaining on the screen at the same time). While of course requiring language processing, this task is arguably also a problem solving task of sorts. It is certainly more complex than a typical task designed to probe fast and automatic aspects of natural language processing.

In addition, given that reading is also a cultural invention, is it really fair to say that coding is being compared to the "language network" here rather than to the "reading network" (in view of the visual presentation of the language task)? The possible implications of this for the interpretation of the data should be considered.

More generally, while an anatomical overlap between networks active during code comprehension and networks recruited during other cognitive tasks may shed some initial light on how the brain processes code, it doesn't support any particularly strong conclusions about the neural mechanisms of code processing in my view. While code comprehension may overlap anatomically with regions involved in executive control and logic, this doesn't mean that the same neuronal populations are recruited in each task nor that the processing mechanisms are comparable between tasks.

3) Sample size and individual differences

At n=15, the sample size of this study is quite small, even for a neuroimaging study. This again limits the conclusions that can be drawn from the study results.

Moreover, the results of the behavioural pre-test - which was commendably included - suggest that participants differed considerably with regard to their Python expertise. For the more difficult exercise in this pre-test, the mean accuracy score was 64.6% with a range from 37.5% to 93.75%. These substantial differences in proficiency weren't taken into account in the analysis of the fMRI data and, indeed, it appears difficult to meaningfully do so in view of the sample size.

Reviewer #2:

The goal of this fMRI study was to determine which brain systems support coding, by way of the extent of overlap of univariate maps with localizer tasks for language, logic, math, and executive functions. The basic conclusion is one we could have anticipated: coding engages a widespread frontoparietal network, with stronger involvement of the left hemisphere. It overlaps with all of the other tasks, but most with the map for logic. This doesn't seem too surprising, but the authors argue convincingly that others wouldn't have predicted that.

It's unfortunate that there are differences in task difficulty among the tasks - in particular, that the logic task was the most difficult of all (both in terms of accuracy and response times), since that happens to be the one that had the largest number of overlapping voxels with the coding task. We can't know whether coding and language task voxels would have overlapped more if the language task had been more difficult.

It seems a shame to present data only from highly experienced coders (11+ years of experience); I can imagine that the investigators are planning to write up another study examining effects of expertise, in comparison with less experienced coders. This seems like an initial paper that's laying the groundwork for a more groundbreaking one.

Reviewer #1:

This manuscript is clearly written and the methods appear to be rigorous, although the number of subjects (15) is a bit low; however, this does not appear to critically limit interpretation of the results. I appreciated the focused inclusion on expert coders to make a clear comparison to language. I also thought that the inclusion of multiple domains for comparison (logic, math, executive function, and language) was quite informative. The laterality covariance between code and language was also quite interesting. I do have some concerns with the literature review and discussion of present and previous results.

1) My main concern with this paper is that it does not clearly review previous fMRI studies on code processing. How do the present results compare with previous studies? E.g. Castelhano et al., 2019; Floyd et al., 2017; Huang et al., 2019; Krueger et al., 2020; Siegmund et al., 2017, 2014;) It seems like the localization/lateralization obtained in the present study is largely similar to these previous studies (e.g. Siegmund et al., 2017). If so, this should be discussed: a convergence across multiple methods/authors is useful to know. Any discrepancies are also useful to know. The authors suggest that "Moreover, no prior study has directly compared the neural basis of code to other cognitive domains." However, Krueger et al. (2020) and Huang et al. (2019) appear to have done this.

2) The authors should point out and discuss the difficulty of understanding the psychological and neural structure of coding in absence of a clear theory of coding, as is the case for language (e.g. Chomsky, 1965; Levelt, 1989; Lewis & Vasishth, 2005). On this point, I appreciate the reference to Fitch et al. (2005) regarding recursion in coding, but I think it would be most helpful to have a clear example of recursion in python code. However, the authors at least focus their results on neural underpinnings without attempting to make strong claims about cognitive underpinnings.

3) The authors report overlap between code comprehension and language in the posterior MTG and IFG. They note that these activations were somewhat inconsistent; yet, they did observe this significant overlap. However the paper discusses the results as if this overlap did not occur, e.g. "We find that the perisylvian fronto-temporal network that is selectively responsive to language, relative to math, does not overlap with the neural network involved in code comprehension." This is not accurate, as there indeed was overlap. It is important to point out that among language-related regions, these two regions are the most strongly associated with abstract syntax (Friederici, 2017; Hagoort, 2005; Tyler & Marslen-Wilson, 2008; Pallier et al., 2011; Bornkessel-Schlesewsky & Schlesewsky, 2013; Matchin & Hickok, 2019), which very well could be a point of shared resources among code and language (as discussed in Fitch, 2005).

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 3 of the manuscript.

This was co-submitted with the following manuscript: https://www.biorxiv.org/content/10.1101/2020.04.16.045732v1

Summary:

The remit of the co-submission format is to ask if the scientific community is enriched by the data presented in the co-submitted manuscripts together more so than it would be by the papers apart, or if only one paper was presented to the community. In other words, are the conclusions that can be made stronger or clearer when the manuscripts are considered together rather than separately? We felt that despite significant concerns with each paper individually, especially regarding the theoretical structures in which the experimental results could be interpreted, that this was the case.

We want to be very clear that in a non-co-submission case we would have substantial and serious concerns about the interpretability and robustness of the Liu et al. submission given its small sample size. Furthermore, the reviewers' concerns about the suitability of the control task differed substantially between the manuscripts. We share these concerns. However, despite these differences in control task and sample size, the Liu et al. and Ivanova et al. submissions nonetheless replicated each other - the language network was not implicated in processing programming code. The replication substantially mitigates the concerns shared by us and the reviewers about sample size and control tasks. The fact that different control tasks and sample sizes did not change the overall pattern of results, in our view, is affirmation of the robustness of the findings, and the value that both submissions presented together can offer the literature.

In sum, there were concerns that both submissions were exploratory in nature, lacking a strong theoretical focus, and relied on functional localizers on novel tasks. However, these concerns were mitigated by the following strengths. Both tasks ask a clear and interesting question. The results replicate each other despite task differences. In this way, the two papers strengthen each other. Specifically, the major concerns for each paper individually are ameliorated when considering them as a whole.

The concerns of the reviewers need addressing, including, specifically, the limits of interpretation of your results with regard to control task choice, the discussion of relevant literature mentioned by the reviewers, and most crucially, please contextualize your results with regard to the other submission's results.

Reviewer #2:

This carefully designed fMRI study examines an interesting question, namely how computer code - as a "cognitive/cultural invention" - is processed by the human brain. The study has a number of strengths, including: use of two very different programming languages (Python and Scratch Jr.) in two experiments; direct comparison between code problems and "content-matched sentence problems" to disentangle code comprehension from problem content; control for the impact of lexical information in code passages by replacing variable names with Japanese translations; and consideration of inter-individual differences in programming proficiency. I do, however, have some questions regarding the interpretation of the results in mechanistic terms, as detailed below.

1) Code comprehension versus underlying problem content

I am generally somewhat sceptical in regard to the use of functional localisers in view of the assumptions that necessarily enter into the definition of a localiser task. In addition, an overlap between the networks supporting two different tasks doesn't imply comparable neural processing mechanisms. With the present study, however, I was impressed by the authors' overall methodological approach. In particular, I found the supplementation of the localiser-based approach with the comparison between code problems and analogous sentence problems rather convincing.

However, while I agree that computational thinking does not require coding / code comprehension, it is less clear to me what code comprehension involves when it is stripped of the computational thinking aspect. Knowing how to approach a problem algorithmically strikes me as a central aspect of coding. What, then, is being measured by the code problem versus sentence problem comparison? Knowledge of how to implement a certain computational solution within a particular programming language? The authors touch upon this briefly in the Discussion section of the paper, but I am not fully convinced by their arguments. Specifically, they state:

"The process of code comprehension includes retrieving code-related knowledge from memory and applying it to the problems at hand. This application of task-relevant knowledge plausibly requires attention, working memory, inhibitory control, planning, and general flexible reasoning-cognitive processes long linked to the MD system [...]." (p.17)

Shouldn't all of this also apply (or even apply more strongly) to processing of the underlying problem content rather than to code comprehension per se?

According to the authors, the extent to which code-comprehension-related activity reflects problem content varies between different systems. At the bottom of p.9, they conclude that "MD responses to code [...] do not exclusively reflect responses to problem content", while on p.13 they argue on the basis of their voxel-wise correlation analysis that "the language system's response to code is largely (although not completely) driven by problem content. However, unless I have missed something, the latter analysis was only undertaken for the language system but not for the other systems under examination. Was there a particular reason for this? Also, what are the implications of observing problem content-driven responses within the language system for the authors' conclusion that this system is "functionally conservative"?

Overall, the paper would be strengthened by more clarity in regard to these issues - and specifically a more detailed discussion of what code comprehension may amount to in mechanistic terms when it is stripped of computational thinking.

2) Implications of using reading for the language localiser task

Given that reading is also a cultural invention, is it really fair to say that coding is being compared to the "language system" here rather than to the "reading system" (in view of the visual presentation of the language task)? The possible implications of this for the interpretation of the data should be considered.

3) Possible effects of verbalisation?

It appears possible that participants may have internally verbalised code problems - at least to a certain extent (and likely with a considerable degree of inter-individual variability). How might this have affected the results of the present study? Could verbalisation be related to the highly correlated response between code problems and language problems within the language system?

Reviewer #1:

The manuscript is well-written and the methods are clear and rigorous, representing a clear advance on previous research comparing computer code programming to language. The conclusions with respect to which brain networks computer programming activates are compelling and well conveyed. This paper is useful to the extent that the conclusions are focused on the empirical findings: whether or not code activates language-related brain regions (answer: no). However, the authors appear to be also testing whether or not any of the mechanisms involved in language are recruited for computer programming. The problem with this goal is that the authors do not present or review a theory of the representations and mechanisms involved in computer programming, as has been developed for language (e.g. Adger, 2013; Bresnan, 2001; Chomsky, 1965, 1981, 1995; Goldberg, 1995; Hornstein, 2009; Jackendoff, 2002; Levelt, 1989; Lewis & Vasishth, 2005; Vosse & Kempen, 2000).

1) p. 15: "The fact that coding can be learned in adulthood suggests that it may rely on existing cognitive systems." p. 3: "Finally, code comprehension may rely on the system that supports comprehension of natural languages: to successfully process both natural and computer languages, we need to access stored meanings of words/tokens and combine them using hierarchical syntactic rules (Fedorenko et al., 2019; Murnane, 1993; Papert, 1993) - a similarity that, in theory, should make the language circuits well-suited for processing computer code." If we understand stored elements and computational structure in the broadest way possible without breaking this down more, many domains of cognition would be shared in this way. The authors should illustrate in more detail how the psychological structure of computer programming parallels language. Is there an example of hierarchical structure in computer code? What is the meaning of a variable/function in code, and how does this compare to meaning in language?

2) p. 19 lines 431-433: "Our findings, along with prior findings from math and logic (Amalric & Dehaene, 2019; Monti et al., 2009, 2012), argue against this possibility: the language system does not respond to meaningful structured input that is non-linguistic." This is an overly simple characterization of the word "meaningful". The meaning of math and logic are not the same as in language. Both mathematics and computer programming have logical structure to them, but the nature of this structure and the elements that are combined in language are different. Linguistic computations take as input complex atoms of computation that have phonological and conceptual properties. These atoms are commonly used to refer to entities "in the world" with complex semantic properties and often have rich associated imagery. Linguistic computations output complex, monotonically enhanced forms. So cute + dogs = cute dogs, chased + cute dogs = chased cute dogs, etc. This is very much unlike mathematics and computer programming, where we typically do not make reference to the "real world" using these expressions to interlocuters, and outputs of an expression are not monotonic, structure-preserving combinations of the input elements, and there is no semantic enhancement that occurs through increased computation. This bears much more discussion in the paper, if the authors intend to make claims regarding shared/distinct computations between computer programming and language.

3) More importantly, even if there were shared mechanisms between computer code programming and language, I'm not sure we can use reverse inference to strongly test this hypothesis. As Poldrack (2006) pointed out, reverse inference is sharply limited by the extent to which we know how cognition maps onto the brain. This is a similar point to Poeppel & Embick, (2005), who pointed out that different mechanisms of language could be implemented in the brain in a large variety of ways, only one of which is big pieces of cortical tissue. In this sense, there could in fact be shared mechanisms between language and code (e.g. oscillatory dynamics, connectivity patterns, subcortical structures), but these mechanisms might not be aligned with the cortical territory associated with language-related brain regions. The authors should spend much additional time discussing these alternative possibilities.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

This was co-submitted with the following manuscript: https://www.biorxiv.org/content/10.1101/2020.05.24.096180v3

Summary:

The remit of the co-submission format is to ask if the scientific community is enriched by the data presented in the co-submitted manuscripts together more so than it would be by the papers apart, or if only one paper was presented to the community. In other words, are the conclusions that can be made stronger or clearer when the manuscripts are considered together rather than separately? We felt that despite significant concerns with each paper individually, especially regarding the theoretical structures in which the experimental results could be interpreted, that this was the case.

We want to be very clear that in a non-co-submission case we would have substantial and serious concerns about the interpretability and robustness of the Liu et al. submission given its small sample size. Furthermore, the reviewers' concerns about the suitability of the control task differed substantially between the manuscripts. We share these concerns. However, despite these differences in control task and sample size, the Liu et al. and Ivanova et al. submissions nonetheless replicated each other - the language network was not implicated in processing programming code. The replication substantially mitigates the concerns shared by us and the reviewers about sample size and control tasks. The fact that different control tasks and sample sizes did not change the overall pattern of results, in our view, is affirmation of the robustness of the findings, and the value that both submissions presented together can offer the literature.

In sum, there were concerns that both submissions were exploratory in nature, lacking a strong theoretical focus, and relied on functional localizers on novel tasks. However, these concerns were mitigated by the following strengths. Both tasks ask a clear and interesting question. The results replicate each other despite task differences. In this way, the two papers strengthen each other. Specifically, the major concerns for each paper individually are ameliorated when considering them as a whole.

The concerns of the reviewers need addressing, including, specifically, the limits of interpretation of your results with regard to control task choice, the discussion of relevant literature mentioned by the reviewers, and most crucially, please contextualize your results with regard to the other submission's results.

Reviewer #3:

In this interesting study, the authors explored the effect of five consecutive generations of high-fat high-sugar diet (WD) in mice and their offspring's metabolic performance under a normal chow diet. It is very interesting to find that the chow-diet-fed progenies from these multigenerational western-diet-fed males develop a "healthy" overweight phenotype (which means without problem of glucose metabolism and fatty liver abnormalities) that persist 4 subsequent generations. In parallel, the authors also performed zygotic sperm RNA injection using sperm RNAs from the WD-fed males (both from first generation and five generations of feeding) and showed that the sperm RNA indeed induce offspring metabolic phenotypes in F1 mice and some phenotypes persist to F2-F3, but none persist to F4, which is different from the mating induced phenotype (last 4 generations). The study is overall well-performed and the comprehensive examinations (especially on phenotypes) represent an advance to the mammalian epigenetic inheritance field. I have a few concerns and suggestions for further improvement.

1) In the abstract, I strongly recommend the authors to clarify what is a "healthy" overweight phenotype, which in the current paper means normal glucose metabolism and without fatty liver. This will make the information in the abstract more informative and precise. In fact, this is the major novel discovery in the phenotypic exploration, not only for social-medical implications, but also from the perspective of evolution. It looks like the five-generational western-diet-fed males have evolved to develop a protective mechanism in glucose and liver fat metabolism that can be inherited by the offspring. The underlying mechanism is intriguing and worth exploring in the future using this model. More extensive discussions on the social-medical and evolutionary aspects could be included.

2) Regarding the phenotype induced by sperm RNA injection, the description should be more precise as the current description is not all consistent with the data presented. In Figure.4, some parameter changes persist to F2-F3, this already suggests transgenerational inheritance rather than merely intergenerational transmission. The more precise description should be that sperm RNAs can unequivocally induce intergenerational phenotype, but may induce some transgenerational features - although the effect is weaker than the effect induced by whole sperm. In fact, in a previous study using a mental-stress induced model, sperm RNA injection can also induce phenotype in both F1 and F2 generations (Nat Neurosci. 2014 May;17(5):667-9.).

3) The sperm small RNA analysis part (Fig. S4) is relatively weak. The datasets generated are in fact quite valuable as they include the sperm from the control diet, first-generation WD and the Fifth-generation WD. This is an opportunity to explore the difference especially between the first-generation WD and Fifth-generation WD as no one has done this before. The current data analyses are crude and did not show these differences in an informative way. It is needed to at least provide the overall length distribution of each datasets with the annotation of different types of small RNAs. The authors have shown some difference regarding miRNAs and tRNA-derived small RNAs (tsRNAs) in Fig.S4, it would be interesting to also look at the rRNA-derived small RNAs (rsRNAs) because rsRNAs are also extensively discovered in both mouse and human sperm and these sperm rsRNAs are sensitive to dietary changes (Nat Cell Biol. 2018 May;20(5):535-540; PLoS Biol. 2019 Dec 26;17(12):e3000559.), closely associated with mammalian epigenetic inheritance and thus represent a component of the recently proposed sperm RNA code in epigenetic inheritance (Nat Rev Endocrinol. 2019 Aug;15(8):489-498). The reanalysis of the datasets could be done by SPORTS1.0 (Genomics Proteomics Bioinformatics. 2018 Apr;16(2):144-151.), which provide the annotation and analyses of miRNAs, tsRNA, rsRNAs and piRNAs that have been used in the above mentioned publications (Nat Cell Biol. 2018 May;20(5):535-540; PLoS Biol. 2019 Dec 26;17(12):e3000559)

Reviewer #2:

Raad et al. examined the effects of multigenerational paternal exposure to an obesogenic diet on epigenetic and metabolic alterations at somatic and germ cell levels. The experimental work addresses an important question. The findings are intriguing that sperm mRNA and natural crosses have different effects on offspring metabolic states. The major tissue of interest explored was WAT. Fat cell size, no and gene expression were reported. The intriguing thing about these data is that the sperm RNA microinjection did not fully recapitulate the effect across multiple generations - there is little explanation of potential mechanisms.

There is no detailed coverage of the gene changes, small RNAs, piRNAs etc observed and the pathways implicated. This would be a welcome addition.

As this is such a complex design, more overall schematics would be helpful.

Number of mice per group ranges widely, and it is unclear how many matings this represents. Fig 3 legend states 4 WD1 and 9 WD5 males from different littermates were mated with CD females - again, unclear - do you mean from different litters? Numbers shown in panel A do not seem to concur with those in panels B, C

Figure 1 shows outcomes for WD 1,2,3,4,5 and largely focuses on gWAT. Gene expression changes are only briefly summarised. Only 1 CD generation is represented.

It is unclear why mice were studied at the various ages- eg Across data sets, ages shown range from 10 weeks, 12 weeks, 16 weeks, 18 weeks. Note there are inconsistencies regarding figure formats and some details are missing, which makes it hard to understand what the authors found. Fig S3 and S5- no n values given. Labels in S4 D, E hard to follow.

In several of the figures, it is not clear what the significance (*) is being compared to - is it always CD? Eg Figure 3, Figure 4

It appears that variability increases from WD1 to WD5- with larger ranges evident- is this why n increases across generations? And is this a consistent observation across paternal studies of this kind?

The effect of paternal WD on BW, GTT and adiposity is relatively larger in mice than rats- have the authors considered species differences?

One page 10 the authors state that the diet used is not associated with hepatic steatosis - but I would have thought there was good evidence of this occurring in mice, over the timeframe described here.

The intriguing thing about these data is that the sperm RNA microinjection did not fully recapitulate the effect across multiple generations - there is little explanation of potential mechanisms.

It is surprising that there is no detailed coverage of the gene changes observed and the metabolic pathways implicated. The story is undersold.

Reviewer #1:

While this study is focusing on an interesting hypothesis and attempting to address the molecular mechanisms at play, there are numerous flaws in the study design and the statistical test that prevail from drawing conclusions.

1) In line 72, the authors state that "the average body weight of the WD-fed male mice increased gradually with multigenerational WD feeding", however, the results of the test indicating gradual increase is not reported. As described in the legend of Figure 1, the test performed tested differences in body weight between the control group and each individual generation, not the generations to each other. Visually, it rather seems that in fact, body weight was not gradually increased for instance, comparison of WD1 and WD3, or WD2 and WD5, does not support the "gradual increase" in body weight that the authors are claiming.

2) There is a lack of clarity in the methods in regards to numbers of animals used in each generation, the number of founders, and what constitutes the control group. In the legend of Figure 1, it is stated that 5 males were used from WD2 and on. However, the method section states "(...) 4 to 6 independent males of WD1 group". The reviewer assumes that the authors know how many animals were used in the WD1 group, and that the authors meant 4 to 6 animals per WD generation. However, if the details indicated in the legend of Figure 1 are accurate (5 fathers per group from WD2), how is it possible that 4 to 6 animals were used? The reviewer suggests to clarify this in the text, as well as in a more detailed experimental setup diagram stating the number of fathers in each generation, the number of offspring studied in each litter, and the total number of offspring studied for each generation.

3) In Supplemental Figure 1I, the CD1 group appears to be composed of 7 individuals and the CD2 group of 10 individuals. This is not consistent with the numbers reported in Figure 1A (10 in CD1 and 13 in WD3) and Figure 1B (22 visible dots). It is thus difficult for the reviewer to trust that body weights were truly compared between all animals in CD1 and CD5. Regardless, the reviewer is intrigued by the choice of the authors to only study control animals from the first generation (CD1), and the fifth generation (CD5) offspring, as they describe in the methods that, for the control group, they followed the same procedure as the WD group, which should have led to the generation of control animals in all F1, F2, F3, F4 and F5 generations. The authors should clarify on this, and if they indeed generated these animals, they should use body weight data in each generation of controls and compare them to their respective generation WD group (i.e. CD1 to WD1, CD2 to WD2 etc..). By having different sample size in the various groups, the authors are biasing results of the statistical test being made, as greater sample size is likely to compare statistically different than a group with lower sample size (as with CD(22 observations) and WD2(12observations) in Figure 1B, but also with the RNA-seq results). In the same line, there were more animals studied in WD4 and WD5 compared to WD1-3 which is likely biasing statistical analysis. Again, if the study design described in the methods section is accurately reported, it implies that an average of 3 offspring per fathers were used in WD1-3, and 8-10 (a full litter) for the WD4-5.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript. David E James (The University of Sydney) served as the Reviewing Editor.

Summary:

In this manuscript, Raad and colleagues exposed male mice to a western diet before conception for 5 consecutive generations and measured body weight, adiposity and various metabolic markers in the offspring. Sequencing of small RNA in sperm from founders identified several differentially expressed tRF and miRNA species. Microinjection of RNAs recapitulated some, but not all effects on body weight and metabolism. The authors report an aggravation of adiposity along generations and a phenotype that persists for 4 consequent generations. Such persistence of phenotype was not observed in animals originating from microinjection of total RNAs, suggesting other epigenetic mechanisms are at play in the persistence of phenotype. Overall the studies were considered to be of interest by the referees but one major overarching problem identified by them concerned the study design and the statistical analyses that limited interpretation of the study. These issues need to be seriously addressed by the authors. These and other points are listed below.

Reviewer #2:

Overall, I think this is a creative study, with very interesting findings. A major weakness is that the interpretations seem a bit exaggerated and alternative interpretations not considered.

Using a creative paradigm of perceptual filling-in, the authors show that increased attention (indexed by a reduction in alpha power over central-parietal locations, and supported by previous psychophysics studies) is associated with perceptual filling-in, and the phenomenal disappearance of targets. By tagging targets and surround with different frequencies, they show that SSVEP elicited by targets increases at the time of perceptual filling-in.

These results suggest that SSVEP, thought to index the content of visual perception in previous binocular rivalry studies, can be dissociated from conscious perception in this paradigm, and instead reflect attention.

While the results are interesting and novel, they are perhaps not as surprising as the authors present them to be. Given that previous studies have shown a clear connection between SSVEP and attention (e.g. Ref 14 cited by the authors), these results show that when attention and awareness are dissociated (as the last author has nicely demonstrated/argued previously), SSVEP goes with attention.

These results do not demonstrate that all sensory-cortical activity goes along with attention instead of awareness, as the authors' abstract/significance statement/discussion suggest to be the case. E.g., in the abstract/significance statement, the authors only state "neural activity" or "neural response", instead of specifically SSVEP, which can be misleading. Similarly, in discussion, it remains a possibility that other types of neural activity (e.g. spiking rate or recurrent activity) in sensory cortex correlates with the vividness of conscious experience, which would in principle be consistent with first-order or GNW theories.

An analysis comment:

In discussion, the authors mention "As more targets disappeared and presumably drew attention, both the duration of their absence and strength of target SNR increased."

The duration effect, shown in SI, is not referenced in the main text as I could find. In Fig. 2, in addition to investigating SSVEP's relation with the number of disappeared targets, the authors could also test its relation with the duration of PFI.

Reviewer #1:

General assessment:

In this paper, Davidson et al. characterize the neural correlates of visual disappearance during perceptual filling-in (PFI) using steady-state visual evoked potentials (SSVEPs). They show that target disappearance actually leads to an increase rather than to a decrease of the target SNR. This finding is potentially of importance. However, the current version of the manuscript does not provide enough details regarding the underlying assumptions and neural mechanisms. The results should also be better described, interpreted and compared to the existing literature. I list my most substantive concerns below.

Substantive concerns:

1) I was a bit frustrated to see that almost no discussion about the neural mechanisms underlying the results is provided. It seems important to better explain the cortical processes involved (e.g. the authors could compare more carefully their results with those obtained in macaque electrophysiology by De Weerd et al. 1995).

To go further along this direction, one possibility would also be to analyse the SNRs at the intermodulation frequencies (I see in supplementary figure 3 that responses at F2-F1 = 5Hz are significantly above noise). This would permit to characterize and discuss the interactions between the neural responses corresponding to the processing of the targets and to the surround (see e.g. Appelbaum et al., 2008).

2) When I read the whole manuscript, I had the feeling that the analysis of the SNR change latencies (which is currently described in the supplements) would deserve to be more documented and to appear in the main document. The finding that changes in background SNR precede changes in target SNR is an important result which clarifies the temporal sequence of neural activations. That would also be nice if the authors could determine when the SNR change corresponding to the inter-modulation product (e.g. at F2-F1) appears (see my first point above).

3) To better characterize the difference between the responses to PFI vs to phenomenally matched disappearances (PMD) and support the claim that target-SNR decreases rather than increases during PMD (l. 170), that would be great to show the target-SNR changes around button press (i.e. the equivalent of figure 2 b & e) for PMD.

4) The target disappearance during PFI is associated with an increase of SNR and therefore, SSVEPs in this case do not reflect conscious perception. But does it necessarily imply that this target-SNR increase reflects attention instead? The authors base their interpretation on previous studies (Lou, 1999; De Weerd et al., 2006) where attending to target feature increased PFI probability (which I think is not exactly equivalent to the PFI magnitude reported here) and also on the correlation they found between target-SNR and evoked alpha. However, these are indirect evidences and in their experimental protocol, attention was not directly manipulated (as e.g. in Morgan et al., 1996 or Müller et al., 2006). I would suggest being a little bit more cautious with this interpretation in the manuscript.

5) Before this study, other groups looked at the dissociation between attention and perceptual awareness (among others, see e.g. Wyart & Tallon-Baudry, 2008; 2009; Koivisto et al., 2009; Norman et al., 2013). A deeper review of the existing literature on this topic (in the introduction and/or discussion) would permit to better understand what is already known and also to provide leads for future investigations.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

This manuscript is in revision at eLife.

Summary:

This manuscript describes a human EEG study which aims at characterizing the neural correlates of visual disappearance during perceptual filling-in (PFI) using steady-state visual evoked potentials (SSVEP). The authors report that target disappearance leads in this paradigm to an increase rather than to a decreased SNR of the target SSVEP. The authors interpret this "neural correlate of invisibility" as an empirical challenge for existing theories regarding the relationship between SSVEP and conscious perception. The two reviewers have found the study to be creative and its findings to be of potential importance for the field. However, they have also raised concerns regarding the interpretation of the findings proposed by the authors, which would require additional analyses to be supported by the data and a more extensive account of the existing literature on the relationship between the neural correlates of visual awareness and attention. There are also concerns regarding the number of subjects included in the analyses which should be clarified. The paragraphs below describe the main concerns that have been discussed among reviewers and the reviewing editor.

Reviewer #3:

In this manuscript, Robinson et al., identified alternative first exon (AFE) switching events conserved between mouse and human following macrophage inflammation. Using short and long-read sequencing, the authors identified a few unannotated transcription initiation sites (TSS) that are specific to an inflammatory response. Among those, they centered on an unannotated TSS in the Aim2 gene that drives expression of a novel isoform regulated by an iron-responsive element in its 5′UTR.

While previous work had documented crucial AFE switching events in many other biological contexts, Robinson et al. presents here an interesting AFE switching event that can have potential implications for our understanding of the molecular regulation of the innate immune response. I would expect further progress on global mechanisms and biological relevance of these AFE switching events, as well as evidence that the AFE are truly first exons/TSSs.

Substantive concerns:

1) Are the AFEs truly first exons/TSS? While both short-read and long-read sequencing detected changes in alternative splicing choices, neither of those are optimal methodologies to analyze first exons. Therefore, I suggest to use a more specialized method to identify (and quantify) more accurately the usage of first exons. Globally, cap analysis of gene expression (CAGE) would be ideal. For validation of specific AFE changes, the qPCR technique has a few issues. First, it does not have nucleotide resolution, so the authors should not refer to TSSs if they used this technique for validation. Second, many downstream first exons are also used as internal exons in other isoforms. There is not a direct technology to analyze specifically first exons/TSSs here. Also, RNA-sequencing technologies, depending on their depth, can definitely miss specific isoforms. Considering a low coverage in 5'end of genes in RNA-seq analysis, this is particularly important for first exons. A qPCR would only analyze the well-known TSSs. Thus, 5'RACE or a similar technology should be performed to assess the relative usage of AFE specifically.

2) Global mechanism. The authors assumed that the mechanism of AFE switching is generated by transcription initiation and looked for transcription factors binding and chromatin structure modifications in promoters. However, they did not rule out the possibility that the global switching effect is a post-transcriptional regulation, such as differential mRNA stability. A transcription initiation measurement (e.g., 4SU metabolic labelling) is necessary to demonstrate that the changes in AFE usage are co-transcriptional. In addition, in terms of their ATAC-Seq analysis, the chromatin structure changes in promoters can be the cause or consequence of transcription initiation. Thus, it should not be listed as one mechanism driving the expression of AFE events (line 145). Also, to demonstrate a mechanism based on transcription factor binding more than 2 transcription factors should be considered. In any case, the expression patterns of the transcription factors considered are not clear. As a minor note, the bioinformatic analysis of the two promoter regions driving the isoforms of Aim2 (line 156) is not explained in the method section.

3) Biological relevance. Could the authors evaluate whether the translation regulation of Aim2 based on its AFE switching is a more generalized phenomenon? Are there any global gene regulation changes triggered by the other genes with significant changes in AFE usage?

Reviewer #2:

This manuscript by Robinson et al. presents an interesting and timely analysis of a wealth of transcriptome data upon immune stimulation. The unique combination of long-read Oxford Nanopore and short-read Illumina high-throughput sequencing across both human and mouse samples presents an opportunity for many interesting inter-species immune response comparisons, as well as elucidation of full-length transcript information. This paper is well-written and has interesting validation and discussions regarding Aim2. My major concern is that the paper seems to narrow in on the characterization of Aim2 and class of RNA processing changes (alternative first exons) quite quickly without really delving into the rest of the data and how they arrived there. Below are my major/minor comments and suggestions:

1) I would have liked the authors to provide more insight into how they honed-in on specifically talking about first exon changes, by discussing more of the other RNA processing changes they found. There is cursory mention in the text and figures of other alternative exon or splice site changes. Firstly, other studies (including those referenced by the authors) have found hundreds of RNA processing changes genome-wide upon immune stimulation - especially of cassette exons, alternative splice sites, and last exon/3'UTR changes. However here, the authors only find tens of changes (Fig 1B). Are they underpowered to identify changes and can they do any sort of analyses to show that they are sufficiently powered (# of sequencing reads & junctions, complexity of reads, etc)?

2) Similarly, I would also be interested in seeing an analysis indicating whether the 50 AFE events that overlap between the long-read and short-read sequencing analyses is a statistically significant overlap. Particularly, how many overlapping events would be expected given the difference in quantification power between the two methods? How many real AFE differences might the authors be missing because the long-read sequencing methods often do not have the power to identify them (ie. lower expressed genes in one or the other condition, thus dropout of isoforms and perhaps fewer isoform differences for differentially expressed genes).

3) Second, for the non-AFE changes that they did find, there is very little discussion about what those changes might represent. Specifically: (a) how many changes are validated with long-read data?, (b) is there any insight into specific domains being included/changed, especially using the long-read data?, (c) how many of these non-AFE changes overlap between species? and (d) which types of genes show higher overlap between species and what are their characteristics (binding sites, etc)? To my knowledge, this is the first study that is really designed to properly really look at the conservation of splicing or RNA processing changes after immune activation, so I would love to see more analysis and discussion of this aspect genome-wide.

4) The authors define significant splicing changes as those with a p-value <= 0.25 and |dPSI| >= 10. I'd like some more clarification on whether this is an adjusted p-value (BH, FDR, or some other multiple test-corrected p-value). Especially if this is adjusted, I find it surprising that the authors are choosing such a liberal statistical confidence level and that even with such a liberal threshold, they are only getting tens of significant events. I would like the authors to at least show these same trends across multiple p-value thresholds or with rank threshold analysis (top 5%, top 10%, top 20%) to show biological trends.

5) The authors introduce their long-read sequencing data by mentioning that they wanted to identify "additional splicing events that are not captured using short-read sequencing." They then go on to only talk about novel first exon events identified with the long-read sequencing data. Did they identify any other non-AFE events in using the long-read that could then be quantified with the short read data? And second, how do they quantify confidence for novel AFE isoforms, when long-read data seems to have lots of issues with properly sequencing the terminal ends of transcripts (particularly the 5' end when polyA primed, as occurs in ONT DirectRNA sequencing)? They mention the use of ATAC-seq data to show putative promoter support, but mention at one point in their methods that ATAC regions within 10kb of AFEs are considered. This seems like it could be a rather large region to be sure that the ATAC peak is specific to a novel AFE - what is the average distance between AFEs? Finally, I would love to also see the incorporation of CAGE-seq data (or other 5'end data) to validate the specific AFEs sites - which I believe the FANTOM consortium has across many human and mouse tissues.

Reviewer #1:

Our understanding of the transcriptomic impact of innate immune signaling remains incomplete. Here Robinson et al., use both long and short read RNA sequencing to gain further insight into LPS-induced changes to mRNA isoform expression in human and mouse macrophages. Their studies report the novel observation that the most common change in isoform expression is alternative use of the first exon. Such changes are indicative of transcriptional regulation, and is thus consistent with the known impact of innate immune signaling on activation of multiple transcription factors. Despite some minor concerns with details of the study, as enumerated below, this is a well-executed and important study that will be of interest and importance to many studying innate immunity, as well as those interested in gene regulation.

Major comments:

1) In some ways this is minor, but the authors should be careful to not describe alternative first exon use as alternative splicing. While a novel splice junction is created, mechanistically this is driven by changing transcriptional regulation, and then splicing occurs in the only pattern available to that TSS. In general this is described appropriately in the manuscript, but at a few points there is confusing terminology.

2) An interesting and somewhat surprising point in the manuscript is that 50% of the AFE events don't show an overall change in gene expression. For Aim2, which does change, the authors show that the AFE change is due to activated use of the unannotated TSS in LPS-stimulated cells. For those genes for which AFE use doesn't correlate with a change in gene expression (e.g. Ncoa7, Rcan1, Ampd3 - Fig S3) is there still transcriptional activation of one TSS and transcriptional silencing of the other? In other words, is there coordinated regulation of the two TSSs to ensure overall message abundance doesn't change, or does activation of one TSS inherently shut off the other (more akin to splice site competition in traditional AS)?

3) The data suggesting that an IRE regulates translation of the induced 5'UTR is compelling, but more work should be done to confirm. Most importantly, the experiment in Figure 4J should be repeated with the deltaIRE version of the unannotated UTR. Also is the IRE regulation controlled upon LPS-stimulation, or just the presence of the IRE element? In other words, what is the distribution of the annotated and unannotated isoforms in the polysome in the absence of LPS (i.e. repeat 4P without LPS)? Can the authors comment on whether the level of iron or the activity of IRP1/2 change in LPS-stimulated cells?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript. Timothy W Nilsen (Case Western Reserve University) served as the Reviewing Editor.

Summary:

There was significant enthusiasm for the work. However, it seems that considerable effort including additional experiments will be required to firm up the conclusions.

Reviewer #2:

The authors set out to investigate whether the cerebellum plays a domain-general and predictive role in speech perception. They leveraged the online platform, Neurosynth to conduct a meta-analysis of fMRI studies to compare the activation results between speech perception and speech production studies. They find that there are distinct as well as overlapping regions of perception- and production-related activity in the cerebellum, and that each of these regions has a distinct connectivity fingerprint with the cerebral cortex. They mined text data from thousands of studies in Neurosynth to determine which labels best explain these speech-perception and speech-production activity patterns. They find that cerebellar regions activated by speech-perception, speech production, and their overlap, are also associated with cognitive and motor processes beyond the domain of speech and language. On the basis of these results, they argue for a domain-general view of cerebellar processing.

One of the most interesting findings in this paper is that speech-perception and speech-production tasks elicit both distinct and overlapping activity patterns in the cerebellum. It has long been known that the cerebellum is activated by speech processing, however, it has been less clear to what extent these two processes (perception and production) differ in their activation patterns. Importantly, the authors also show that these distinct and overlapping networks in the cerebellum display connectivity patterns with corresponding regions of the cerebral cortex. However, there are some major concerns.

One of the central take-aways from this study is that prediction is a domain-general mechanism that supports speech perception in the cerebellum. The authors argue for domain-generality on the basis that regions activated by speech perception and production in the cerebellum are also activated by a wide range of non-speech tasks. However, I was a bit confused by this argument. It is my understanding that the same region of the cerebellum can be activated by many different tasks, and that each task will demand its own computational description. However, that does not necessarily provide evidence for domain-generality. What could point to domain-generality is a function/computation that explains the diverse set of computations required by the tasks. That speech-related regions of the cerebellum are also activated by a range of non-speech tasks does not (in my opinion) support a domain-general view of cerebellar processing.

Another take-away from this study is that the cerebellum plays a predictive role in speech processing. Prediction is at the core of many theories of cerebellar function (e.g., internal models, error-based learning), of course, it is a very broad term that is not necessarily unique to the cerebellum. The authors hypothesize that, "if the cerebellum is involved in prediction during natural speech perception, there should be a greater amount of activity throughout the brain when the cerebellum is not active during this task". The authors compare two different sets of speech perception studies, those that report cerebellar activation and those that do not. They then compare the level of activation in cortex versus cerebellum for both of these study types. They find that cortical activation in the "no cerebellum" studies is increased relative to cortical activation in the "cerebellum active" studies. On the basis of these results, they infer that the cerebellum must be involved in prediction and that prediction results in metabolic savings (i.e. decreased activity in cortex). However, why did the speech perception tasks in the "no cerebellum" studies not activate the cerebellum. Did they not involve prediction in some capacity? There are likely other reasons that there was increased cortical activation in the "no cerebellum" studies that are unrelated to the absence of cerebellar activation.

It is also not clear to me why speech perception studies that involved passive sound and music perception were included. How are tones related to speech perception? It would have been helpful if the authors had shown consistency across the different modalities (i.e. speech, sounds, instrumental music, and tones). I'm also assuming that the speech production studies were not matched across these four groups. Couldn't differences in activity patterns arising between the two study types potentially be attributed to sounds, instrumental music, and tones present in the speech perception studies?

Reviewer #1:

I have very much enjoyed reading this piece of work, investigating the role of the cerebellum in non-motor functions using a meta-analysis and focusing especially on speech perception and predictive processing. I believe that this work is highly relevant to the field and will contribute considerably to the understanding of cerebellar functioning.

I appreciate the careful description of the methods and the aim to challenge the hypotheses through additional testing. However I have only very few major concerns, which however I believe are all addressable:

1) From page 8, but mainly throughout the whole paper: I am concerned with the inclusion of 22.5% of instrumental music or tone studies. The paper's overall focus is on speech perception and production, and the authors always only refer to "speech" throughout the manuscript. Whereas the inclusion of speech sound perception studies can be easily justified, the inclusion of tone perception is highly different if the focus lies on speech, e.g. due to the varying complexity of the input signal.

Although the authors address this issue in the limitation section, it weakens the overall impact of the findings (as they also state, but downplay). For consistency the authors should exclude tone processing studies from their analysis; as the role of cerebellum in contributing to processing of time and potential motor sequencing is widely discussed in the literature (see Gordon et al 2018, PLoSOne, https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6242316/ ). As I very much support the ideas presented in the paper I believe a clear differentiation between perception of speech and perception of music is crucial for making a convincing argument regarding the role of the cerebellum in "passive" predictive language perception, if that is the focus of the paper. It would be interesting, however, if the regions for perception differ when including music studies compared to speech studies only. A separate analysis of the tone studies might not be feasible for 20 or so studies.

Generally, the authors should either refrain from setting the focus on "speech perception" when the paper clearly focuses on "speech and tone perception" (or more generally "non-motor auditory perception", which is, by the way, not problematic at all, as the findings support a domain-general function of cerebellum. In that case speech perception should not be mentioned singularly in the title. However, if the authors wish to make a statement on speech perception, then they should exclude the tone perception studies from the analysis.

2) Relatedly, page 5 last sentence, whereas I do agree with this approach and appreciate effort to test the own hypothesis, this approach is missing the testing of an alternative hypothesis: Could the decrease of general cortical activation be linked to the greater activity of a different region, other than the cerebellum. This should be at least discussed.

3) Page 16/20: To test their hypothesis the authors compare the cortical activation of studies that report cerebellar activity and those that don't. If the cerebellum had this domain general function in predictive processing why would it not be active in some studies? Was there a systematic difference between the two sets of studies, and, as furthermore argued, did those studies that did not activate the cerebellum use indeed speech in novel contexts? A further investigation of the difference between the two sets of studies would be helpful in support of the argumentation.

Preprint Review

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Summary:

The importance of cerebellum in cognition generally, and in speech processing more specifically, are timely and interesting questions, and metaanalysis is a helpful tool. The paper is clearly written. However, in the opinion of at least one reviewer and the Reviewing Editor, neither of the two stated aims of the paper were satisfactorily achieved.

The stated aims were to demonstrate:

1) "that the cerebellum plays a domain-general role in speech perception-that is, a role that is not inherently speech specific." However, just showing coactivation with other tasks does not indicate domain-generality; for a variety of reasons. First, this conclusion is not supported because of the computational specificity issue raised by Reviewer 2, and second, coactivation in brain imaging can be an artifact of the spatial resolution of BOLD, and of preprocessing -- it does not necessarily imply coactivation at a neural level.

2) "that the domain-general role played by the cerebellum and its connections during speech perception is related to prediction." Two lines of evidence are offered for this. 1) the reverse inference that regions identified in the paper are associated in Neurosynth with the term 'prediction'; and 2) that there was more cortical activity when the cerebellum was inactive. Just because accurate prediction should reduce activity, doesn't mean that a reduction in activity signifies prediction.

Reviewer #3:

Otsuka et al. report the characterisation of three temperature sensitive alleles of genes which prominently lead to overproliferation of cells in lateral root primordia. Interestingly this phenotype which is not underpinned by alteration of the auxin pattern, can be phenocopied by treatment with ROS and by interfering with the mitochondrial respiratory chain. This reveals that ROS modulate cell proliferation in the LR. The cloning and biochemical characterisation of the genes affected, reveal that all three encode enzymes involved in mt RNA processing, that perturb the production of certain components of the mitochondrial electron transport chain.

This is an excellent manuscript that points to a new and very interesting link between primary metabolism and cell proliferation in lateral roots. It is remarkably well written and presented. The conclusions are fully supported by the data. As it is the case for exciting new discoveries, they raise a lot of questions and this manuscript is no exception. It would be very interesting for future work to uncover the nature of the molecular link between ROS and cell proliferation and why are LR so sensitive to this. It'd be eventually interesting to speculate whether the reported existence of an hypoxic environment in the centre of the LRP has to do with this.

The one point I would like to hear some comments from the authors about relates to the growth conditions used to reveal the phenotype at restrictive temperature. They mention that they use explant culture on RIM (characterised by high glucose and high 2.5µM IBA). What's the penetrance of the phenotype in standard (1/2 MS, 1% sucrose, no additional auxin/IBA)?

Reviewer #2:

The manuscript by Otsuka and coworkers, describes the mapping of the mutations in rrd1, rrd2 and rid4 causing the temperature sensitive lateral root morphogenesis defects (fascinated LR meristem). Interestingly, the respective mutated genes all map to genes involved in mitochondrial mRNA processing, mRNA deadenylation, and mRNA editing. The authors propose that defective ROS homeostasis is causal to excessive cell proliferation in the lateral root primordia, and associated fasciation phenotype. Overall the manuscript is well-written, and is overall convincing with respect to characterization and mapping of the mutants, and the importance of RNA editing in mitochondria for the mutant phenotypes. I am not yet entirely convinced about the link to ROS production and the lateral root morphogenesis defects.

1) The fascinated LR phenotype is reminiscent of mutants defective in coordination of LR emergence, such as CASP:shy2 (Vermeer et al). Suggesting that defective signaling in LR overlaying layers, could be causal to the observed phenotype. However, the phenotyping presented in this manuscript does not allow to assess this. A detailed staging of LRPs would be required, and/or an analysis of the LRP developmental dynamics using a root bending assay.

2) Furthermore the expression domain analysis shows clear expression in LRPs. However, I suspect expression of at least RID4-GFP in LRP overlaying layers. However, the resolution of the picture, and interference of the bright PI counterstaining in Fig2B preclude a thorough assessment of this.

3) The colocalization analysis in Fig 2D and E is not very clear. The mitotracker signal is set a bit too weak, making it difficult to assess the distinction between the GFP signal and the overlapping (yellow) signal). This could be amended by using different LUTs (also green/reds are not great for colorblind readers). Of note is the presence of a relatively large structure labeled by RDD1-GFP, that is not colocalizing with mitotracker, suggesting it also localized to another subcellular compartment. Therefore, colocalization should be addressed more quantitatively, also using additional organellar markers. Additionally, the mitochondrial localization could be further supported by western blot on purified mitochondria.

4) The accumulation of polyadenylated transcripts in Fig3D, seems to also display a temperature sensitivity in the WT. Why was this assay not done using a quantitativePCR, that will allow for better appreciation of temperature component.

5) In contrast to the LR phenotyping as displayed in Fig 1, the LR phenotyping in Fig4 is done in a completely different way. Why not use a uniform way to quantify. As it was done now, the suppression of rdd1 by ags1 mutation, is not very convincing, as the rrd1 phenotype is nearly abolished in the Col-0 introgressed line (Fig 4 B), suggesting that the rrd1 phenotype is sensitized in the Ler background.

6) While the authors focus on the LR morphology phenotype in the mutants, there is also a prominent effect on primary root growth that is not described. However, this phenotype does not seem to be very ecotype-specific, and is rescued in the ags1 background. A small phenotypic characterization of the primary root phenotype could thus be beneficial for the manuscript, and it’s wider relevance for development.

7) Fig5. -> explain arrowheads in B, in the legend. Bar charts using mean + and - SD should be avoided when you do not have many data points, as in D and F (N=3 and 2). Better to show the raw data. Loading controls are missing for Fig5 C and E.

8) The section about ROS is all based on ROS related pharmacology. However, ROS levels in the mutants were not assessed, making it difficult to use the pharmacological treatments to interpret the origin of the mutant phenotypes.

9) What is the link to the temperature sensitivity. Are these mutants hypersensitive to ROS inducing treatments?

10) While the role of ROS in LR development is key to the proposed model, the authors did not introduce what is the state of the art about ROS in lateral and primary root development.

11) In their model the authors might need to discuss whether or not ROS from the LRP could act as an intercellular coordinative developmental signal.

Reviewer #1:

This study continues research started by Professor Munetaka Sugiyama and his laboratory who identified about 20 years ago, or so, very interesting temperature-dependent fasciation (TDF) mutants affected in lateral root primordium (LRP) morphogenesis. The authors identified and reported in this study genes responsible for the mutant phenotype of the root redifferentiation defective 1 (rrd1), rrd2, and root initiation defective 4 (rid4). Intriguingly, all the genes are involved in RNA processing. Detailed analysis of the role of RRD2 and RID4 in mitochondrial mRNA editing and RRD1 in poly(A) degradation of mitochondrial mRNA make this work a solid and substantial study. The fact that pharmacological treatments of wild type seedlings by mitochondrial electron transport inhibitors can phenocopy the fasciated LRP phenotype is really fine. Similarly, the experiments with paraquat and ascorbate are very interesting. The main conclusion of the work (that LRP morphogenesis is linked to mitochondrial RNA processing and mitochondrion-mediated ROS generation) is novel and significant. I think this is an important step forward in our understanding of LRP morphogenesis.

I see only one main conceptual or interpretation problem.

The authors conclude that "that mitochondrial RNA processing is required for limiting cell division during early lateral root (LR) organogenesis" (line, L, 51). A similar statement appears on L101-103 where the authors postulate that TDF encode "negative regulators of proliferation that are important for the size restriction of the central zone during the formation of early stage LR primordia". Again, similar statements appear on L151-152, 344, and in the section of discussion "Mitochondrial RNA processing is linked to the control of cell proliferation", especially where the authors say about "the control of cell proliferation at the early stage".

To my opinion, the above conclusions are arguable and cannot be accepted. To conclude about excessive cell division, the number of anticlinal divisions must be estimated per founder cell. This analysis has not been performed. The fact that at early stages LRPs are wider in the TDF mutants suggests that a greater number of FCs in the longitudinal plane participate in LRP formation. So, if this is correct, the mutations apparently affect control of lateral inhibition, and TDF genes are negative regulators of lateral inhibition. This question should be further investigated, but currently a more careful interpretation of the results is required. Also, if TDF genes encode "negative regulators of proliferation" then more frequent divisions would occur in the mutant. This question was not addressed either. If more frequent cell division is expected in early stage LRPs, this should result in formation of smaller cells. In accordance with Fig. 1D of this study and Figs. 1b and 3a of Otsuka and Sugiyama (2012), this is not the case. Contrary, it seems that at the same developmental stage there are lower numbers of cells per unit of volume in the mutants compared to wild type. Another, possible explanation of the TDF mutant phenotype, in addition to lateral inhibition, is abnormal establishment of stem cell identity or affected stem cell function. Therefore, the mechanistic explanation of the link between TDF gene action and the respective mutant phenotype is not satisfactory. The interpretation given can be corrected and carefully rephrased throughout the text.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 3 of the manuscript.

Summary:

The reviewers were very enthusiastic about your work. They identified some shortcomings, but most of it could be addressed by text edits. The reviewers were less convinced about the envisioned link to reactive oxygen species (ROS). Ideally, you should consolidate this aspect by depicting the mis-regulated ROS in the mutant, and its restoration in the suppressor double mutants (e.g. by staining).

Reviewer #3:

The manuscript by Hutchings et al. describes several previously uncharacterised molecular interactions in the coats of COP-II vesicles by using a reconstituted coats of yeast COPI-II. They have improved the resolution of the inner coat to 4.7A by tomography and subtomogram averaging, revealing detailed interactions, including those made by the so-called L-loop not observed before. Analysis of the outer layer also led to new interesting discoveries. The sec 31 CTD was assigned in the map by comparing the WT and deletion mutant STA-generated density maps. It seems to stabilise the COP-II coats and further evidence from yeast deletion mutants and microsome budding reconstitution experiments suggests that this stabilisation is required in vitro. Furthermore, COP-II rods that cover the membrane tubules in right-handed manner revealed sometimes an extra rod, which is not part of the canonical lattice, bound to them. The binding mode of these extra rods (which I refer to here a Y-shape) is different from the canonical two-fold symmetric vertex (X-shape). When the same binding mode is utilized on both sides of the extra rod (Y-Y) the rod seems to simply insert in the canonical lattice. However, when the Y-binding mode is utilized on one side of the rod and the X-binding mode on the other side, this leads to bridging different lattices together. This potentially contributes to increased flexibility in the outer coat, which may be required to adopt different membrane curvatures and shapes with different cargos. These observations build a picture where stabilising elements in both COP-II layers contribute to functional cargo transport. The paper makes significant novel findings that are described well. Technically the paper is excellent and the figures nicely support the text. I have minor suggestions that I think would improve the text and figures.

L 108: "We collected .... tomograms". While the meaning is clear to a specialist, this may sound somewhat odd to a generic reader. Perhaps you could say "We acquired cryo-EM data of COP-II induced tubules as tilt series that were subsequently used to reconstruct 3D tomograms of the tubules."

L 114: "we developed an unbiased, localisation-based approach". What is the part that was developed here? It seems that the inner layer particle coordinates where simply shifted to get starting points in the outer layer. Developing an approach sounds more substantial than this. Also, it's unclear what is unbiased about this approach. The whole point is that it's biased to certain regions (which is a good thing as it incorporates prior knowledge on the location of the structures).

L 124: "The outer coat vertex was refined to a resolution of approximately ~12 A, revealing unprecedented detail of the molecular interactions between Sec31 molecules (Supplementary Fig 2A)". The map alone does not reveal molecular interactions; the main understanding comes from fitting of X-ray structures to the low-resolution map. Also "unprecedented detail" itself is somewhat problematic as the map of Noble et al (2013) of the Sec31 vertex is also at nominal resolution of 12 A. Furthermore, Supplementary Fig 2A does not reveal this "unprecedented detail", it shows the resolution estimation by FSC. To clarify, these points you could say: "Fitting of the Sec31 atomic model to our reconstruction vertex at 12-A resolution (Supplementary Fig 2A) revealed the molecular interactions between different copies of Sec31 in the membrane-assembled coat.

L 150: Can the authors exclude the possibility that the difference is due to differences in data processing? E.g. how the maps’ amplitudes have been adjusted?

L 172: "that wrap tubules either in a left- or right-handed manner". Don't they always do both on each tubule? Now this sentence could be interpreted to mean that some tubules have a left-handed coat and some a right-handed coat.

L276: "The difference map" hasn't been introduced earlier but is referred to here as if it has been.

L299: Can "Secondary structure predictions" denote a protein region "highly prone to protein binding"?

L316: It's true that the detail in the map of the inner coat is unprecedented and the model presented in Figure 7 is partially based on that. But here "unprecedented resolution" sounds strange as this sentence refers to a schematic model and not a map.

L325: "have 'compacted' during evolution" -> remove. It's enough to say it's more compact in humans and less compact in yeast as there could have been different adaptations in different organisms at this interface.

L327: What's exactly meant by "sequence diversity or variability at this density".

L606-607: The description of this custom data processing approach is difficult to follow. Why is in-plane flip needed and how is it used here?

L627: "Z" here refers to the coordinate system of aligned particles not that of the original tomogram. Perhaps just say "shifted 8 pixels further away from the membrane"

L642-643: How can the "left-handed" and "right-handed" rods be separated here? These terms refer to the long-range organisation of the rods in the lattice; it's not clear how they were separated in the early alignments.

Figure 2B. It's difficult to see the difference between dark and light pink colours.

Figure 3C. These panels report the relative frequency of neighbouring vertices at each position; "intensity" does not seem to be the right measure for this. You could say that the colour bar indicates the "relative frequency of neighbouring vertices at each position" and add detail how the values were scaled between 0 and 1. The same applies to SFigure 1E.

Figure 4. The COP-II rods themselves are relatively straight, and they are not left-handed or right-handed. Here, more accurate would be "architecture of COPII rods organised in a left-handed manner". (In the text the authors may of course define and then use this shorter expression if they so wish.) Panel 4B top panel could have the title "left-handed" and the lower panel should have the title "right-handed" (for consistency and clarity).

Reviewer #2:

The manuscript describes new cryo-EM, biochemistry, and genetic data on the structure and function of the COPII coat. Several new discoveries are reported including the discovery of an extra density near the dimerization region of Sec13/31, and "extra rods" of Sec13/31 that also bind near the dimerization region. Additionally, they showed new interactions between the Sec31 C-terminal unstructured region and Sec23 that appear to bridge multiple Sec23 molecules. Finally, they increased the resolution of the Sec23/24 region of their structure compared to their previous studies and were able to resolve a previously unresolved L-loop in Sec23 that makes contact with Sar1. Most of their structural observations were nicely backed up with biochemical and genetic experiments which give confidence in their structural observations. Overall the paper is well-written and the conclusions justified. However, this is the third iteration of structure determination of the COPII coat on membrane with essentially the same preparation and methods. Each time, there has been an incremental increase in resolution and new discoveries, but the impact of the present study is deemed to be modest. The science is good and appropriate for a specialized journal. Areas of specific concern are described below.

1) The abstract should be re-written with a better description of the work.

2) Line 166 - "Surprisingly, this mutant was capable of tubulating GUVs". This experiment gets to one of the fundamental unknown questions in COPII vesiculation. It is not clear what components are driving the membrane remodeling and at what stages during vesicle formation. Isn't it possible that the tubulation activity the authors observe in vitro is not being driven at all by Sec13/31 but rather Sec23/24-Sar1? Their Sec31ΔCTD data supports this idea because it lacks a clear ordered outer coat despite making tubules. An interesting experiment would be to see if tubules form in the absence of all of Sec13/31 except the disordered domain of Sec31 that the authors suggest crosslinks adjacent Sec23/24s.

3) Line 191 - "Inspecting cryo-tomograms of these tubules revealed no lozenge pattern for the outer 192 coat" - this phrasing is vague. The reviewer thinks that what they mean is that there is a lack of order for the Sec13/31 layer. Please clarify.

4) Line 198 - "unambiguously confirming this density corresponds to 199 the CTD." This only confirms that it is the CTD if that were the only change and the Sec13/31 lattice still formed. Another possibility is that it is density from other Sec13/31 that only appears when the lattice is formed such as the "extra rods". One possibility is that the density is from the extra rods. The reviewer agrees that their interpretation is indeed the most likely, but it is not unambiguous. The authors should consider cross-linking mass spectrometry.

5) In the Sec31ΔCTD section, the authors should comment on why ΔCTD is so deleterious to oligomer organization in yeast when cages form so abundantly in preparations of human Sec13/31 ΔC (Paraan et al 2018).

6) The data is good for the existence of the "extra rods", but significance and importance of them is not clear. How can these extra densities be distinguished from packing artifacts due to imperfections in the helical symmetry.

7) Figure 5 is very hard to interpret and should be redone. Panels B and C are particularly hard to interpret.

8) The features present in Sec23/24 structure do not reflect the reported resolution of 4.7 Å. It seems that the resolution is overestimated.

9) Lines 315/316 - "We have combined cryo-tomography with biochemical and genetic assays to obtain a complete picture of the assembled COPII coat at unprecedented resolution (Fig. 7)." Figure 7 is a schematic model/picture; the authors should reference a different figure or rephrase the sentence.

Reviewer #1:

Hutchings et al. report an updated cryo-electron tomography study of the yeast COP-II coat assembled around model membranes. The improved overall resolution and additional compositional states enabled the authors to identify new domains and interfaces, including what the authors hypothesize is a previously overlooked structural role for the SEC31 C-Terminal Domain (CTD). By perturbing a subset of these new features with mutants, the authors uncover some functional consequences pertaining to the flexibility or stability of COP-II assemblies.

Overall, the structural and functional work appears reliable, but certain questions and comments should be addressed. This study provides a valuable refinement of our understanding of COP-II that I believe is well suited to a specialized, structure-focused journal.

Major Comments: 1) The authors belabor the comparison between the yeast reconstruction of the outer coat vertex with prior work on the human outer coat vertex. Considering the modest resolution of both the yeast and human reconstructions, the transformative changes in cryo-EM camera technology since the publication of the human complex, and the differences in sample preparation (inclusion of the membrane, cylindrical versus spherical assemblies, presence of inner coat components), I did not find this comparison informative. The speculations about a changing interface over evolutionary time are unwarranted and would require a detailed comparison of co-evolutionary changes at this interface. The simpler explanation is that this is a flexible vertex, observed at low resolution in both studies, plus the samples are very different.

2) As one of the major take home messages of the paper, the presentation and discussion of the modeling and assignment of the SEC31-CTD could be clarified. First, it isn't clear from the figures or the movies if the connectivity makes sense. Where is the C-terminal end of the alpha-solenoid compared to this new domain? Can the authors plausibly account for the connectivity in terms of primary sequence? Please also include a side-by-side comparison of the SRA1 structure and the CTD homology model, along with some explanation of the quality of the model as measured by Modeller. Finally, even if the new density is the CTD, it isn't clear from the structure how this sub-stoichiometric and apparently flexible interaction enhances stability. Hence, when the authors wrote "when the [CTD] truncated form was the sole copy of Sec31 in yeast, cells were not viable, indicating that the novel interaction we detect is essential for COPII coat function." Maybe, but could this statement be a leap to far? Is it the putative interaction essential, or is the CTD itself essential for reasons that remain to be fully determined?

3) Are extra rods discussed in Fig. 4 are a curiosity of unclear functional significance? This reviewer is concerned that these extra rods could be an in vitro stoichiometry problem, rather than a functional property of COP-II.

4) The clashscore for the PDB is quite high, and I am dubious about the reliability of refining sidechain positions with maps at this resolution. In addition to the Ramchandran stats, I would like to see the Ramachandran plot as well as, for any residue-level claims, the density surrounding the modeled side chain (e.g. S742).

Minor Comments:

1) The authors wrote "To assess the relative positioning of the two coat layers, we analysed the localisation of inner coat subunits with respect to each outer coat vertex: for each aligned vertex particle, we superimposed the positions of all inner coat particles at close range, obtaining the average distribution of neighbouring inner coat subunits. From this 'neighbour plot' we did not detect any pattern, indicating random relative positions. This is consistent with a flexible linkage between the two layers that allows adaptation of the two lattices to different curvatures (Supplementary Fig 1E)." I do not understand this claim, since the pattern both looks far from random and the interactions depend on molecular interactions that are not random. Please clarify.

2) Related to major point #1, the author wrote "We manually picked vertices and performed carefully controlled alignments." I do now know what it means to carefully control alignments, and fear this suggests human model bias.

3) Why do some experiments use EDTA? I may be confused, but I was surprised to see the budding reaction employed 1mM GMPPNP, and 2.5mM EDTA (but no Magnesium?). Also, for the budding reaction, please replace or expand upon the "the 10% GUV (v/v)" with a mass or molar lipid-to-protein ratio.

4) Please cite the AnchorMap procedure.

Preprint Review

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Reply to the reviewers

Response to Reviewers and Revision Plan

We thank all three reviewers for their time and their comments on our manuscript.

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

Here Ryan et al. have used localization analysis following induced rapid relocalization of endogenous proteins to investigate the composition and recruitment hierarchy of a clathrin-TACC3-based spindle complex that is important for microtubule organization and stability.

The authors generate different HeLa cell lines, each with one of four complex members (TACC3, CLTA, chTOG and GTSE1) endogenously tagged with FKBP-GFP via Cas9-mediated editing. This tag allows rapid recruitment to the mitochondria upon rapamycin addition ("knocksideways"). They ultimately quantify each of the 4 components' localization to the spindle following knocksideways of each component using fluorescently-tagged transfected constructs. The authors' interpretation of the results of this analysis are summarized in the last model figure, in which a core MT-binding complex of clathrin and TACC3 recruit the ancillary components GTSE1 and chTOG. In addition, the authors investigate the contribution of individual clathrin-binding LIDL motifs in GTSE1 to the recruitment of clathrin and GTSE1 to spindles. Their findings here largely agree with and confirm a recent report regarding the contribution of these motifs to GTSE1 recruitment to the spindle. They further analyzed GTSE1 fragments for interphase and mitotic microtubule localization, and identified a second region of GTSE1 required (but not sufficient) for spindle localization. Finally, the authors report that PIK3C2A is not part of this complex, contradicting (correcting) a previously published study.

**Major comments:**

1.The chTOG-FKBP-GFP cell line the authors generate has only a small fraction of chTOG tagged, and thus should not be used for any conclusions about protein localization dependency on chTOG. Because they were unable to construct a HeLa cell line with all copies tagged, the authors expect that the homozygous knock-in of chTOG-FKBP-GFP is lethal, and thus their experience is appropriate to report. However, the authors should not use this cell line alone to make statements about chTOG dependency. They would have to use similar localization analysis, but after another method to disrupt chTOG (as a second-best approach), such as RNAi. In fact, they have reported this in a previous publication (Booth et al 2011). However, the result was different. There, loss of chTOG resulted in reduced clathrin on spindles, suggesting it may stabilize or help recruit the complex. Alternatively, they could remove their chTOG data, but this would compromise the "comprehensive" nature of the work.

The referee is correct. The point here is to show the results we had using this approach for all four proteins under study. For this reason, we do not want to remove this data and prefer to show our results “warts-and-all”. We feel that the shortcomings of our approach are honestly presented and discussed in the manuscript. While only a fraction of chTOG was tagged, we should expect some co-removal after its induced mislocalization. Since we saw no change, we concluded that chTOG is auxiliary.

The “second best” approach suggested (RNAi of chTOG) is problematic for two reasons. First, chTOG RNAi results in gross changes to spindle structure (multipolar spindles) and it is difficult to pick apart differences in protein partner localization that result from loss of chTOG from those resulting from changes in spindle structure. Second, the paper is about induced mislocalization as a method for determining protein complexes once a normal spindle has formed. So, removing chTOG prior to mitosis is not comparable. If we get the same or different result, does it confirm or conflict with the data we have? Nonetheless, given the discrepancy with our earlier work, we should investigate this further.

To address this concern, we will stain endogenous clathrin, TACC3 and GTSE1 following chTOG RNAi and measure their relative levels at the spindle.

Making the chTOG-FKBP-GFP cell line was difficult. As described in the paper, we only recovered heterozygous clones despite repeated attempts. Since submission, we have been made aware of a HCT116 chTOG-FKBP-GFP cell line that is reported to be homozygously tagged (Cherry et al. 2019 doi: 10.1002/glia.23628).

A note about this cell line has been added to the paper (Results section, final sentence of 1st paragraph).

2.The authors initially analyze complex member localization after knocksideways experiments by antibody staining, which has the advantage of analyzing endogenous proteins (versus the later transfected fluorescent constructs). Setting aside potential artefacts from fixation, this would seem to be a better method for controlled analysis to take advantage of their setup (short of generating stable cell lines with second proteins endogenously tagged in a second color - a huge undertaking). The authors conclude that antibody specificity problems confounded their analysis and explained unusual results. However, I think is worth investing a little more effort to sort this out, rather than bringing doubt to the whole data set. Verifying and then using another antibody for chTOG localization would be informative. Of course, the negative control should not be their chTOG-FKBP-GFP line, as it does not relocalize most of chTOG.

In the case of GTSE1, an alternative explanation to antibody specificity issues would be that the GTSE1-FKBP-GFP cell line is not in fact homozygously tagged. Given the low expression levels on the western provided, and the detection of GTSE1 on the spindle in the induced GTSE1-FKBP-GFP cell line (but not TACC3-FKBP-GFP), it seems plausible that an untagged copy remains. If there are multiple copies of GTSE1 in Hela cells, one untagged copy could represent a small fraction of total GTSE1. This should thus be ruled out. GTSE1 clones should be analyzed with more protein extracts loaded - dilutions of the extracts can determine the sensitivity of the blot to lower protein levels. In addition, sequencing of genomic DNA can reveal a small percentage with different reads.

We used a two-pronged approach for assessing relocalization of protein partners (staining vs transfected constructs). The staining approach is superior since endogenous proteins are examined, but it is limited by antibody specificity. The transfection approach overcomes this limitation but is in turn limited by effects of overexpression and tagging. Together the two approaches allow us, and anyone employing this method, to get a picture of protein complexes. We didn’t want to create the impression that one or other approach is confounded, but the referee is correct that this analysis would benefit from further work.

Specifically, to address these concerns:

• We will verify and use alternative chTOG antibodies to try to improve this dataset.
• We will test the possibility that an untagged allele of GTSE1 remains. We will use western blotting and a summary of our genomic analysis will be added to the paper.

  3.There is a lot of data contained in the small graphs summarizing quantification of localization in Figs 3 and 4. They would be more accessible to the reader if they were larger and/or an "example" of the chart with labels was present explaining it (essentially what is in the figure legends). Furthermore, there is no statistical test applied to this data that I see. This is needed. How do authors determine whether there is an "effect"?

Our aim was to compress a lot of information into a small space, while still showing some example primary data. All reviewers raised the same concern which tells us that we went too far towards “data visualization”.

To address this point, we will rework these figures.

**Minor issues:**

1.The GTSE1 constructs used for mutation and localization analysis are 720 amino acids long. A recent study analyzing similar mutations uses a 739 amino acid construct (Rondelet et al 2020). The latter is the predominant transcript in NCBI and Ensembl databases. It appears the construct used by the authors omits the first 19 a.a.. I do not think using the truncated transcript affects conclusions of the manuscript, but it could generate confusion when identifying residues based on a.a.#s of mutant constructs (Fig 6). This should be somehow clarified.

We were aware of the longer transcript but were using the 720 residue form since it is the canonical sequence in Uniprot (https://www.uniprot.org/uniprot/Q9NYZ3). We did not know that the 739 form is the predominant transcript. We agree this is unlikely to affect our work but that the numbering may cause confusion.

We have added a note to the Methods (Molecular Biology section) to accurately describe what we and Rondelet et al. have used.

2.The labeling of constructs in Fig 6C/D is confusing, and appears shifted by eye at places. Please relabel this more clearly.

Apologies for the error.

We have relabeled Figure 6C,D and also made a similar alteration to Figure 5C.

The recommended new experimental data (Analysis complex member levels on spindles after full perturbation of spindle chTOG; new chTOG antibody stainings in the FKBP lines; reanalysis of GTSE1 DNA/protein in GTSE1-FKBP line) should only require a new antibody/siRNA, plus a few weeks time to repeat the analyses already in the paper with new reagents.

Reviewer #1 (Significance (Required)):

While multiple individual components of this complex have been previously characterized, the structure and nature of the complex formation and its recruitment to microtubules/spindles remains a complex problem that has yet to be solved.

Overall this study represents a comprehensive localization-dependency analysis of the Clathrin-TACC3 based spindle complex using a consistent methodology. Although several of the conclusions of the findings echo previous reports, some of the previous literature is contradictory within itself as well as with the conclusions here. Analyzing all components with a single, rapid-perturbation technique thus has great value to present a clear data set, given that the experimental setup conditions and analysis are solid (a goal to which the majority of comments refer).

Beyond the complex localization/recruitment analysis, two novel findings of this study that emerge are:

a)GTSE1 contains a second, separate protein region, distinct from the clathrin-binding motifs that is required for its localization to the spindle, and most likely a microtubule-interaction site. This suggests that GTSE1 recruitment to the spindle is more complex than previously reported.

b)PI3KC2A, which has been reported previously to be a stabilizing member of this complex, is in fact not a member, nor localizes to spindles, nor displays a mitotic defect after loss. This is important conclusion to be made as it would correct the literature, and avoid future confusion.

--

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

In this paper, the authors investigate the nature of interactions between members of the TACC3-chTOG-clathrin-GTSE1 complex on the mitotic spindle. By using a series of HeLa cell lines that they have created by CRISPR/Cas9 editing to enable spatial manipulation (knocksideways) of either TACC3, chTOG, clathrin and GTSE1, they show that on spindle microtubules TACC3 and clathrin represent core complex members whereas chTOG and GTSE1 bind to them respectively but not to each other. Additionally, the authors find that the protein PIK3C2A, which has been implicated in this complex previously is in fact not a component of this complex in mitotic cells. The main advance of the paper in my opinion is the endogenous tagging of the proteins for knocksideways experiments since former experiments depended on RNAi silencing and expression of tagged proteins from plasmids, which introduced issues of protein silencing efficiency and plasmid overexpression problems. This approach seems to alleviate these problems, except in the case of chTOG which seems to be lethal in its homozygous variant.

**Major comments:**

I find the key conclusions regarding the localization of the components of the complex convincing. There are some issues regarding the specificity of antibodies in immunostaining experiments (Fig 3.) and the influence of mCherry-TACC3 expression on distorted localization of the complex prior to knocksideways. However, I think the general conclusion about which complex components (clathrin and TACC3) influence the localization of the other proteins in the complex (chTOG and GTSE1) stands. One thing that I miss from the paper is the data on the consequences on the spindle shape and morphology after knocksideways. I have noticed on images in both Figure 3 and Figure 4 that in some cases distribution of the signal seems to influence quite a bit the spindle morphology. Also, In Figure 3 I have noticed what seems to me a quite big variation in spindle size in tubulin signal in both untreated and rapamycin cells. Since authors have many of these images already, I believe it would be realistic, not costly and of additional value for the paper to provide more data on the consequences of the knocksideways experiments. Change of spindle size, tubulin intensity and DNA/kinetochore misalignment upon knocksideways would be helpful to appreciate more the findings of the paper. More so since the authors on more than one occasion find their motivation in the field of cancer research and spindle stability relation to it. Some data connection to this motivation would be of value. Experiments seem reproducible.

The focus of the paper is on using the knocksideways methodology to understand a protein complex during mitosis, rather than looking at its function. We are not keen to do new experiments that are not part of the central message of the paper. However, the Reviewer is correct that we do already have a dataset that can be mined in the manner described.

To address this point, we will analyze spindle size parameters and also the intensity of tubulin. Our analysis will be limited to the short timeframe of our experiments, but it should reveal or refute any changes in spindle structure that may result from loss of complex members.

**Minor comments:**

I have some problems with the clarity of Figure 3 and 4. For Figure 3. In Figure 3 plots on the right are a bit small and not easy to read. Some reorganization of the figure might be beneficial. In Figure 4 plots to the right are also too small to be clear. Also, I miss the number of cells (n) I can't see the number of individual arrows because of the size of graphs.

Our aim was to compress a lot of information into a small space, while still showing some example primary data. All reviewers raised the same concern which tells us that we went too far towards “data visualization”.

To address this point, we will rework these figures.

Reviewer #2 (Significance (Required)):

I find that the biggest significance of the paper is in the creation of new tools (cell lines) to study the localization of proteins TACC3, chTOG, clathrin and GTSE1. Cell lines where endogenous proteins can be delocalized rapidly will be of value for scientist working not only in mitosis but such as in the case of clathrin research, vesicle formation and trafficking or p53-dependent apoptosis in the case of GTSE1. In the field of mitosis it will surely help and speed up the research concerning the role of these proteins in spindle assembly and stability.

Field of expertise: mitotic spindle

--

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

**Summary:**

This papers analyses the chTog/TACC3/clathrin/GTSE1 complex that crosslinks and stabilises microtubule bundles in the mitotic spindle. The authors have developed an elegant knock sideways approach to specifically analyse the effects of removing individual components of the complex from the spindle and study the effect this has on the other interactors. They report, based on these assays that the core of the complex is formed by TACC3 and Clathrin while GTSE1 and chTog are auxiliary interactors. They also refute previous evidence that this complex also incorporates PIK3C2A. Overall, this is an interesting study that distinguishes itself predominantly by its methodology. However, some of the reported results need more thorough analysis to allow convincing conclusions.

**Major comments:**

1)The knockside way method is the main highlight if this paper. Unlike previous studies by the PI, this time endogenous genes are tagged which is a key advance and allows much better interpretation of the results. I am not sure why the authors have chosen HeLa cells as their model here, given the messed up genome of these cells. A non-transformed cell line would have been preferable, but as a proof of principle study, I think HeLa are acceptable, and I wouldn't expect the authors to repeat all the experiment in another system.

Figure 1,2 and S1 are describing and validating this approach in some detail, but this will require some more work.

The authors state that gene targeting was validated using a combination of PCR, sequencing, Western blotting, but show only the results for westerns. PCR analysis that demonstrates homozygous or heterozygous gene targeting should be shown here.

Another issue is the penetrance of the phenotypes induced by Rapamycin. The authors show nice data of the system working in individual cells but do not give us an idea if this happens in all cells. The localisation of the individual tagged genes should be quantified (ideally with line plots) in 50 randomly chosen mitotic cells with 3 repeats before and after rapamycin treatment. Moreover, the analysis of mitotic duration (Figure S1D) should be extended to include a plus Rapamycin cohort and this should be moved in the main Figure.

If the system works only in a small proportion of cells, this should be clearly stated. I don't think this would prevent publication, but it is an important piece of information that is missing.

The Reviewer raises two issues here.

• PCR analysis should be shown. This issue was also partly raised by Reviewer 1. A summary of our PCR analysis was actually included in Table 1, since the analysis we did is pretty unwieldy. We agree though that presenting our evidence for homozygosity of the cell lines would be useful. To address this point, we will add more detail of the PCR and sequencing work done to validate these cell lines.
• Does knocksideways happen in all cells? The answer to this depends on the transient expression of MitoTrap and sufficient application of rapamycin. We agree that this will be a useful piece of information to add to the manuscript. A related issue is whether knocksideways of complex members affects mitotic progression. We have established through other experiments that rapamycin application to wild-type cells alters mitotic progression, although application of Rapalog does not have this effect. Our plan to address these points is 1) to analyze the efficacy of knocksideways that readers can expect to achieve using these, or similar cells, and 2) analyze mitotic duration in rapalog-treated cells expressing a rapalog sensitive MitoTrap.

  2)Apart from a simple quantification of mitotic duration, I believe a more detailed mitotic phenotype analysis for each knock-side way gene, especially the homozygous targeted clones, should be included. This can involve more high-resolution live cell imaging of mitotic progression with SiR-DNA and GFP-tubulin, using the dark mitotrap.

We don’t agree that such an analysis should be included. The focus of this paper is on using the knocksideways methodology to understand a protein complex during mitosis, and not looking at its function. There are several papers on the mitotic phenotypes of these genes probed using RNAi in different cellular systems (examples for chTOG: 10.1101/gad.245603; TACC3/clathrin: 10.1038/emboj.2011.15, 10.1242/jcs.075911, 10.1083/jcb.200911091, 10.1083/jcb.200911120; GTSE1: 10.1083/jcb.201606081). Moreover, our 2013 paper used knocksideways (with RNAi and overexpression) and has a detailed analysis of mitotic progression, microtubule stability, checkpoint activity and kinetochore motions (Cheeseman et al., 2013 doi: 10.1242/jcs.124834).

New experiments that are not part of the central message of the paper and are unlikely to give new insight are not the best use of our revision efforts for this paper (especially during the pandemic). Having said this, Reviewer 2’s suggestion to use our existing dataset to investigate mitotic phenotypes, will largely answer Reviewer 3’s request.

We will analyze spindle size parameters and also the intensity of tubulin. Our analysis will be limited to the short timeframe of our experiments, but it should reveal or refute any changes in spindle structure that result from the loss of complex members.

3)Overall, the quantitative analysis in Figure 3 ,4 and 7 is not good enough and sometimes doesn't fully support the conclusions. In Figure 3,4 a convoluted way of demonstrating the change in localisation is shown and this panel is so small that is almost impossible to read. Also, there is no statistical analysis, and the sample size seems very small . At least 25 cells should be analysed here in 3 repeats. I would suggest to unify the quantification in the MS and use the line plots shown in Figure 5 and 6 and compare each protein before and after rapamycin addition. This is much easier to read and more convincing. The images of the cells panels can be moved to a supplement as they contain very little information. This would generate space to expand the size and depth of the quantitative analysis. Instead of Anova tests, I would recommend using a simple t-test comparing each condition to its relevant control since this is the only relevant comparison in the experiment. Statistical significance should be calculated for each experiment with sufficient sample size. It would also be better to show the individual data points from the three repeats in different colours so that the reproducibility between repeat can be judged.

This type of statistical analysis should be uniformly done throughout the MS and also extended to Figure 7.

The referee raises several issues here with our data presentation and statistical analysis.

• Our aim in Figures 3 and 4 was to compress a lot of information into a small space, while still showing some example primary data. All reviewers raised the same concern about these figures which tells us that we went too far towards “data visualization”. To address this point, we will rework Figures 3 and 4 to provide more clear data presentation.
• The Reviewer’s comments about statistical analysis however are not sound. First, it is incorrect to state that simple t-tests can be applied (this is a form of p-hacking). Correction for multiple testing must be done on these datasets. Second, the reviewer arbitrarily states numbers for cells and experimental repeats without considering the effect size or it seems, understanding the structure of the data that we have collected. Sample sizes are small but they are taken from many independent replicates. Third, and related to the previous point, the fixed and live cell data are structured differently which means that a uniform data presentation is not possible. The live data has a paired design and each cell is an independent replicate (with replicates done over several trials). The fixed data is unpaired and we have taken measures from several experiments (independent replicates). The point about applying statistical tests to the data is also made by Reviewer 1 and we will use appropriate tests (NHST or estimation statistics) as we re-work the figures.

  Reviewer #3 (Significance (Required)):

In my opinion, the most interesting aspect of the MS is the methodology. Based on this, publication is justified and will be of interest to a wider audience. That is why a more detailed analysis of the penetrance of this manipulation across the cell population will be critical.

The application of this method to analyse the composition of the TACC3/Clathrin complex on the spindle is the main biological advance, and the novel information is rather limited but not unimportant.

Overall, if these results can be properly quantified I would recommend publication.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This papers analyses the chTog/TACC3/clathrin/GTSE1 complex that crosslinks and stabilises microtubule bundles in the mitotic spindle. The authors have developed an elegant knock sideways approach to specifically analyse the effects of removing individual components of the complex from the spindle and study the effect this has on the other interactors. They report, based on these assays that the core of the complex is formed by TACC3 and Clathrin while GTSE1 and chTog are auxiliary interactors. They also refute previous evidence that this complex also incorporates PIK3C2A. Overall, this is an interesting study that distinguishes itself predominantly by its methodology. However, some of the reported results need more thorough analysis to allow convincing conclusions.

Major comments:

1)The knockside way method is the main highlight if this paper. Unlike previous studies by the PI, this time endogenous genes are tagged which is a key advance and allows much better interpretation of the results. I am not sure why the authors have chosen HeLa cells as their model here, given the messed up genome of these cells. A non-transformed cell line would have been preferable, but as a proof of principle study, I think HeLa are acceptable, and I wouldn't expect the authors to repeat all the experiment in another system. Figure 1,2 and S1 are describing and validating this approach in some detail, but this will require some more work. The authors state that gene targeting was validated using a combination of PCR, sequencing, Western blotting, but show only the results for westerns. PCR analysis that demonstrates homozygous or heterozygous gene targeting should be shown here. Another issue is the penetrance of the phenotypes induced by Rapamycin. The authors show nice data of the system working in individual cells but do not give us an idea if this happens in all cells. The localisation of the individual tagged genes should be quantified (ideally with line plots) in 50 randomly chosen mitotic cells with 3 repeats before and after rapamycin treatment. Moreover, the analysis of mitotic duration (Figure S1D) should be extended to include a plus Rapamycin cohort and this should be moved in the main Figure. If the system works only in a small proportion of cells, this should be clearly stated. I don't think this would prevent publication, but it is an important piece of information that is missing.

2)Apart from a simple quantification of mitotic duration, I believe a more detailed mitotic phenotype analysis for each knock-side way gene, especially the homozygous targeted clones, should be included. This can involve more high-resolution live cell imaging of mitotic progression with SiR-DNA and GFP-tubulin, using the dark mitotrap.

3)Overall, the quantitative analysis in Figure 3 ,4 and 7 is not good enough and sometimes doesn't fully support the conclusions. In Figure 3,4 a convoluted way of demonstrating the change in localisation is shown and this panel is so small that is almost impossible to read. Also, there is no statistical analysis, and the sample size seems very small . At least 25 cells should be analysed here in 3 repeats. I would suggest to unify the quantification in the MS and use the line plots shown in Figure 5 and 6 and compare each protein before and after rapamycin addition. This is much easier to read and more convincing. The images of the cells panels can be moved to a supplement as they contain very little information. This would generate space to expand the size and depth of the quantitative analysis. Instead of Anova tests, I would recommend using a simple t-test comparing each condition to its relevant control since this is the only relevant comparison in the experiment. Statistical significance should be calculated for each experiment with sufficient sample size. It would also be better to show the individual data points from the three repeats in different colours so that the reproducibility between repeat can be judged. This type of statistical analysis should be uniformly done throughout the MS and also extended to Figure 7.

Significance

In my opinion, the most interesting aspect of the MS is the methodology. Based on this, publication is justified and will be of interest to a wider audience. That is why a more detailed analysis of the penetrance of this manipulation across the cell population will be critical. The application of this method to analyse the composition of the TACC3/Clathrin complex on the spindle is the main biological advance, and the novel information is rather limited but not unimportant. Overall, if these results can be properly quantified I would recommend publication.

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Referee #2

Evidence, reproducibility and clarity

In this paper, the authors investigate the nature of interactions between members of the TACC3-chTOG-clathrin-GTSE1 complex on the mitotic spindle. By using a series of HeLa cell lines that they have created by CRISPR/Cas9 editing to enable spatial manipulation (knocksideways) of either TACC3, chTOG, clathrin and GTSE1, they show that on spindle microtubules TACC3 and clathrin represent core complex members whereas chTOG and GTSE1 bind to them respectively but not to each other. Additionally, the authors find that the protein PIK3C2A, which has been implicated in this complex previously is in fact not a component of this complex in mitotic cells. The main advance of the paper in my opinion is the endogenous tagging of the proteins for knocksideways experiments since former experiments depended on RNAi silencing and expression of tagged proteins from plasmids, which introduced issues of protein silencing efficiency and plasmid overexpression problems. This approach seems to alleviate these problems, except in the case of chTOG which seems to be lethal in its homozygous variant.

Major comments:

I find the key conclusions regarding the localization of the components of the complex convincing. There are some issues regarding the specificity of antibodies in immunostaining experiments (Fig 3.) and the influence of mCherry-TACC3 expression on distorted localization of the complex prior to knocksideways. However, I think the general conclusion about which complex components (clathrin and TACC3) influence the localization of the other proteins in the complex (chTOG and GTSE1) stands. One thing that I miss from the paper is the data on the consequences on the spindle shape and morphology after knocksideways. I have noticed on images in both Figure 3 and Figure 4 that in some cases distribution of the signal seems to influence quite a bit the spindle morphology. Also, In Figure 3 I have noticed what seems to me a quite big variation in spindle size in tubulin signal in both untreated and rapamycin cells. Since authors have many of these images already, I believe it would be realistic, not costly and of additional value for the paper to provide more data on the consequences of the knocksideways experiments. Change of spindle size, tubulin intensity and DNA/kinetochore misalignment upon knocksideways would be helpful to appreciate more the findings of the paper. More so since the authors on more than one occasion find their motivation in the field of cancer research and spindle stability relation to it. Some data connection to this motivation would be of value. Experiments seem reproducible.

Minor comments:

I have some problems with the clarity of Figure 3 and 4. For Figure 3. In Figure 3 plots on the right are a bit small and not easy to read. Some reorganization of the figure might be beneficial. In Figure 4 plots to the right are also too small to be clear. Also, I miss the number of cells (n) I can't see the number of individual arrows because of the size of graphs.

Significance

I find that the biggest significance of the paper is in the creation of new tools (cell lines) to study the localization of proteins TACC3, chTOG, clathrin and GTSE1. Cell lines where endogenous proteins can be delocalized rapidly will be of value for scientist working not only in mitosis but such as in the case of clathrin research, vesicle formation and trafficking or p53-dependent apoptosis in the case of GTSE1. In the field of mitosis it will surely help and speed up the research concerning the role of these proteins in spindle assembly and stability.

Field of expertise: mitotic spindle

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Referee #1

Evidence, reproducibility and clarity

Here Ryan et al. have used localization analysis following induced rapid relocalization of endogenous proteins to investigate the composition and recruitment hierarchy of a clathrin-TACC3-based spindle complex that is important for microtubule organization and stability. The authors generate different HeLa cell lines, each with one of four complex members (TACC3, CLTA, chTOG and GTSE1) endogenously tagged with FKBP-GFP via Cas9-mediated editing. This tag allows rapid recruitment to the mitochondria upon rapamycin addition ("knocksideways"). They ultimately quantify each of the 4 components' localization to the spindle following knocksideways of each component using fluorescently-tagged transfected constructs. The authors' interpretation of the results of this analysis are summarized in the last model figure, in which a core MT-binding complex of clathrin and TACC3 recruit the ancillary components GTSE1 and chTOG. In addition, the authors investigate the contribution of individual clathrin-binding LIDL motifs in GTSE1 to the recruitment of clathrin and GTSE1 to spindles. Their findings here largely agree with and confirm a recent report regarding the contribution of these motifs to GTSE1 recruitment to the spindle. They further analyzed GTSE1 fragments for interphase and mitotic microtubule localization, and identified a second region of GTSE1 required (but not sufficient) for spindle localization. Finally, the authors report that PIK3C2A is not part of this complex, contradicting (correcting) a previously published study.

Major comments:

1.The chTOG-FKBP-GFP cell line the authors generate has only a small fraction of chTOG tagged, and thus should not be used for any conclusions about protein localization dependency on chTOG. Because they were unable to construct a HeLa cell line with all copies tagged, the authors expect that the homozygous knock-in of chTOG-FKBP-GFP is lethal, and thus their experience is appropriate to report. However, the authors should not use this cell line alone to make statements about chTOG dependency. They would have to use similar localization analysis, but after another method to disrupt chTOG (as a second-best approach), such as RNAi. In fact, they have reported this in a previous publication (Booth et al 2011). However, the result was different. There, loss of chTOG resulted in reduced clathrin on spindles, suggesting it may stabilize or help recruit the complex. Alternatively, they could remove their chTOG data, but this would compromise the "comprehensive" nature of the work.

2.The authors initially analyze complex member localization after knocksideways experiments by antibody staining, which has the advantage of analyzing endogenous proteins (versus the later transfected fluorescent constructs). Setting aside potential artefacts from fixation, this would seem to be a better method for controlled analysis to take advantage of their setup (short of generating stable cell lines with second proteins endogenously tagged in a second color - a huge undertaking). The authors conclude that antibody specificity problems confounded their analysis and explained unusual results. However, I think is worth investing a little more effort to sort this out, rather than bringing doubt to the whole data set. Verifying and then using another antibody for chTOG localization would be informative. Of course, the negative control should not be their chTOG-FKBP-GFP line, as it does not relocalize most of chTOG.

In the case of GTSE1, an alternative explanation to antibody specificity issues would be that the GTSE1-FKBP-GFP cell line is not in fact homozygously tagged. Given the low expression levels on the western provided, and the detection of GTSE1 on the spindle in the induced GTSE1-FKBP-GFP cell line (but not TACC3-FKBP-GFP), it seems plausible that an untagged copy remains. If there are multiple copies of GTSE1 in Hela cells, one untagged copy could represent a small fraction of total GTSE1. This should thus be ruled out. GTSE1 clones should be analyzed with more protein extracts loaded - dilutions of the extracts can determine the sensitivity of the blot to lower protein levels. In addition, sequencing of genomic DNA can reveal a small percentage with different reads.

3.There is a lot of data contained in the small graphs summarizing quantification of localization in Figs 3 and 4. They would be more accessible to the reader if they were larger and/or an "example" of the chart with labels was present explaining it (essentially what is in the figure legends). Furthermore, there is no statistical test applied to this data that I see. This is needed. How do authors determine whether there is an "effect"?

Minor issues:

1.The GTSE1 constructs used for mutation and localization analysis are 720 amino acids long. A recent study analyzing similar mutations uses a 739 amino acid construct (Rondelet et al 2020). The latter is the predominant transcript in NCBI and Ensembl databases. It appears the construct used by the authors omits the first 19 a.a.. I do not think using the truncated transcript affects conclusions of the manuscript, but it could generate confusion when identifying residues based on a.a.#s of mutant constructs (Fig 6). This should be somehow clarified.

2.The labeling of constructs in Fig 6C/D is confusing, and appears shifted by eye at places. Please relabel this more clearly.

The recommended new experimental data (Analysis complex member levels on spindles after full perturbation of spindle chTOG; new chTOG antibody stainings in the FKBP lines; reanalysis of GTSE1 DNA/protein in GTSE1-FKBP line) should only require a new antibody/siRNA, plus a few weeks time to repeat the analyses already in the paper with new reagents.

Significance

While multiple individual components of this complex have been previously characterized, the structure and nature of the complex formation and its recruitment to microtubules/spindles remains a complex problem that has yet to be solved.

Overall this study represents a comprehensive localization-dependency analysis of the Clathrin-TACC3 based spindle complex using a consistent methodology. Although several of the conclusions of the findings echo previous reports, some of the previous literature is contradictory within itself as well as with the conclusions here. Analyzing all components with a single, rapid-perturbation technique thus has great value to present a clear data set, given that the experimental setup conditions and analysis are solid (a goal to which the majority of comments refer).

Beyond the complex localization/recruitment analysis, two novel findings of this study that emerge are:

a)GTSE1 contains a second, separate protein region, distinct from the clathrin-binding motifs that is required for its localization to the spindle, and most likely a microtubule-interaction site. This suggests that GTSE1 recruitment to the spindle is more complex than previously reported.

b)PI3KC2A, which has been reported previously to be a stabilizing member of this complex, is in fact not a member, nor localizes to spindles, nor displays a mitotic defect after loss. This is important conclusion to be made as it would correct the literature, and avoid future confusion.

Reviewer #2:

In this manuscript by de Rus Jacquet et al., authors present an interesting study to detect changes in extracellular vesicles in human PD patient derived iPSC-derived astrocytes carrying the LRRK2 G2019S mutation. Isogenic gene corrected iPSCs were used as controls in all experiments. Authors first performed RNA-Seq for global gene expression changes between G2019S and "WT" gene corrected astrocytes. GO analysis showed an upregulation of extracellular compartments (including exosome compartments) in LRRK2 astrocytes. Subsequent experiments focusing on extracellular vesicles (EVs) and multivesicular bodies (MVBs), showed specific differences of MVB area and the size of secreted EVs. Secreted EVs from G2019S astrocytes also contained more LRRK2 particles and G2019S EVs contained more phosphorylated aSyn particles. Co-culture of LRRK2 astrocytes with human dopamine neurons showed accumulation of CD63+ exosomes in neurites, compared to co-culture with WT astrocytes. Co-culture with LRRK2 astrocytes decreased viability of TH+ neurons and LRRK2 dendrites/neurites were also shorter. These co-culture findings were replicated using EV-enriched conditioned media. Finally, authors showed that the trophic effect of astrocytes on neurons was due both to soluble factors released into the media, and production and release of EVs. Overall, this is a well-written and systematically performed study. This reviewer has several comments as detailed below.

1) Based on their data, authors conclude that astrocyte-to-neuron signaling and trophic support mediated by EVs is disrupted in LRRK2 G2019S astrocytes. Have authors measured the differences in trophic factors released by LRRK2 astrocytes in EVs and in conditioned media?

2) Authors differentiate cells (astrocytes and neurons) from midbrain lineage NPCs. The data show convincing effects of the LRRK2 derived astrocytes on neurons, but one question is whether this is specific to dopaminergic cells. Would this genotype specific effect also be expected in other lineages, e.g. cortical neurons? Authors should discuss this point.

3) Prior work has demonstrated reductions in neurite length in neurons derived from LRRK2 G2019S iPSCs (not specific to dopaminergic neurons in LRRK2 cells) (for example Reinhard et al 2013). It is curious that the LRRK2 G2019S mutation itself can cause such a phenotype in neurons mono-cultures, and as shown in the current study, that LRRK2 G2019S astrocytes also induce a similar effect on WT neurons in co-culture. Can authors expand on this point in the Discussion?

4) Authors should provide data on % dopaminergic neurons generated in the cultures.

5) p7. Authors refer to phosphorylated a-synuclein as accelerating PD pathogenesis, but the references cited do not show this. In fact, Gorbatyuk et al 2008, showed that overexpression of S129 with constitutive phosphorylation eliminated a-synuclein induced nigrostriatal degeneration. The Fujiwara et al 2002 reference showed the presence of phospho a-syunclein in Lewy bodies and neurites. Authors should revise their statement that phospho a-synuclein is associated with accelerated pathology.

6) Please provide details on the number of iPSC lines used for these experiments.

7) Clarify whether the WT neurons used for co-culture were derived from the isogenic human neurons?

Reviewer #1:

In this manuscript titled "The LRRK2 G2019S mutation alters astrocyte-to-neuron communication via extracellular vesicles and induces neuron atrophy in a human iPSC-derived model of Parkinson's disease", Jacquet and colleagues investigated the role of Parkinsonism gene mutation LRRK2 G2019S in hiPSC-differentiated astrocytes. By isolating extracellular vesicles from ACM and examining astrocytes with various electron microscopy techniques, the authors found that LRRK2 G2019S affects the morphology and distribution of MVBs and the morphology of secreted EVs in hiPSC-differentiated astrocytes. Furthermore, the authors observed that astrocyte-derived EVs can be internalized by dopaminergic neurons and such EVs support neuronal survival. However, LRRK2 G2019S EVs lost the ability of promoting neuronal survival. This is an interesting study showing a non-cell autonomous contribution to dopaminergic neuron loss in PD.

The proposed idea of how LRRK2 G2019S dysregulates EV-mediated astrocyte-to-neuron communication is novel and exciting. However, the authors present some conflicting data that is not addressed during the discussion: they first conclude upregulated exosome biogenesis by RNAseq in G2019S vs WT astrocytes, but later show a decrease in the number of <120nm particles in G2019S mutants suggesting a decrease in the classical exosome-sized vesicle secreted compared to WT. Lastly, their MVB images show less CD63 gold particles in G2019S compared to WT control (though this was not quantified). Do the authors suggest and increase or decrease in exosome biogenesis in G2019S mutants? How do they reconcile these seemingly contradicting data? Several experiments, controls and additional analyses are needed to fully demonstrate the validity of the proposed mechanism.

Major concerns:

1) In figure 1 A authors demonstrate iPSC-derived astrocytes characterization. Since there is no one unified and validated method for astrocytes differentiation, there is a need for more accurate characterization of iPSC-derived astrocytes. Authors should demonstrate the percentage of cells positive to astrocytic markers and to prove that obtained astrocytes are functional (able to promote synaptogenesis and uptake glutamate). I would also recommend analyzing the iPSC-derived astrocyte cultures for expression of more specific astrocytic markers as GLT1, SOX9 in addition to those which have been analyzed. Moreover, it is highly important to know what is the proportion of astrocytes derived from LRRK2 G2019S line and its isogenic control in order to be able to compare their effect on neurons.

2) In Figure 1, the authors found a significant upregulation of exosome components in astrocytes, demonstrating an important role of LRRK2 G2019S in EV signaling pathway. In the discussion, the authors briefly mentioned 'sub-populations of CD63- EVs may be differentially secreted in mutant astrocytes'. Since the authors have obtained the RNA-seq data, it would be nice to dig deep into the data and comment on potential EV sub-populations which can be differentially secreted. This information can be very beneficial for follow-up studies in the PD and LRRK2 field. Furthermore, the authors should assess the expression of Rab27a and CD82 in WT and LRRK2 G2019S astrocytes by western blots to verify RT-qPCR data. Furthermore, the authors should present specifically exosome biogenesis or secretion genes are altered to provide further insight into the stage of exosome biogenesis that is affected (ESCRT0-3, VPS4, ALIX, etc).

3) In Figure 2A and B, data shows that both WT and LRRK2 G2019S astrocytes produce MVBs and MVBs in LRRK2 G2019S astrocytes is smaller than in WT astrocytes. In Figure 2E, the authors showed the abundance of CD63 localized within MVBs in WT astrocytes but did not show the CD63 localization in MVBs in G2019S astrocytes. However, it is important to show CD63 localization in MVBs in G2019S astrocytes to fully support the conclusion that CE63+ MVBs are present in LRRK2 G2019S astrocytes. In addition, CD44 is a marker for astrocyte-restricted precursor cells. Although CD44+ positive cells are committed to give rise to astrocytes, it is crucial to include another astrocyte marker to ensure these cells are indeed mature astrocytes. -Related, authors should consider citing some of the MVB maturation literature to guide the readers.

4) In Figure 3, it is impressive that the authors are able to image EVs using cyro-EM approach and analyze their sizes. The authors also observed different shapes of EVs. Is there any shape difference between WT EVs and G2019S EVs? Is there a way that the authors could categorize these shapes and do a detailed analysis in EV shapes? Also, In Figure 3D, both WT EV and G2019S EV images should present side by side for comparison. -Related, the size frequencies of EVs presented suggest a difference in the types of EV's released. Interestingly, exosomes are classically known to range from ~50-120nm and this population is significantly decreased in G2019S compared to WT. What does this suggest?

5) In figure 3c, SBI ELISA claims to quantify CD63+ vesicles, the authors should present more standardized particle quantification data (either by CD63 FACs for isolated EVs in WT vs G2019S or ZetaView/QNano particle tracking). The authors should also directly quantify the total number of EVs secreted in WT vs G2019S conditions (not only CD63+).

6) In Figure 4, the authors quantify LRRK2+/CD63+ particles by imaging. Importantly, it appears that there are less CD63 "large gold" particles in MVB of G2019S compared to control. This CD63 baseline quantification in MVB of WT vs. G2019S should be presented in this figure. These data are not convincing and should be quantified by FACS in secreted EV. Supplementary figure 3 should be brought into this figure.

7) In Figure 5, using CD63 as a MVB marker is not the most accurate approach. ESCRT markers should be co-stained with these experiments to truly show MVB localization (CD63 can localize to MVBs but is known to have a wider distribution throughout the cell compared to TSG1010 or other ESCRT complex proteins). Additionally, the authors must show their Supplemental Figure 3 ELISA quantification of p-aSyn in this main figure, and comment on why they conclude higher p-aSyn content in MVBs based on their IEM but then find no differences in aSyn in secreted EVs in WT vs. G2019S by ELISA.

8) In figure 6, it is even more clear that there is a stark difference between the CD63 presence in/near MVBs between WT and G2019S conditions. Since the authors normalize several pieces of data to CD63 (MVB localization, LRRK2 co-localization, etc), it is critical to quantify the number of baseline CD63 gold particles in MVBs in WT vs G2019S.

9) In Figure 7, the authors used the co-culture of astrocytes and neurons to assess astrocyte-derived EV uptake by dopaminergic neurons. Although 3D reconstitution of neurons and exosomes can be precise, the data may not be 100% clean. It would be better if the authors collect ACM containing EV fraction from WT astrocyte and G2019S astrocytes and then incubate dopaminergic neurons with ACM containing EV fraction. In this way, only dopaminergic neurons are in the culture and there will be no CD63-GFP expressed astrocytes to contaminate the CD63-GFP signal in neurons.

10) In Figure 9, the authors must show their ACM control. They show untreated, EV-free, and EV-rich ACM, but do not show unmanipulated ACM control.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The discussion between reviewers and editors centered on a few key points. First, all reviewers felt that it is of utmost importance that a justified and appropriate number of hiPSCs and their appropriate controls are utilized throughout. In particular, there is concern that G2019S-related phenotypes may be more variable than other presumed monogenetic causes of disease, for example a low penetrance of disease causation associated with G2019S in people (e.g., 20% lifetime penetrance for PD) that may necessitate more lines analyzed than usual, and possible lines from carriers of the mutation that appear resilient to disease. Studies in the past decade that use only one or a few lines of G2019S hIPSCs have generally failed to replicate in more than one laboratory, possibly due to low power. The reviewer's were not sure how rigorous the study was in this regard. Second, reviewer's felt there was over-interpretation and speculation regarding the possible roles of differential trophic factors released by the astrocytes in EVs and conditioned media without many measures of specific trophic factors, or rescue experiments, to help define the mechanism. Third, the EV data are not broadly supported by NTA (like Zeta or nanosight) or quantitative measures fairly standard in the EV field. For example, the authors did not clearly quantify the total number of EVs secreted in WT vs. G2019S conditions, which would be a basic experiment needed to create interest in the study in the EV community.

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Reply to the reviewers

We are grateful for the insightful, constructive and very positive reviews provide by the three reviewers. Please find responses to each of the reviewer comments below.

---

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

The authors study proteins localised to the apical end of the highly polarised parasites causing Toxoplasmosis and malaria. They find new proteins using BioID and examine the localisation of these along with recently identified proteins in the two different parasites. They key question they address is whether there is a conservation of the apical components in these distantly related parasites as well as in some even more distantly related organisms. This is an important question as the apical part comprises many essential proteins of invasion of host cells and shows a unique structure that defines the apicomplexans as a group. The apical structure can be highly elaborate such as in T. gondii and less elaborate as in P. falciparum. The authors now show that there is a large conservation between the species in the protein makeup of the apical end. The experiments are well performed, displayed and discussed and there is no doubt about the validity of the presented results. The text is eloquently written, if at times a bit wordy.

My only main suggestion would be to possibly add data on gene disruption of the two candidates (0310700 and 1216300) that are not detected in blood stage parasites but in the insect stages. A deletion of these should be technically straightforward and would show whether the proteins are important to the parasite. Likely not all of the now many proteins are essential for the parasites but these are good candidates to rapidly investigate. But showing a functional impact might convince editors at certain journals.

Authors’ response: The central aim of this study was to ask if the molecular composition of the conoid complex is conserved across Apicomplexa. Functional dissection of proteins is part of an exciting set of subsequent questions and studies that will now follow by us and others. However, careful and thorough phenotyping of gene disruptions is not trivial work, would be most informative to perform in both Toxoplasma and Plasmodium, and is therefore beyond the scope of this project. Regarding the two proteins suggested by this reviewer for follow-up work and the question of ‘essentiality’, that the proteins have not been lost during parasite selection through evolution is clear evidence of their relevance to the biology of Plasmodium.

Other suggestions in chronological order (line numbers would have helped)

title: maybe write 'conoid complex proteome'

Authors’ response: while we initially thought that this change would be suitable, given that the subsequent part of the title is ‘reveals a cryptic conoid feature’ we think it is clearer and more logical to leave this title in its original form. The conoid complex includes the apical polar rings, and these are not considered to be cryptic or previously unrecognised, only the conoid. While our study confirms that there is conservation across all proteome components of the conoid complex, this is secondary to the primary question of this study.

abstract: not sure about the use of the words instrument and substructures

Authors’ response: we believe that the use of ‘instrument’ is an appropriate analogy of a tool and not different from the use of ‘machine’ and ‘machinery’ that is widely used in molecular and cellular biology. Similarly, ‘substructure’ acknowledges that within recognised structures, such as the conoid, there is further specific organisation such as the conoid base or apex.

page 2 last lines: is tubulin monomeric or polymerized?

Authors’ response: to specify the polymerized state of tubulin as mentioned here the text has been changed to ‘the presence of tubulin polymers’.

page 3 name protein talked about in 9th line

Authors’ response: we have now named this protein (RNG2) as suggested.

third paragraph: mention previous proteomics studies e.g. from Ke Hu (mentioned later in discussion)

Authors’ response: We feel that it is more appropriate to leave the discussion of the Hu et al (2006) proteomics study, along with various subsequent approaches used in pursuit of discovering conoid-associated proteins, to the discussion as currently occurs. In the introduction we seek to efficiently inform the reader of the current state of knowledge that makes the value and nature of the questions that we have asked in this study apparent. But we do give full credit and evaluation of previous studies in the discussion which we think is the most appropriate place for this.

first paragraph or results could go into introduction

Authors’ response: The first paragraph of the Results contains specific detail of just one aspect of this study, the use of hyperLOPIT. This is relevant to the new analysis that we have made of the hyperLOPIT data in this study. We, therefore, believe that it is most appropriately presented here in the Results in association with the new analyses we described. Our aim is that the Introduction is succinct and serves the entire study.

page 4: add reference after BioID

Authors’ response: reference added as suggested

page 5: add definitions of the conoid; what technique was used to report YFP-SAS6?

Authors’ response: It is unclear what this reviewer is requesting with respect to definitions of the conoid on this page. Nevertheless, we have now included a thorough definition of the conoid based on the original electron microscopy studies (fourth paragraph of the Introduction).

With respect to the technique used to report on YFP-tagged SAS6 in the de Leon et al 2013 study, we now include fuller description of this previous study as follows:

‘The fluorescence imaging used in the de Leon et al study was limited to lower resolution widefield microscopy. Immuno-TEM was also used, however, contrary to their conclusions, did show YFP presence throughout transverse and oblique sections of the conoid consistent with our detection of SAS6L throughout the conoid body.’

page 7: 'showed similar localisation' instead of 'phenocopied'?; add reference after ookinete stage; add expression levels from PlasmoDB to the Table 1 data at least for merozoites, ookinetes and sporozoites or add separate table for the 9 proteins in supplement

Authors’ response: ‘phenocopied’ replaced, as suggested. Reference added after ookinete stage, as suggested.

As requested, we have complied available expression data for the Plasmodium proteins throughout the different zoite stages and will include these data as supplemental material in our subsequent revision.

Discussion: Maybe discuss that the conoid complex is a cytoskeletal structure and that the other cytoskeletons (actin, microtubules, subpellicular network) also differ between the species investigated in their composition and overall architecture

Authors’ response: These are reasonable suggested analogies and we will introduce them in the subsequent revision.

page 9: at least two proteins could be deleted as they seem to not confer any growth defect on blood stages (see main comment)

Authors’ response: This reviewer has not linked this comment to a specific statement on page 9, however, we are cautious not to interpret lack of observed growth defects in experimental scenarios with unimportant or irrelevant proteins. Maintenance, through natural selection and evolution, of proteins of a structure indicate that they are selectively advantageous and of functional relevance. The two proteins in question are not expressed in the blood stage, so one wouldn’t expect their deletion to have consequence in this stage.

Apart from classic TEM images also Cryo EM data is available for apex of merozoite and sporozoite. Worth to discuss?

Authors’ response: According to this review’s subsequent suggestion (below), we are now preparing a schematic for the subsequent revision of each of the zoite stages of Plasmodium and these draw on Cryo EM tomography data.

Add and discuss the recent work from Curr Biol and EMBO J of the Yuan lab on ookinete formation?

Authors’ response: These two reports are excellent studies of the polarised development of the cell pellicle during ookinete formation and control of gliding initiation, but don’t specifically related to the conoid complex structures that are the subject of our study. We, therefore, do not see a logical place to include discussion of these works.

Reviewer #2 (Significance (Required)):

The paper provides a conceptual advance over previous data as it shows clearly a high level of conservation of the protein components of the conoid complex. It could introduce a new terminology for these important apical structure of Apicomplexan parasites and provides a good basis to dissect the molecular functions.

Authors’ response: We appreciate this reviewer recognising this opportune point in time to more clearly define the terminology applied to these apical structures so that they can be more clearly and easily compared between taxa. We will use the suggested schematic figure (see comment below) that is now in preparation as a basis and guide for a refined nomenclature based on precedent in the literature.

As it stands all scientists investigating Plasmodium and Toxoplasma invasion of host cells will be highly interested in this study, most scientists researching apicomplexan organisms should be and some evolutionary scientists will be interested in this study.

Key papers in the field are the discovery of the Toxoplasma conoid as a highly twisted microtubule-like structure (Hu et al., JCB 2002; doi: 10.1083/jcb.200112086) the first description of an apical proteome (Hu et al., PLoS Path 2006; 10.1371/journal.ppat.0020013), the description of a tilted arrangement of the rings in Plasmodium versus Toxoplasma (Kudryashev et al., Cell Microbiol 2012; doi: 10.1111/j.1462-5822.2012.01836.x) and the discovery of apical located proteins that are essential for conoid formation (Tosetti et al., eLife 2020; 10.7554/eLife.56635) to name a few.

If intended for a broader audience, a cartoon of a conoid complex across the different species investigated and discussed here would help for visual guidance highlighting the similarities and differences

Authors’ response: This is a good suggestion and we are presently preparing a schematic of all stages studied and supporting this with electron microscopy.

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

In this work, Koreny et al. characterized the localization of a new collection of conoid proteins in Toxoplasma gondii as well as in several different stages of Plasmodium berghei. The authors discovered that these proteins are located in several distinct substructures in Plasmodium and are expressed in a stage-specific manner. The data are of high quality, well‐organized, and well presented. The paper is well written. The introduction, in particular, was a pleasure to read. This reviewer (Ke Hu) does not have any new experiments to suggest.

However, while the authors present LOPIT+BIOID as a powerful approach to identify conoid proteins, implying that it is more reliable than previously published approaches (see below), the manuscript includes no data to show what the false positive or false negative rate is with the current approach, nor any estimate of how many conoid proteins were missed entirely.

Authors’ response: In our validation of putative conoid-associated proteins identified by the hyperLOPIT+BioID approach we reporter-tagged 18 proteins to resolve their cellular location by microscopy. All 18 were verified as being located at the site of the conoid. So, by this measure there were no false positives. The veracity of the hyperLOPIT data was also confirmed across other cell compartments in our report where 62 proteins were reporter-tagged from which there were no false positive assignments of cell location (Barylyuk et al., 2020, Cell Host & Microbe, in press:doi:10.1016/j.chom.2020.09.011), bioRixv: https://doi.org/10.1101/2020 .04.23.057125).

Estimating false negatives is more difficult, but we know that these would occur as for any mass spectrometry-based detection technique. However, we have not claimed to have been exhaustive, nor was this required to answer our central question of are there conserved conoid-associated proteins throughout Apicomplexa? To address this question, we required a good sample of proteins, and the methods that we have employed provided this.

Page 7: "Previous identification of conoid complex proteins used methods including subcellular enrichment, correlation of mRNA expression, and proximity tagging (BioID) (Hu et al. 2006; Long, Anthony, et al. 2017; Long, Brown, et al. 2017). Amongst these datasets many components have been identified, although often with a high false positive rate. We have found the hyperLOPIT strategy to be a powerful approach for enriching in proteins specific to the apex of the cell, and BioID has further refined identification of proteins specific to the conoid complex region."

The authors should state whether the candidate proteins were chosen in an unbiased way or not.

Authors’ response: Candidate proteins selected for validation by microscopy were not biased for any known likelihood of being associated with the conoid, other than our proteomics data what we were seeking to test. However, we did preference proteins with the following traits, 1) proteins with strong corresponding gene knockout fitness phenotypes from published studies, 2) proteins with some evidence of conserved functional domains, and 3) genes with orthologues found in Plasmodium spp. and other apicomplexans. These traits were chosen with future functional studies in mind where proteins might be more informative of conoid-related functions and relevance in other apicomplexans. All validated proteins, however, were otherwise uncharacterised and, therefore, were not knowingly biased for more likely conoid-association over others discovered by our proteomics approach. We now include the following statement.

“All proteins selected for validation were previously uncharacterised and with no a priori reason to be identified as conoid-associated other than our proteomics data.”

If so, how many proteins were localized to the conoid and how many were not?

Authors’ response: as stated above, we observed no false positives from the sample of 18 protein locations verified by microscopy.

Related to this, the majority (14 out of 20) of the conoid proteins identified by LOPIT+BIOID in this paper were previously identified as conoid candidate proteins in Hu et al's 2006 paper, based on the number of peptides retrieved from the conoid enriched vs depleted fractions. Those data (see below) have been available from ToxoDB for many years and should be acknowledged.

Accession# - conoid enriched : conoid depleted (from Hu et al. 2006)

222350 - 2:0

274120 - 3:0

291880 - 1:0

301420 - 3:1

246720 - 4:0

258090 - 10:0

266630 - 8:1

208340 - 4:2

253600 - 1:0

306350 - not found

250840 - 1:0

292120 - not found

219070 - not found

274160 - not found

320030 - 7:1

227000 - 10:0

278780 - not found

284620 - not found

295420 - 6:0

297180 - 4:0

Authors’ response: Proteomic methods and mass spectrometry have experienced revolutionary advances since this 2006 study was conducted. These include improvements in both sensitivity and quantitation accuracy. The Hu et al 2006 study provided an exciting first step towards conoid protein discovery. However, by their original estimation, at least 35% of their putative conoid-specific proteins were identifiable as false positives (e.g. ribosomal proteins) and this estimate could not account for the majority of uncharacterised proteins whose potential for false positive attribution to the conoid was untested. From almost 300 proteins, this study only validated four as associated with the conoid. The further proteins listed above were not validated as conoid proteins in the Hu et al study and, therefore, could not be distinguished from the many false positives reported in their work. In our Table 1, we have acknowledged the Hu et al study for the select proteins that they established as conoid proteins in their study.

To further assess the utility of this 2006 conoid-enriched proteome we sorted the Hu et al detected proteins on our full hyperLOPIT assignments. Of the proteins that were reported by Hu et al as either exclusive to the conoid-enriched fraction or enriched by at least 2-fold over the conoid-depleted fraction, 15% were assigned to the apical 1 and 2 clusters (representing the relevant compartments to the conoid complex). Thus, according to the hyperLOPIT data these represent the true positives found in this study and 13 of these proteins were independently validated as conoid-associated by us. Significantly, however, 85% of the conoid-exclusive and conoid-enriched proteins from Hu et al (2006) were allocated to a non-apical location with 99% probability by hyperLOPIT, and, during our validation of 62 assignments we verified the alternative location of eight of these. False positives, therefore, greatly outnumbered true positives in this earlier dataset. This high rate of false positives in subcellular isolation proteomics is typical of the challenges that this method faces, and this was the rationale for and strength of the alternative hyperLOPIT approach. Given the overall relatively low level of conoid specificity in the earlier work we do not think that there is value in making specific protein-by-protein reference to it.

Reviewer #3 (Significance (Required)):

see above

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

This manuscript details the further use of the hyperplexed Localisation of Organelle Proteins by Isotope Tagging (hyperLOPIT) that the group has previous published using T. gondii tachyzoites by combining this with BioID and super-resolution microscopy in order to uncover new proteins that form part of a structurally known and functionally elusive conoid. The authors conclusively identified new proteins that localise to the conoid structure in T. gondii and also excitingly showed that not only is this structure found in all invasive forms of plasmodium (using the P. berghei model) but there also is a different molecular make up in the blood stage merozoites which have a slightly reduced number of proteins (or possible as yet unknown alternatives) compared to ookinetes and sporozoite conoid structures. This study is scientifically sound and the conclusions reached are well supported by the results presented.

**Major Comments:** No major comments

**Minor Comments:**

1)While both the introduction and discussion and well written and detailed they could both be a little more concise.

Authors’ response: We take this as a style recommendation, but we note that the other reviewers commented on the text’s “eloquence” and that the introduction in particular was a “pleasure to read”. We take these comments as votes of confidence in the current form.

2)Selection of the 5 new genes in Tg to be tagged (top pg 5) it was not clear as to the selection criteria for these 5.

Authors’ response: Please see the same query, and response with modified text, made by Reviewer #3.

This also leads to the second part of this question where there appears to be some genes missing from Table 1 and Table S1, specifically those found in both SAS6L and RNG2 BioID. It was mentioned that 25 were identified in both SAS6L and RNG2 BioID. In Table 1 (there are 23) there is no mention of 223790, 281650, 224700, and 293540 but they are in the Table S1 (assuming these 4 are not selected in this study for tagging) but in table S1 (there are 25 listed) 216080 (AKMT) and 234250 (CIP1) that are in the Table 1 as being identified in both SAS6L and RNG2 BioID are absent from the Table S1 does this mean there are actually 27 or was the indication of identified in both SAS6L and RNG2 BioID for 216080 (AKMT) and 234250 (CIP1) in Table 1 a mistake?

Authors’ response: This reviewer has overlooked that Table 1 reports on all currently known conoid associated proteins, including those not detected in the hyperLOPIT data but reported in the literature, whereas Table S1 is exclusively those proteins detected and assigned as ‘apical’ by hyperLOPIT. The reported BioID-detection for each protein is then made within this framework. Thus, the proteins that occur in only one or the other table do so because they don’t satisfy these two sets of criteria. We have rechecked the numbers reported in the text and they are correct.

3)Table 1: There is the fitness score for Pf orthologues but no mention of fitness in Pb (the model used) from the PlasmoGEM screens, considering the authors use the Pb model it would be of interest to add this in the table.

Authors’ response: The Plasmodium berghei PlasmoGEM gene disruption screen were much more limited in number than that for P. falciparum. Consequently, fitness scores were available for only two of the Plasmodium orthologues for which we have location data. We, therefore, thought it was of limited utility to include these data in Table 1, and these data are in the public domain should a reader seek them.

4)Figure 2: The image for localisation with SAS6L for 291880 and 258090 appear to be missing.

Authors’ response: Initially we did not make the separate transgenic cell lines for each protein with both the SAS6L and RNG2 markers. This was because one marker was usually sufficient to resolve the relative location of the protein of interest. However, given this reviewer’s comment and the potential for some extra information to be recovered by using both markers, we have now generated all cell lines necessary for this analysis. We are presently completing the imaging of these new cell lines and these data will be included in the subsequent revision.

5)Figure 3: It is unclear why both SAS6L and RNG2 are not used for all localisations shown (this could be clarified in the text)

Authors’ response: see previous comment.

6)Figure 5: It is a shame only 7 of the 9 plasmodium orthologues were included in the super resolution as there is only 2 more to have the complete set.

Authors’ response: Ideally, we would have been able to achieve this but, the restrictions imposed by the COVID-19 disruption to laboratory access and activities ultimately slightly limited these analyses. However, to answer the central question of whether there is conservation of the Toxoplasma conoid proteome in Plasmodium it was not necessary to perform super resolution imaging for all of these proteins. The major outcome of this study, therefore, is not affected by this.

7)Figure 6: As with Figure 5 it would be better if more were included in the super-resolution images in this sporozoite stage.

Authors’ response: Same response as above. Generation of sporozoites requires passage through the mosquito vector so this is even more resource-intensive than generation of ookinetes that can be differentiated in vitro from mouse-derived parasites. Again, the answers to the central questions posed by this study do not require these further, high resolution, data.

8)Figure 7: This would be improved with at least a selection (or even all 6) to have the super-resolution images (possibly even with free merozoites)

Authors’ response: We did apply 3D-SIM imaging to fixed merozoites, however, unlike ookinetes and sporozoites, the imaged fixed material was inferior to the live cell GFP imaging that we have included. This likely reflects the poorer fixation properties of Plasmodium merozoites that is a challenge of these cell forms that is widely experienced by Plasmodium researchers. We do not have access to a 3D-SIM microscope within a containment laboratory necessary for handling viable parasites, therefore, could not attempt to image live material with this instrument. Again, the answers to the central questions posed by this study do not require these further, high resolution, data

9)As there are numerous new protein identified in 2 different parasites and with the composition of the conoid differing at different stages it would be beneficial to have some sort of schematic model of the apical complex in Tg and Pb indicating where each new protein localises

Authors’ response: In response to this reviewer, and reviewer #2’s suggestion, we are now preparing schematic models of the apices of all of the relevant organism stages.

Reviewer #4 (Significance (Required)):

The authors have combined expert mass spectrometry and super-resolution microscopy to identify new components of the conoid in Tg and added to the knowledge that will help to uncover the function of the structure. But perhaps the most significant is the conclusive identification of the conoid in all 3 invasive stages of the plasmodium parasite. Until now it was widely accepted that the conoid was missing in plasmodium and to uncover multiple proteins that appear to make up and constitute this structure in Plasmodium is highly significant and clear of interest to the Apicomplexean field. Furthermore the suggestion that the conoid differs in the molecular makeup within Plasmodium depending on stage is very intriguing and clearly of interest. This paper expertly combined cutting-edge proteomic and microscopy to identify the conoid in Plasmodium. This manuscript would have a broad readership in parasitology, proteomics, and cell biology

Our expertise is largely in molecular parasitology and microscopy

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Referee #3

Evidence, reproducibility and clarity

This manuscript details the further use of the hyperplexed Localisation of Organelle Proteins by Isotope Tagging (hyperLOPIT) that the group has previous published using T. gondii tachyzoites by combining this with BioID and super-resolution microscopy in order to uncover new proteins that form part of a structurally known and functionally elusive conoid. The authors conclusively identified new proteins that localise to the conoid structure in T. gondii and also excitingly showed that not only is this structure found in all invasive forms of plasmodium (using the P. berghei model) but there also is a different molecular make up in the blood stage merozoites which have a slightly reduced number of proteins (or possible as yet unknown alternatives) compared to ookinetes and sporozoite conoid structures. This study is scientifically sound and the conclusions reached are well supported by the results presented.

Major Comments: No major comments

Minor Comments:

1)While both the introduction and discussion and well written and detailed they could both be a little more concise.

2)Selection of the 5 new genes in Tg to be tagged (top pg 5) it was not clear as to the selection criteria for these 5. This also leads to the second part of this question where there appears to be some genes missing from Table 1 and Table S1, specifically those found in both SAS6L and RNG2 BioID. It was mentioned that 25 were identified in both SAS6L and RNG2 BioID. In Table 1 (there are 23) there is no mention of 223790, 281650, 224700, and 293540 but they are in the Table S1 (assuming these 4 are not selected in this study for tagging) but in table S1 (there are 25 listed) 216080 (AKMT) and 234250 (CIP1) that are in the Table 1 as being identified in both SAS6L and RNG2 BioID are absent from the Table S1 does this mean there are actually 27 or was the indication of identified in both SAS6L and RNG2 BioID for 216080 (AKMT) and 234250 (CIP1) in Table 1 a mistake?

3)Table 1: There is the fitness score for Pf orthologues but no mention of fitness in Pb (the model used) from the PlasmoGEM screens, considering the authors use the Pb model it would be of interest to add this in the table.

4)Figure 2: The image for localisation with SAS6L for 291880 and 258090 appear to be missing.

5)Figure 3: It is unclear why both SAS6L and RNG2 are not used for all localisations shown (this could be clarified in the text)

6)Figure 5: It is a shame only 7 of the 9 plasmodium orthologues were included in the super resolution as there is only 2 more to have the complete set.

7)Figure 6: As with Figure 5 it would be better if more were included in the super-resolution images in this sporozoite stage.

8)Figure 7: This would be improved with at least a selection (or even all 6) to have the super-resolution images (possibly even with free merozoites)

9)As there are numerous new protein identified in 2 different parasites and with the composition of the conoid differing at different stages it would be beneficial to have some sort of schematic model of the apical complex in Tg and Pb indicating where each new protein localises

Significance

The authors have combined expert mass spectrometry and super-resolution microscopy to identify new components of the conoid in Tg and added to the knowledge that will help to uncover the function of the structure. But perhaps the most significant is the conclusive identification of the conoid in all 3 invasive stages of the plasmodium parasite. Until now it was widely accepted that the conoid was missing in plasmodium and to uncover multiple proteins that appear to make up and constitute this structure in Plasmodium is highly significant and clear of interest to the Apicomplexean field. Furthermore the suggestion that the conoid differs in the molecular makeup within Plasmodium depending on stage is very intriguing and clearly of interest. This paper expertly combined cutting-edge proteomic and microscopy to identify the conoid in Plasmodium. This manuscript would have a broad readership in parasitology, proteomics, and cell biology

Our expertise is largely in molecular parasitology and microscopy

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Referee #2

Evidence, reproducibility and clarity

In this work, Koreny et al. characterized the localization of a new collection of conoid proteins in Toxoplasma gondii as well as in several different stages of Plasmodium berghei. The authors discovered that these proteins are located in several distinct substructures in Plasmodium and are expressed in a stage-specific manner. The data are of high quality, well‐organized, and well presented. The paper is well written. The introduction, in particular, was a pleasure to read. This reviewer (Ke Hu) does not have any new experiments to suggest.

However, while the authors present LOPIT+BIOID as a powerful approach to identify conoid proteins, implying that it is more reliable than previously published approaches (see below), the manuscript includes no data to show what the false positive or false negative rate is with the current approach, nor any estimate of how many conoid proteins were missed entirely.

Page 7: "Previous identification of conoid complex proteins used methods including subcellular enrichment, correlation of mRNA expression, and proximity tagging (BioID) (Hu et al. 2006; Long, Anthony, et al. 2017; Long, Brown, et al. 2017). Amongst these datasets many components have been identified, although often with a high false positive rate. We have found the hyperLOPIT strategy to be a powerful approach for enriching in proteins specific to the apex of the cell, and BioID has further refined identification of proteins specific to the conoid complex region."

The authors should state whether the candidate proteins were chosen in an unbiased way or not. If so, how many proteins were localized to the conoid and how many were not? Related to this, the majority (14 out of 20) of the conoid proteins identified by LOPIT+BIOID in this paper were previously identified as conoid candidate proteins in Hu et al's 2006 paper, based on the number of peptides retrieved from the conoid enriched vs depleted fractions. Those data (see below) have been available from ToxoDB for many years and should be acknowledged.

Accession# - conoid enriched : conoid depleted (from Hu et al. 2006)

222350 - 2:0

274120 - 3:0

291880 - 1:0

301420 - 3:1

246720 - 4:0

258090 - 10:0

266630 - 8:1

208340 - 4:2

253600 - 1:0

306350 - not found

250840 - 1:0

292120 - not found

219070 - not found

274160 - not found

320030 - 7:1

227000 - 10:0

278780 - not found

284620 - not found

295420 - 6:0

297180 - 4:0

Significance

see above

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Referee #1

Evidence, reproducibility and clarity

The authors study proteins localised to the apical end of the highly polarised parasites causing Toxoplasmosis and malaria. They find new proteins using BioID and examine the localisation of these along with recently identified proteins in the two different parasites. They key question they address is whether there is a conservation of the apical components in these distantly related parasites as well as in some even more distantly related organisms. This is an important question as the apical part comprises many essential proteins of invasion of host cells and shows a unique structure that defines the apicomplexans as a group. The apical structure can be highly elaborate such as in T. gondii and less elaborate as in P. falciparum. The authors now show that there is a large conservation between the species in the protein makeup of the apical end. The experiments are well performed, displayed and discussed and there is no doubt about the validity of the presented results. The text is eloquently written, if at times a bit wordy. My only main suggestion would be to possibly add data on gene disruption of the two candidates (0310700 and 1216300) that are not detected in blood stage parasites but in the insect stages. A deletion of these should be technically straightforward and would show whether the proteins are important to the parasite. Likely not all of the now many proteins are essential for the parasites but these are good candidates to rapidly investigate. But showing a functional impact might convince editors at certain journals.

Other suggestions in chronological order (line numbers would have helped)

title: maybe write 'conoid complex proteome'

abstract: not sure about the use of the words instrument and substructures

page 2 last lines: is tubulin monomeric or polymerized?

page 3 name protein talked about in 9th line

third paragraph: mention previous proteomics studies e.g. from Ke Hu (mentioned later in discussion)

first paragraph or results could go into introduction

page 4: add reference after BioID

page 5: add definitions of the conoid; what technique was used to report YFP-SAS6?

page 7: 'showed similar localisation' instead of 'phenocopied'?; add reference after ookinete stage; add expression levels from PlasmoDB to the Table 1 data at least for merozoites, ookinetes and sporozoites or add separate table for the 9 proteins in supplement

Discussion: Maybe discuss that the conoid complex is a cytoskeletal structure and that the other cytoskeletons (actin, microtubules, subpellicular network) also differ between the species investigated in their composition and overall architecture

page 9: at least two proteins could be deleted as they seem to not confer any growth defect on blood stages (see main comment)

Apart from classic TEM images also Cryo EM data is available for apex of merozoite and sporozoite. Worth to discuss?

Add and discuss the recent work from Curr Biol and EMBO J of the Yuan lab on ookinete formation?

Significance

The paper provides a conceptual advance over previous data as it shows clearly a high level of conservation of the protein components of the conoid complex. It could introduce a new terminology for these important apical structure of Apicomplexan parasites and provides a good basis to dissect the molecular functions. As it stands all scientists investigating Plasmodium and Toxoplasma invasion of host cells will be highly interested in this study, most scientists researching apicomplexan organisms should be and some evolutionary scientists will be interested in this study.

Key papers in the field are the discovery of the Toxoplasma conoid as a highly twisted microtubule-like structure (Hu et al., JCB 2002; doi: 10.1083/jcb.200112086) the first description of an apical proteome (Hu et al., PLoS Path 2006; 10.1371/journal.ppat.0020013), the description of a tilted arrangement of the rings in Plasmodium versus Toxoplasma (Kudryashev et al., Cell Microbiol 2012; doi: 10.1111/j.1462-5822.2012.01836.x) and the discovery of apical located proteins that are essential for conoid formation (Tosetti et al., eLife 2020; 10.7554/eLife.56635) to name a few.

If intended for a broader audience, a cartoon of a conoid complex across the different species investigated and discussed here would help for visual guidance highlighting the similarities and differences

Reviewer #2

In this manuscript, the authors applied Gaussian Process regression to drug response data and attempted to utilize the estimates of uncertainty from these regression to improve on drug response curve fitting and biomarker discovery. Their approach and application case is an interesting one that deserves further investment and attention. However, I have substantive concerns with the current manuscript draft and would recommend to the authors that these concerns be addressed.

1) Figure 3 and the accompanying text section of the main document seems to be focused on characterizing estimation uncertainty, which appears to simply be the between-sample dispersion of the dose-response curve (or summary statistics thereof) from replicate runs. The main conclusion seems to be that drug compounds with partial responders are the ones with the greatest between-sample dispersions.

What is missing from this Figure and accompanying text is a comparison of these results with analogous ones for the observation uncertainty to help readers understand why one approach may be preferred over the other.

2) Figure 5A compares the posterior probability from the Bayesian test (presumably accounting for estimation uncertainty) against the q-value from an ANOVA test. The q-value should be the False Discovery Rate, which controls for the proportion of false positives. This does not seem to be directly comparable to a posterior probability. The authors should clarify why a comparison of proportion to posterior probability is reasonable.

3) The authors do not appear to have demonstrated how estimation uncertainty can improve on drug response curve fitting or biomarker discovery?

For the former, the fitted curves using standard approaches appear similar to those fitted using GP regression, as the authors seemed to have focused on those curves where the two approaches are concordant and as the IC50 value differences appear minimal for those cases where IC50 is within the tested concentration range. The greatest differences are seen for those cases where IC50 values are outside the tested concentration ranges, but these cases were not in focus in the text. In addition, for these cases, it is unclear if relying on curve fits from GP regression makes sense because they are also the cases with the highest estimation uncertainty.

For the latter, it appears that every significant biomarker identified using Bayesian posterior probability is also significant by ANOVA (using a standard q-value < 0.05 cutoff).

Reviewer #1

The authors propose two related (though distinct) methods for the improvement of pharmacological screening analysis and related biomarker analyses. The first is a Gaussian process (GP) approach to dose-response curve fitting for the estimation of IC50, AUC, and related quantities. The goal of this method is to improve point and uncertainty estimates of these quantities through more flexible functional specification and outlier-robust error modeling. The second method is a hierarchical Bayesian approach to biomarker association analysis. This incorporates uncertainty estimates produced by the GP modeling with the aim of providing more sensitive association analyses with fewer false positives.

The combination of methods presented has some potential. Flexible modeling of dose-response relationships and better estimation of uncertainty are interesting axes to wring more information out of large-scale screening datasets. There are a few areas to shore up in the paper to increase confidence in the empirical results and generalizability of the methods.

1) There are a number of fixed parameters in the proposed methods, and the calibration procedure used to set these is unclear to me. For the GP models, there are a set of noise parameters for Beta mixture and the length scales and variance parameter for the kernel. I'm not sure how one would generalize the GP methods to other screening datasets as a result of this ambiguity (e.g., how would one determine appropriate noise parameters?). For the hierarchical Bayesian biomarker association model, we have prior scale parameters related to both the effect size and variance parameters. The number of researcher degrees of freedom introduced by these tuned parameters also raises some concerns about the sensitivity of empirical results (e.g., 24 clinically established biomarkers and 6 novel) to these choices. It's not clear if we're seeing a corner case or a robust result. I think the work would benefit from both sensitivity analyses with respect to tuned parameters and guidance on or methods for their estimation. The latter is particularly important if other researchers hope to employ these methods in a different context.

2) The proposed hierarchical Bayesian approach to biomarker association analysis is a reasonable start, but it was unclear to me whether changes in performance stemmed from correcting misspecification in original ANOVA or the use of uncertainty estimates. I suggest comparing results to a heteroskedasticity-robust estimator (e.g., HC3, see Long and Ervin, 2000), which would be valid under the stated model without the requirement for explicit uncertainty estimates or priors. The transformations and tuning applied to uncertainty estimates in this context also make generalization of the approach challenging. The need for the c (power) parameter suggests a potential misspecification or miscalibration at some point in the modeling chain. It would be useful to understand this misspecification better, particularly for researchers hoping to extend or reuse these methods.

3) The GP method provides reasonable estimates of uncertainty, but it would be useful to see them compared to those from the sigmoid model (e.g., from the delta method). It wasn't clear to me how much of the difference in results is coming from incorporation of uncertainty estimates as opposed to changes in the point estimates.

4) The handling of cases with IC50 beyond the maximum observed dose (extrapolating to 10x the maximum concentration) provided a reasonable starting point, but a few subtleties in the handling of corner cases remain unaddressed (e.g., GPs allow positive slope at right edge of range). It would be useful to provide a more general, systematic procedure to address these. Imposing monotonicity may not be the best path, but additional guidance for researchers applying these methods in other contexts would help.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 3 of the manuscript.

Summary

This manuscript presents two statistical approaches to evaluating drug effect measurements and associations between biomarkers, for dose curve data. Measurements of these kinds are made in many contexts, and frequently reported without accounting well for measurement uncertainties. A statistical framework of this kind will be widely useful and should be frequently applied.

Reviewer #3

This manuscript reports the first description of a eukaryotic-like Bin/Amphiphysin/RVS (BAR) domain protein in a bacterium (Shewanella oneidensis MR-1), BdpA, with conserved roles in membrane curvature control during outer membrane vesicle (OMV) formation. Consistent with this, a BdpA-defective mutant had defects in the size and shape of redox-active membrane vesicles and formed outer membrane extensions (OMEs) lacking the characteristic tubular structure. Heterologous expression of the BdpA proteins in model (Escherichia coli) and non-model (Marinobacter atlanticus) bacteria hosts promoted OME formation. The authors propose BdpA as a new subclass of prokaryotic BAR proteins with eukaryotic-like roles in membrane curvature modulation. This is an interesting finding that could be strengthened with topological studies of BdpA in OMV/OME and quantitative analyses to validate the many qualitative microscopic observations.

Numbered summary:

1) To my knowledge this is the first description of a BAR-domain protein in a prokaryotic organism. But the role of prokaryotic proteins with amphipathic α-helical domains in membrane binding/curvature is not new. A review by Dowrkin1 describes some of these structural homologs and their role in membrane binding and curvature control via their amphipathic domains (e.g., Bacillus subtilis SpoVM, which controls forespore membrane curvature during sporulation using its helical domain). This information is important in the introduction and could help with the phylogenetic analyses (comment 4 below).

2) I am having a hard time reconciling the presence of a galactose-binding domain in BdpA and LPS sugar binding. This would suggest that the proteins coat the OMV rather than interacting with the periplasmic side of the outer membrane to promote OMV formation and release (which I somehow assume based on the role of some eukaryotic BARs). The lack of topological studies makes these models highly speculative and weakens some of the conclusions. The paper would be strengthened with the addition of topological studies in OMVs and OMEs.

3) Many experiments rely on microscopic observations of cells, OMVs and OMEs to support conclusions based on (at most) semiquantitative data. These experiments require validation with methods that quantitatively determine critical variables such as OMV size and size distribution. Also note the microscopic methods are poorly described or not described at all in the methods section. Thus, it is not clear how many cells they examined microscopically and how many biological replicates (cultures) they used. The variability associated with this type of microscopic assessments makes sample size (number of cells, typically in the hundreds) and replication in independent cultures critical.

4) Many of the branch points in the phylogenetic tree (Fig. 5) have very low confidence values. The authors did not provide the alignments so I could not evaluate the accuracy of the approach to offer suggestions for improvement. The predictive value of the tree may improve by including prokaryotic amphipathic helical domains such as those from SpoVM, MinD and FtsA. These issues are not as concerning in the tree presented in Fig. S6 although I note that this tree is supposed to show the distribution of "BdpA orthologs in other prokaryotes" but most of the branches are for eukaryotic proteins. I also note that the Methods section describes important results about the homology (or lack of homology) between BdpA and other prokaryotic and eukaryotic proteins. This information is more appropriate in the Results section.

References:

1) Dworkin, J. Cellular polarity in prokaryotic organisms. Cold Spring Harbor perspectives in biology 1, a003368-a003368, doi:10.1101/cshperspect.a003368 (2009).

2) Gorby, Y. et al. Redox-reactive membrane vesicles produced by Shewanella. Geobiology 6, 232-241, doi:10.1111/j.1472-4669.2008.00158.x (2008).

Reviewer #2

Some Gram-negative bacteria, such as Shewanella oneidensis, produce outer membrane extensions (OME) that mediate electron transfer to extracellular substrates. Many of the players involved in the transfer of electrons via these nanowires have been discovered but the mechanisms of outer membrane remodeling have remained mysterious. Here, Phillips, Zacharoff, and colleagues, identify BdpA as a protein that stabilizes OMEs in Shewanella oneidensis and perhaps displays outer membrane remodeling activity in other bacterial species. Given its homology to eukaryotic BAR-domain proteins, the authors suggest that BdpA and its homologs define the first prokaryotic family of BAR proteins or pBARs.

This works tackles a number of significant questions that span broad areas of microbiology and cell biology. First, it explores a critical area of bacterial cell biology: how do gram negatives remodel their outer membranes? Second, it focuses on an underappreciated aspect of extracellular electron transfer, an activity widespread amongst bacteria with clear relevance to basic and applied fields. Finally, it provides a possible glimpse into the evolution of BAR-domain proteins which play diverse cellular roles in eukaryotes. Despite the substantial advances presented here, I have some concerns which, if addressed, can lead to more certain conclusions about the cellular role of BdpA.

1) I liked the comparative proteomics approach as a tool to identify unique OME components. I was surprised that the two fractions differed so much in their protein composition. Based on the materials and methods the OM and OME fractions were isolated from cells grown under very different conditions. Could this account for the large differences between these two fractions? Looking at the list of proteins enriched in either fraction is there any indication of significant contamination from other cellular fractions? What controls were used to ensure that the purification procedure was working effectively?

2) The authors conclude that the OM vesicles are conductive. However, some controls are needed since other cellular components (such as OM fractions containing Mtr proteins) may have contaminated the OME fraction. Is the OME fraction "enriched" for this activity compared to just the OM fraction?

3) Is BdpA really a BAR-domain protein? The authors use computational tools (such as BLAST and homology modelling) to posit that BdpA is a BAR-domain protein. This hypothesis is strengthened by the phenotype of mutants missing bdpA. While OMEs are not absent, their architecture is visibly altered which may point to some instability in the membrane extensions. Significantly, BdpA is sufficient to induce OME-like structures when expressed in planktonic Shewanella cells, a condition during which OMEs are not normally produced. However, as authors state, BdpA barely meets the cutoff (as set by the program used) for a BAR-domain protein. Furthermore, some of its homologs that share high levels of sequence identity don't pass the bar set by these computational methods. However, we cannot say that BdpA is actually a BAR-domain protein. Its effects on membrane stability could be indirect or the result of binding to outer membrane features in a manner distinct from other BAR proteins. Therefore, some biochemical corroboration of its activity on membranes or structural data are needed to confirm its relationship to eukaryotic Bar domain proteins. On a minor note I would prefer "bacterial" rather than "prokaryotic" since BdpA Bar-like domain is not found in archaea. Also, other groups have proposed that bacterial proteins contain BAR domains (for instance, Tanaka et al in reference 28). How similar is BdpA to these proteins?

4) Heterologous expression of BdpA in other bacteria provides one of the most compelling arguments for its central role in producing OMEs. However, the imaging data provided here (at least in my pdf) do not provide the clearest evidence for induction of OMEs in M. atlanticus and E. coli. This is especially the case with the E. coli images. The extended web of staining in 4c does not resemble the tubules seen in S. oneidensis. It would be great to have some electron microscopy data and/or higher resolution fluorescence images of these bacteria as corroborating evidence. Additionally, only a few cells are shown so some quantification of the proportion of cells with OMEs is needed.

5) Other than the predicted signal peptide, does BdpA have any predicted features that indicate it is an outer membrane protein? The authors hypothesize that the putative Galactose-binding domain of BdpA mediates binding to LPS. However, it is also possible that it binds to peptidoglycan components. Therefore, independent data on localization of BdpA via microscopy or higher resolution biochemical fractionation would provide greater confidence that the protein is acting in the appropriate cellular location.

Reviewer #1

In the manuscript "A Prokaryotic Membrane Sculpting BAR Domain Protein" the authors describe the identification of the first bacterial membrane sculpting BAR domain protein, and the characterization of its function. In eukaryotes this protein is important for shaping membrane curvature. Here they identify a protein containing a BAR domain in the bacterium Shewanella oneidensis, which they name BdpA (BAR domain-like protein A). The authors show that BdpA is enriched in outer membrane vesicles (OMVs) and outer membrane extension (OMEs), regulates the size of OMVs and the shape of OMEs. They show this by characterizing and quantifying membrane vesicles and extension comparing WT with a BdpA mutant and the BdpA mutant with heterologous BdpA expression. They further show that heterologous expression of BdpA promotes OME in E. coli.

In my opinion this paper provides solid support for the presence of these proteins in bacteria with an important function in membrane vesicles and membrane extensions.

Minor Comments:

1) In the introduction the authors summarize what is known about BAR eukaryotic protein in terms of membrane localization and their role in membrane curvature and tubulation events. I think it is important to also provide a summary of what is known about the functional biological implication of these proteins in eukaryotes. Namely, if the main function of BAR proteins in eukaryotes is always related to tubulation formation or if there are other functions attributed to these proteins.

2) Contrast and resolution in Figure 3, panel a, is weak making it difficult to see tubules described by the authors.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 3 of the manuscript.

Summary

In this manuscript the authors propose the identification of a novel protein involved in outer membrane remodelling, named BdpA (BAR domain-like protein A). According to the proposed model BdpA has a conserved role in membrane curvature control during formation of outer membrane vesicle (OMV) and of outer membrane extension (OMEs) in Shewanella oneidensis. The authors also provide evidence that heterologous expression of BdpA promotes formation of OMEs in other bacteria (namely in E. coli), and that BdpA is sufficient to induce OME-like structures when expressed in conditions where OMEs are normally not formed. In eukaryotes proteins containing BAR domains are important for shaping membrane curvature. Given the homology of BdpA to eukaryotic BAR-domain proteins, the authors suggest that BdpA and its homologs define the first prokaryotic family of BAR proteins or pBARs, with eukaryotic-like roles in membrane curvature modulation.

Overall, the reviewers think that this is a very interesting study, and provided that further support is obtained to substantiate the proposed model the reviewers agree that the findings described here tackle a number of significant questions of broad interest. However, the reviewers also think that the evidence provided in this manuscript still does not fully support the conclusion that BdpA protein is involved in membrane curvature control as the eukaryotic proteins containing the BAR domains.

We have compiled a list of comments that we hope will help the authors address the concerns of the reviewers to obtain stronger support for the function of BdpA.

1) The reviewers are concerned that some of the conclusions are based on qualitative observations of microscopy analysis of OMVs and OMEs, and quantitative analyses are lacking to validate qualitative observations. As specified in with examples in the list of minor points below the reviewers propose that the data should be re-analyzed to obtain quantitative results. Specifically, a size distribution analysis could be applied to some microscopy data. Also note that the microscopy methods are poorly described, and as the calculation methods used are not fully available it is difficult to understand if the appropriate methods were used. Please specify how many cells were examined microscopically and how many biological replicates (cultures) were used in each experiment.

2) Statistical analyses were not always the most accurate. In figure 2 unpaired t-test was used for samples that have high variance, this approach may inflate the statistical difference between the strains. For figure 2 a histogram of size distribution analyses could be shown for each strain.

3) The reviewers are concerned that the proteomic data is not clear enough to conclude that the BdpA protein is localized to or enriched in OMV/OME. Could the results be complemented with some other method to confirm BdpA localization? The reviewers are particularly concerned by the fact that a large number of proteins were identified in the OMV fraction. Could it be that some of the OMV/OME fractions were contaminated? What controls were used to ensure that the purification procedure was working effectively? Could the data be strengthened by some quality control analyses to determine how many of those proteins are actually predicted to localize to the outer membrane and periplasm? From the methods it seems that the culture conditions used to prepare the OM versus OMV were different, is this so? If yes, why were the culture conditions different? This could affect protein expression? Please include the detailed growth conditions in the method section.

4) The conclusion that BdpA is a BAR-domain protein is largely based on homology. The supplementary information file includes homology models that show striking similarity with eukaryotic BAR proteins. However, as the authors state, BdpA barely meets the cutoff for a BAR-domain protein. The results with the phenotype of the BdpA mutant, complementations and sufficiency data provide good support to the functional role of BdpA in membrane remodelling. However, the effect of BdpA on membrane stability could be indirect or the result of binding to outer membrane features in a manner distinct from other BAR proteins. Could these results be strengthened with some biochemical corroboration of its activity on membranes or structural data to confirm its relationship to eukaryotic Bar domain proteins? Or structural data to confirm its relationship to eukaryotic BAR domain proteins?

5) The reviewers propose that the paper would be strengthened with the addition of topological studies in OMVs and OMEs. The reviewers had problems in reconciling the presence of a galactose-binding domain in BdpA and LPS sugar binding. The authors hypothesize that the putative Galactose-binding domain of BdpA mediates binding to LPS. However, it is also possible that it binds to peptidoglycan components. This would suggest that the proteins interact with the periplasmic side of the outer membrane rather than coat the OMV to promote OMV formation and release (which one could assume based on the role of some eukaryotic BARs). The addition of topological studies (or some biochemical approach) could make these models less speculative, strengthening the conclusions.

6) Heterologous expression of BdpA in other bacteria provides important compelling arguments for its central role in producing OMEs. However, the imaging data provided do not provide the clearest evidence for induction of OMEs in M. atlanticus and E. coli. This is especially the case with the E. coli images. The extended web of staining in 4c does not resemble the tubules seen in S. oneidensis. It would be great to have some electron microscopy data and/or higher resolution fluorescence images of these bacteria as corroborating evidence. Additionally, only a few cells are shown and quantification of the proportion of cells with OMEs is needed. Thus, as already discussed in point 1, quantitative analyses could improve this important point.

Reviewer #4

This is an innovative and very interesting study reporting the correlation of extracted neural timescales and expression of NMDA and GABA_a receptor subunits amongst others.

Comments:

-definition of timescale is missing in the introduction. Fast and slow responding to sensory versus cue related information reflects a circular definition of timescales.

-the results text say that the aperiodic components is interpreted as time scale but not how the inference is made, i.e. what quantity is interpreted as time scale.

-it is difficult to keep track of which timescales are referred to when in the text, e.g. the authors start referring to neuronal timescales after having discussed ECOG based time scales and spike timescales. It seems important for cleanly separating the source of the timescale to denote them with a unique label depending on the source data that gives rise to them. Why not use a subscript for spike, epiduralECoG, subduralECoG, intracranialLFP, ... ?

-the article seems to assume that mRNA expression for specific receptor subunits correspond to the density of expression of those receptors. It seems important that this is made explicit (if correct) and that a reference is given that shows this relationship.

-line 142 refers to "task-free ECoG recordings in macaques" but does not clarify where the data comes from. No reference is provided.

Reviewer #3

In this paper entitled 'Neuronal timescales are functionally dynamic and shaped by cortical microstructure', Gao et al. use open access databases to address two distinct questions: 1) the relationship between hierarchically organized variations in neuronal timescales and brain gene expression and 2) the effect of task and age onto the neuronal timescales of a given cortical regions.

Overall, this is a well-designed study and the combination of open access databases is well organized and astutely exploited. I, in particular, very like the analysis that tests whether variations in gene expression still accounts for variations in neuronal timescales when the main gradient effect is regressed out. Below are my comments on the manuscript.

1) For the non-specialist reader, the concept of neuronal timescales that is central to the paper should be defined more explicitly in the introduction ('neuronal timescales' appear in paragraph 3, while it gets defined in paragraphs 1 and 2).

2) In figure 2B, some T1w/T2w values are above values of 2, which is not standard. Likewise, several outliers can be observed. This might have impacted the estimation of the regression slope. This slope currently matches the one from Burt et al. 2018, although the data point distribution is different.

3) Figure 4B is contradicting figure 2C as the evidenced timescale hierarchy is different (comparing PC, PFC and OFC). Please explain.

4) Figure 4B and 4C, please show actual data points and justify parametric tests.

5) Figure 4C: how consistent is the increase in delay period timescales across areas within each subject. In other words, is this a general property of the brain, task-related effects resulting in a non-specific adjustment in neuronal timescales or are there regional differences in the reported increase (you might want to exclude the PFC from the analysis to remove task related effects).

6) The manuscript addresses two distinct aspects of neuronal timescales: their relationship to local microarchitecture and their dynamics as a function of task or age. Although there is obviously a strong inter-relationship between these two aspects, this deserves a more extensive discussion. For example, in relation with the previous point, if local microstructural properties predict neuronal timescales, why is it that timescale changes during the delay seem to be ubiquitous (or are they)? And why should such changes (that are overall in the same range) correlate with subject performance in the PFC but not in the other areas? How does this relate to the aging observations? Although this discussion is bound to be speculative, I think it is important in order to strengthen the link between these two independent avenues of the paper, and to enrich the discussion about the functional role of these dynamic changes in neuronal timescales.

7) Given the described age-related effect, did the authors check that the different databases they used sampled from subjects with the same age distribution.

8) Legend of figure 1 is not self-explanatory and a lot of the symbols and information plotted in the figures are not explained. Unfortunately, this information is also missing from the result section.

9) Figs 3E and 3F are mislabeled as 4E and 4F.

10) Generally speaking, given that the main text itself is very dense, figure legends should be more self-explanatory. Quite often, figure detail description and contextual information are missing both from the text and the figures. This also applies to the supplementary figures.

Reviewer #2

Overall, this is an interesting manuscript and a well-done study. The main finding is that neural timescales, as quantified through the decay of the power spectrum, vary over cortical regions and are correlated with genes that regulate ionic and structural properties of neurons. The findings aren't terribly surprising and the computational impact on cognition and aging remains unclear (other than showing differences), but the overall approach is novel and interesting.

I have an overarching concern, which is that the manuscript is written to be dense yet terse, which makes it harder to read, particularly given the complexity of the analyses. It feels like it was written for a journal with extreme word limitations. The manuscript would be overall improved if the authors would "loosen their belt" and explain the findings and methods in more detail.

What are "these" limitations on line 96?

Figure 1e: how is r2=1 when the dots do not fall on the line?

I'm confused about the description of the methods on page 5. For example, "we can estimate neuronal timescale from the 'characteristic frequency'" which implies a peak in the spectrum. Yet in the next sentence they write that they extract timescale from aperiodic components.

Page 7: Are these markers also correlated with cell packing density? If so, it's possible that denser neural networks have longer timescales.

Relatedly, how strongly inter-correlated are these genetic markers across the cortex? The authors mostly take a mass-univariate approach except for showing gene-PC1 in Figure 3a. There isn't enough information shown to evaluate whether the top PC is suitable, or whether this PC comprises many/all gene contributions or is driven by a small number, etc.

I'm missing the modeling results. They appear as a schematic in figure 1 and are mentioned in the Methods section. Was this model actually used somewhere?

Reviewer #1

These findings are a significant advance in comparison to previous work like Murray et al. (2014) and Dotson & Gray (2018 - please cite here) in the sense that brain-wide hierarchy is considered, whereas previous work considered a smaller set of brain areas. Furthermore, several other interesting correlations are reported with timescales. Overall the analyses appear to be of very high quality, providing a standard for similar studies in the future, and the authors carefully considered problems that arise in correcting for dependent samples, which I applaud.

Some of the claims need further discussion or refinement, in my opinion.

1) The comparison shown in Figure 2 between spiking time-scale and ECOG time-scale might be problematic, in the sense that the spiking time-scales were taken from the Murray et al. (2014) paper where they were quantified with a different technique. My suggestion would be to quantify time-scales in the same manner as Murray, or maybe there is a convincing argument why this is not a problem.

2) The correlations shown between transcriptomics and timescales need to be carefully considered. While the authors regress out T1w/T2w residuals, these might just be one structural factor that changes with cortical hierarchy and assumes that the underlying relationships are linear. Hence, it is possible that timescales and gene profiles are correlated with structure but that there is no causal relationship between these genes and timescales. In this sense, the correlation of genes with hierarchy might also yield similar genetic profiles. It would be important to show the correlation of hierarchy with genetic profiles, to see whether this looks different from the correlations that are obtained with timescale.

3) The authors use T1W/T2W as the measure for cortical hierarchy. This is a gradient-based perspective on cortical hierarchy. However, there are other perspectives on hierarchy that are not gradient-based, but are based on anatomical connectivity, e.g. as pursued by Kennedy and Van Essen (Vezoli et al., 2020, Biorxiv). This needs to be discussed.

4) The paper does not consider oscillations, which is fine, but the reader is left wondering how oscillations affect these time-scales. Discussion on this aspect would be useful.

5) Are the rho correlation values corrected for the expected value of the surrogate distribution? That is, are they significantly overestimated due to the dependent samples issue? In this case I would recommend reporting the corrected correlation values, rather than the raw correlation values.

6) The correlation performed in Figure 4D is a bit unclear to me. Are the different dots+lines participants, or is this a binned correlation? If it is a binned correlation, does that represent a problem for the correlation analysis?

7) It would be useful in Figure 1/2 to show some examples of ECOG time-scales related to the actual underlying signals and PSDs, rather than just illustrating the technique on simulated data, so that the validity of the technique can be judged.

8) In general it would be useful to report carefully the N's and the dataset that is used for each analysis, because it is easy to get lost in what is what as the authors analyze a huge number of datasets.

9) The technique of removing spatial autocorrelations that influence the p-value appears to be sophisticated and well done. In case this analysis poses problems with other reviewers, I would recommend using a cross-validation prediction approach where a subset of subjects is used for training and the other subjects are used for testing.

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Summary

Gao et al. analyze how brain-wide timescales of ECoG signals vary across the cortical hierarchy and relate these timescales to several other aspects of structure, behavior and function. They report the following main findings: 1) Timescales increase with the cortical hierarchy. 2) Time-scales, after regressing out the hierarchical T1w/T2w structure variable, correlate significantly with several genes related to synaptic receptors and ion channels. 3) Time-scales increase with working memory task vs. baseline, and predict working memory performance across subjects. 4) Time-scales decrease with aging, in a region-specific way. These findings are a significant advance in comparison to previous work by considering brain-wide hierarchy at a high spatial and temporal resolution and relating them to behaviour and genetics.

Reviewer #3

The work by Barros et al. looks at the role of the Ribosome Quality Control pathway (RQC) in regulating the expression of endogenous messages containing polybasic sequences. Using ribosome profiling and western blotting, the authors show that proteins containing various types of polybasic sequences are not targeted by the RQC. The authors argue that one of the few endogenous RQC substrate, RQC1, is not regulated via the canonical RQC pathway, but by a Ltn1p-dependent post transcriptional mechanism.

The question of whether there are endogenous RQC substrates has previously been explored. With the exception of the few identified substrates, such as RQC1 (Brandman et al, 2012) and SDD1 (Matsuo et al., 2020), these studies largely concluded the RQC has a minimal regulatory role for endogenous messages, and is most likely protecting cells from damage and environmental stressors. This idea is further supported by the observation that the RQC is non-essential under standard growth condition, but becomes synthetic lethal with translation inhibitors (Kostova et al, 2017, Choe et al, 2016). The work by Barros et al. comes to the same conclusions, and therefore it is unclear how this work contributes to the already established role of the RQC.

The authors also explore the regulation of RQC1 by the RQC and argue that this gene is regulated by Ltn1p in an RQC-independent way. However, mechanistic understanding of the proposed regulation is lacking, and the data are largely inconsistent with the previously published observations by Brandman et al, 2012.

Major points:

1) The authors use the dataset published by Pop et al., 2014 for their 27-29 nt no drug ribosome profiling analysis. However, these no-drug samples have been reported to exhibit surprising heterogeneity, and similarities with CHX-pretreated samples (see Hussmann et al., 2015 for detailed analysis). It is unclear how this heterogeneity can affect the analysis in the current manuscript, and whether the authors were aware of these caveats. Have the authors used independent datasets to confirm their observations? Have they excluded replicas that show CHX-like characteristics, such as A-site occupancy bias similar to CHX pretreated samples?

2) It is not clear what the purpose of the analysis presented in Fig 2 is, and how it is different from the modeling in the Park and Subramaniam 2019 paper? Are the authors using these parameters (TE, Kozak score, etc.) to show adaptations that minimize ribosome collisions?

3) Fig 3 - some of the selected examples (Dbp3, Yro2, Nop58) lack sufficient coverage in the region of interested highlighted in the right column for the short and/or long footprints. Since the data are insufficient to make conclusions about ribosome stalling and queuing, these examples should be excluded from the analysis.

4) Fig 4:

-Does ASC1 deletion cause frameshifting? Since the TAP-tag is C-terminal, it is possible that it is now out of frame, and therefore undetectable. Is it possible for the authors to introduce the tag on the N-terminus, and follow simultaneously the stalled nascent polypeptide (upon LTN1 deletion), and the full length protein?

-Is the putative stalling site of Dbp3 too close to the stat codon to cause collisions?

-Can the authors include a positive control, such as TAP-tagged Sdd1 to make sure their assay works and their strains and KOs behave as expected?

5) Fig 5:

-What is causing the inconsistency with the Brandman et al., 2012 data about RQC-dependent regulation of RQC1? In the original paper, Rqc1p has an N-terminal FLAG tag, so the authors primarily follow the stalled nascent polypeptide, whereas the current study focuses on the full length protein. Can the authors compare the same construct (FLAG-tagged Rqc1p) in their strains, so it is an "apples to apples" comparison?

-Fig 5c bottom panel - the read coverage is too sparse to make a conclusion. This analysis should be removed.

-5 d, e. The comparison between the GFP-12R-RFP stalling reporter and RQC2-TAP is not fair. The GFP construct reports on the fate of the stalled nascent polypeptide, whereas the RQC1-TAP looks at the full-length protein, and remains blind to the putative stalling product. Can the authors change the location of the tag, and repeat the experiment now looking at the stalled nascent polypeptide for RQC1? In addition, the signal in Fig. 5e look saturated. Is it possible that no effect is observed simply because the TAP signal is out of the dynamic range for the assay?

Minor Comments:

1) The introduction presents an overly simplistic view of ribosome stalling, arguing that stalling can be caused by polybasic stretches. We now know that stalling is much more complex, and there are many other factors, including the presence of non-optimal codon pairs, that cause ribosome collisions. Although the authors discuss these factors in their discussion, they should also be emphasized in the introductory paragraph.

Reviewer #2

In this manuscript, Barros et al. examine published ribosome profiling data in an effort to identify possible targets for ribosome-quality-control (RQC) process in yeast. They found that although many of the obvious mRNA features, such as polybasic sequences, appear to stall the ribosome, they in fact are not targets of RQC. The authors then went on to confirm these observations by western-blot analysis of a few candidate genes and observe that deletion of the RQC factors Ltn1 and Asc1 has no effect on the levels of the full-length protein products. The authors conclude that RQC has little to no endogenous targets in yeast. While I have no doubt about the authors' conclusions and most of their analyses, I have major issues with the originality of the manuscript.

1) The argument that RQC has little to no endogenous targets is not new. Many groups, including the authors' one, made the same arguments before. The authors recently published a paper in the Biochemical Journal "Influence of nascent polypeptide positive charges on translation dynamics". In particular, the analysis in that paper appears similar to the one carried out here. Furthermore, the Guydosh group made similar arguments in their recent paper (Meyden and Guydosh, Mol Cell).

2) The authors conclude their abstract by stating that "our results suggest that RQC should not be regarded as a general regulatory pathway for gene expression". To the best of my knowledge, RQC has not been regarded as such and instead the consensus has been that the process is a quality control one (as the name suggests).

3) The authors use LTN1 and ASC1 deletions to determine whether certain sequences are RQC targets or not. But for the ltn1D, instead of looking at the stabilized shorter products, the authors only looked at the full-length one. Ltn1 has no effect on readthrough on stalling sequences. A better deletion should have been that of HEL2.

Reviewer #1

In this manuscript the authors use existing high throughput data sets and perform some new experiments to explore in yeast potential physiological substrates of RQC. In a first step, they use bioinformatics to identify genes with features previously implicated in RQC (usually with reporter assays) including inhibitory codon pairs, poly-basic stretches, and poly-A tracts. With these genes in hand, they characterized various features of "translatability", using existing ribosome profiling data sets, and concluded that with the exception of the ICPs, that there were no strong signatures indicative of reduced ribosome density that might have evolved to deal with problematic ribosome queueing. The authors then looked at the RP data at higher resolution, looking for characteristic patterns of RPF distribution around the pausing site, and found that the striking patterns seen previously for Sdd1 (and for reporter analysis in D'Orazio et al. eLife) were not recapitulated for any of the top candidates in their list. In a final set of experiments, the authors took advantage of TAP-tagged variants of their proteins of interest and asked whether deletion of Asc1 or Ltn1 impacted protein levels - and found that there were no discernible effects (though validation with TAP-tagged Sdd1 is an important missing control). Importantly, expression of full length Rqc1 (previously argued to be a direct target of the RQC) was unaffected by RQC components including Asc1, Hel2 and Rqc2, but was strongly impacted by Ltn1. These data together argue for an RQC-independent role for Ltn1 in regulating Rqc1 expression.

Overall, the manuscript was thought provoking for consideration of what might be natural targets of RQC, and in the end, one would conclude that natural targets of RQC are not encoded in the genome, but may instead be predominantly either prematurely polyadenylated mRNA substrates that escape nuclear QC, or instead, ubiquitous damaged mRNAs in the cell. In general, the discussion of the analysis of RP data indicated naivete about the identity of different RPF sizes and their relevance to mechanism (this could be corrected easily in a revised version). In the end, this manuscript brings important questions to the table, and provides some reasonable evidence to suggest that natural poly-basic stretches, including the one found in Rqc1, are not targets for the RQC under normal conditions. Moreover, the data support a non-canonical role for Ltn1 in regulating expression of Rqc1 which needs to be more fully explored. Importantly, however, what is critical to support the negative results surrounding Rqc1 is a demonstration of a role for RQC for Sdd1, around which the narrative is constructed (this gene exhibits characteristics by RP of being a target and is reported previously to be impacted by the relevant genes Asc1 etc.).

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Summary:

There were substantial concerns about the novelty of the study, the choice of RP libraries, coverage depth, and analysis of the ribosome profiling data. Previous studies have argued that there are very few endogenous targets (so far Rqc1 and Sdd1) of the RQC pathway, and that this is rather a QC pathway for damaged mRNAs. While we appreciate that your studies were inconsistent with these earlier studies, it will be critical for you to replicate those experiments, using protein tags that allow you to follow the fate of both the full length and truncated species. Additionally, it will be important to validate using your own approaches and reagents that Sdd1 is indeed a substrate for RQC, given that your data suggest that Rqc1 itself is not. Finally, the novel Ltn1-dependent, RQC-independent pathway proposed to regulate Rqc1 expression requires further mechanistic work.

Reviewer #3

Three distinct amyloid-based cell-death pathways in fungi have been reported. The authors of the current manuscript extend their previous work of the HELLP/SBP/PNT1 pathway in Chaetomium globosum and describe a similar system in P. anserina. It is shown that the amyloid signaling domain of PTN1 can form a prion in cells deleted of HELLP, which is otherwise activated by the prion to cause cell death. Using this artificial system, the authors test whether the related RHIM motif of the human RIP1 and RIP3 protein can also form a prion in P. anserina and whether RHIM amyloids as well as other fungal amyloid-forming motifs can cross-seed PTN1.

The experiments are well executed and explained but I have a few suggestions:

1) Amyloid cross seeding is usually assayed in vitro using purified protein fragments. The artificial genetic system used here is certainly clever but the expression level of different proteins needs to be measured for better comparison of cross-seeding efficiencies.

2) Page 16, line 333-334 and Fig 8: How were recipient strains sampled? How random was it? How many samples?

3) Jargons/abbreviations. Page 19, line 405; Page 20, line 429: What are PAMPs, MAMPs, and PCD?

Reviewer #2

This work reports the discovery of an amyloid-based cell death signaling pathway in the filamentous fungus, Podospora anserina. This makes the third such pathway in this fungus. As for the others, the amyloid in this case has prion-like activity, is selectively nucleated by a cognate innate immunity sensor protein, and results in activation of the membrane-disrupting activity of the protein. They show that all three pathways operate orthogonally - that is without cross-seeding. In contrast, cross-seeding did occur between this pathway and the putatively homologous human necroptosis pathway when it is reconstituted in P. anserina, which further supports an evolutionary relationship between them.

Substantive concerns:

1) The novelty of this finding is somewhat dampened by this group's prior demonstration of several of the major points of interest in previous papers. They had previously discovered and characterized the homologous pathway in a different fungus, and suggested an evolutionary link between fungal amyloid signalosomes and mammalian necroptosis using strong bioinformatic and structural evidence. In addition, they had shown that the two previously known amyloid signaling pathways in P. anserina operated orthogonally. Hence the major point of novelty, as reflected in the title, is the demonstration that this particular amyloid pathway can cross-seed the human necroptosis amyloids.

2) Implications of "cross-seeding". The interspecific cross-seeding observed was modest; much lower than that for intraspecific templating between proteins of the same pathway. Specifically, it failed to induce a barrage, the puncta formed at different times, and colocalization was incomplete. More importantly, cross-seeding does not imply functional or evolutionary conservation. Consider the wide range of amyloid proteins that have been reported to cross-seed each other despite in some cases very different sequences, structures, and functions - for example the type-II diabetes peptide IAPP with the Alzheimer's peptide Aβ; the yeast prion protein Rnq1 with human Huntingtin; and the yeast prion Sup35 with human transthyretin. Although a direct comparison with the present data are not possible, these cross-seeding interactions appear comparably robust. The present demonstration of limited cross-seeding therefore seems not to add much additional support for an evolutionary relationship between necroptosis and fungal amyloid cell-death pathways.

3) Rigor of the fusion experiments. In all cases, despite having generated and validated the use of RFP- and GFP-labeled proteins, all fusion experiments to examine cell death microscopically (using Evans Blue staining) were between two GFP-expressing strains. This is frustrating because it makes it impossible to know from the images alone which of the two proteins is expressed in which cells, and in which cases of mycelia crossing paths is fusion occurring. I must therefore rely entirely on the labels provided, but they sometimes appear implausible. For example, the lower fusion event demarcated in Fig. 3C left panel would have been expected to allow GFP levels to equilibrate across the point of contact; instead there remains a sharp transition in GFP intensity between the two mycelia (third panel) indicating the cytoplasm is not being shared at the time of the image. In Fig. S8 top row, there is no apparent relationship between cell death and HELLP-GFP; moreover, cell death is seen occurring in mycelia containing either punctate or diffuse GFP-RIP3. While I appreciate that Evans Blue fluorescence may overlap with that of RFP (which should be stated) and preclude its visualization without multispectral imaging capabilities that may not be available to the authors, alternative viability stains and fluorescent proteins could in principle have been used to avoid this problem.

Minor Comments:

1) The significance of these proteins forming "prions", as opposed to (merely) amyloids, should be articulated. This is important because prion-formation per se is irrelevant to the cell-level functions of the proteins, as nucleation of the amyloid state causes cell death and hence precludes their persistent/heritable propagation. Amyloid by nature is self-perpetuating at the molecular level and hence would seem to explain the properties of the protein. The discussion about possible exaptation of these pathways for allorecognition could be expanded or clarified in this regard.

2) Colocalization between two proteins does not imply that one has templated the other to form amyloid, even when both are capable of forming amyloid independently (see https://doi.org/10.1073/pnas.0611158104 ).

3) Statements of partial cross-seeding are supported by quantitation (Fig. 8). In contrast, the authors appear to use qualitative observations to support rather definitive statements about the "total absence of" (line 344) of cross-seeding between other pathways.

4) Fig. S9. "Note that induction of [Rhim] in transformants leads to growth alteration to varying extent ranging from sublethal phenotype to more or less stunted growth." Can the authors suggest an explanation for this heterogeneity? From my limited perspective, it suggests the existence of amyloid polymorphisms (i.e. a prion strain phenomenon), which is quite unexpected given the lack of polymorphism among known functional amyloids in contrast to rampant polymorphism among pathological amyloids. Hence the phenomenon could be interpreted as suggesting that amyloid is not an evolved/functional state for the PP motif. In any case the phenomenon is interesting and merits further discussion.

Reviewer #1

Bardin and colleagues identify and characterize a third prion system in P. anserina based on the PNT1/HELLP NLR-based signalosome based on the amyloid signaling motif PP from Chaetomium globosum. The C-terminal domain of HELLP is shown to exist in either soluble or aggregated states based on fluorescence microscopy of tagged protein in vivo, termed the [pi] state, and to form amyloid in vitro. These distinct states can be propagated independently and induce conversion of full-length HELLP upon cytoplasmic mixing, which leads to cell death. The PNT1 N-terminal domain also forms foci in vivo and can seed conversion of HELLP, also leading to cell death. The C-terminal domain of C. globosum HELLP and the RHIM regions of mammalian RIP1 and RIP3, which both contain PP motifs, can cross-seed HELLP conversion to the aggregated state but the other known P. anserina prions [Het-s] and [phi] are unable to do so.

Support for the model proposed is generally qualitative in nature, with multiple instances of data described but not presented, including the timing of conversion to the aggregated state, revision of the aggregated state in meiotic progeny, the frequencies of conversion and co-localization, and the correlations between growth and prion phenotype. For the data presented, replicates, frequency of observations, and variability are not reported. In addition, a mechanism is proposed to explain the toxicity associated with HELLP conversion to the aggregated state - membrane localization - but this model is not supported by robust data such as a marker for the membrane in the fluorescence images or a biochemical fractionation. Moreover, the absence of functional data, such as mutations that disrupt amyloid formation, leave the model with correlative observations to support it. Finally, observations on the C. globosum system decrease the novelty of the observations.

Preprint Review

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Summary

Bardin and colleagues identify and characterize a third prion system in P. anserina based on a cognate innate immunity signalosome comprised of PNT1/HELLP. The authors demonstrate that the three prion pathways operate orthogonally without cross-seeding; however, the newly identified PNT1/HELLP prion can be cross-seeded by the putatively homologous human necroptosis pathway when it is reconstituted in P. anserina, which further supports an evolutionary relationship between them. The review has identified substantive concerns, which limit the novelty of the work and would require significant new studies to address the mechanistic gaps. These concerns include prior work revealing several major tenets including prion activity for PNT1/HELLP in C. globosum and evolutionary conservation to the mammalian necroptosis pathway and the absence for robust experimental support for cross-seeding, or the absence thereof, membrane disruption as the cause of incompatibility, and for the relationship among toxicity, growth, protein state, and protein interaction. Concerns were also raised about the data presented, or absent, in terms of replicates, frequency of observations, and variability.

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Reply to the reviewers

Point-by-point response to reviewers

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

The authors constructed a virtually complete fitness landscape of the P1 extension region (4-base-paired helix) in the group I intron from Tetrahymena thermophila, using a kanamycin resistance reporter to evaluate the fold-change in fitness, which is related to self-splicing activity. This was a clever choice of system because it was known from earlier work that the P1 extension adopts two different conformations during self-splicing. The fitness of each variant was determined from the number of reads acquired from the sequencing data sets and analyzed through an extensive computational pipeline. The strength of the paper is that this machine learning approach can be used to calculate how individual variants contribute to the fitness landscape and assess the directions of epistasis across a large number of identified genotypes.

We thank the reviewer for highlighting one of the key strengths of our manuscript, the fact that our analytical approach, using SHAP values, enables contributions of individual variants to be assessed in a genotype-specific manner. This approach provides for a sound, robust, and principled way of describing and understanding the fitness impact of one mutation in the context of (potentially many) others.

The authors argue that machine learning more successfully models subtle effects that arise from interactions between RNA residues, and that the power to analyze deep mutational sequencing experiments can better rationalize fitness constraints arising from multiple conformational states.

We do indeed argue that machine learning is likely to play an increasing role in making sense of deep mutational scanning data. These scans provide high-resolution information on how fitness maps onto genotype, but the molecular underpinnings of this relationship often remain obscure. It is these “hidden” underpinnings, including the effects of specific mutations on RNA/protein folding, structures, and dynamics, that machine learning approaches can help elucidate.

The results are mostly consistent with previous studies even though the authors collected the data in a more advanced and complicated way. They are also able to rationalize complex phenotypes - for example, the observed fitness defects are more prevalent under an unfavorable growth condition (30ºC), because the lower temperature hinders conformational exchange. Although such cold sensitive effects are well known in RNA, it is gratifying that this can be captured in the fitness landscape.

Finding temperature-related fitness effects that are consistent with impaired conformational exchange was also gratifying for us and we thank the reviewer for highlighting this finding.

The results would be more convincing if the authors directly measure the self-splicing activity of a few key variants, such as the C2C21 mutant, to determine whether these mutations alter the self-splicing mechanism of the Tte-119(C20A) master sequence in the way that they infer from their model. In interpreting their results, they may want to consider misfolding of the intron core (coupled to base pairing of P1) and reverse self-splicing. Reversibility in the hairpin ribozyme, for example, turned out to be the key for understanding the effects of certain mutations.

We appreciate that measurements of splicing activity for individual genotypes would complement and further strengthen our study. We will therefore aim to construct strains for a few key genotypes and assay self-splicing activity using RT-qPCR – an approach we previously used successfully to monitor splicing kinetics of self-splicing introns in yeast mitochondria (see Rudan et al. 2018 eLife 7:e35330). Specifically, we will quantify the fraction of spliced and unspliced transcripts using primers that span the exon-exon and the 3’ exon-intron junction, respectively (the 5’ intron-exon junction is genotypically diverse and would require genotype-specific primers). This will be done under non-selective (-kan) conditions, where the relative fraction of spliced and unspliced transcripts is a function of intrinsic splicing ability and not confounded by selection. We aim to include the master sequence, C2C21, G3C20 and its mirror genotype C3G20, U3 (which restores perfect complementarity in the master sequence), and G5 (inferred from the high-throughput experiment to make a strong negative contribution to fitness).

In interpreting our results, we will consider different mechanisms of splicing failure, such as kinetic problems (slow dissociation of P1ex), misfolding of the intron core, reverse self-splicing, and the use of cryptic splice sites, which has previously been documented (see e.g. Woodson & Cech 1991 Biochemistry 30:2042-2050). We note, however that a precise mechanistic dissection of the splicing defects of individual variants is not the purpose of this manuscript and we therefore do not aim to establish genotype-specific defects in great molecular detail.

Related to the point above, interesting conclusions regarding the relationships between base identity and epistasis that arise from metastability should be strengthened with additional examples. For example, the authors can explain why a reverse base-pairing variant (C3G20) exhibits negative epistasis but is not similar to that of the G3C20 construct. This would ideally use the data from the screen but also be validated by checking the self-splicing activity of a few individuals at low and high temperature.

In measuring splicing activity and its link to fitness for a subset of key variants (see point #4), we will include at least one mirror example such as C3G20/G3C20. In addition, we will highlight additional examples of this mirror asymmetry based on the results from our high-throughput screen.

They should validate the screen by showing that kanamycin resistance does indeed correlate strictly with self-splicing activity, and not some other feature such as RNA turnover. (It would also not be a bad idea to check this in the cell, which can be done by primer extension or Northern blotting.)

This question (i.e. whether altered RNA stability rather than splicing efficiency explains differential KNT production and ultimately fitness) has previously been addressed by Guo & Cech (2002) when introducing the knt+intron reporter system. These authors found no difference in mRNA stability in constructs that displayed differential kanamycin resistance. To shore up this conclusion further, we will measure fitness (via colony counts, growth rate or more directly through competitive fitness assays) of the key variants for which we determine splicing activity (see point #4) and then correlate splicing and fitness.

The benefit of the machine learning model is that it can extract signals that may be hard to detect otherwise. The downside is that it doesn't produce a physical model, as far as I am aware. The parameters are themselves not meaningful - except to the degree that trends in the fitness estimates can be explained after the fact. This is something that should ideally be explained more directly in the manuscript.

The reviewer raises an interesting point, that indeed deserves further discussion/explanation. The reviewer is right that, at first sight, high-resolution fitness landscapes like ours do not directly produce a physical (structural) model of the molecule under investigation. They connect genotype and fitness, but the molecular intermediate – a biophysical structure – is not explicit. However, over the last few years, it has become apparent that deep mutational scanning experiments can – both in principle and in practice – yield information that can be leveraged to infer such a physical model. In short, covariation in fitness between residues in a protein or bases in an RNA can be used as inputs for constraint-based modelling of physical interactions. Notably, Schmiedel & Lehner (2019, Nature Genetics 51: 1177-1186) recently demonstrated that deep mutational scanning data can be used in this manner to reconstruct secondary and tertiary protein structure with high accuracy. In principle, the same approach can be used to reconstruct RNA structures. This will require more extensive, molecule-wide fitness data, but our study points towards just this future, even for data collected from structural ensembles.

When we stated in the original manuscript that deconvolution of the fitness landscape might help to reverse engineer structures, this ability to interpolate between genotype and fitness to reveal hidden biophysical/structural relationships is what we refer to. We will revise the manuscript to make this connection more explicit.

The authors claim that by evaluating a large number of sequences at two conditions, they can capture variants with intermediate phenotypes (Fig. 1). This is not necessarily true. If the original screen allows only the most active variants to survive on kan+ medium, then the signature of intermediate phenotypes may not be encoded in the original data, and thus not retrievable even with sophisticated algorithms, which may also be prone to overfitting. At what limit of stringency will the screen fail to yield information about intermediate fitness? How deeply must one sequence to recover this information, especially if noisy or degraded? Some discussion of these effects would be helpful.

The capacity of any high-throughput sequencing-based DMS experiment to resolve intermediate phenotypes does indeed depend on a number of things. The reviewer highlights two of these: First, in screens where the phenotype is not binary (dead/alive) but fitness can be measured on a continuous scale, can we – and do we – capture phenotypes with intermediate fitness? What if only the fittest/most active variants survive? This is, ultimately, an empirical question, and one we can answer quite definitively: we do observe a large range of intermediate phenotypes, which – in our study – correspond to intermediate fold-change values. For each genotype, we can provide confidence limits and assess statistical significance. Table S1 provides this information. Our capacity to resolve these intermediate phenotypes is mainly based on three things. One is adequate sequencing depth, as highlighted by the reviewer. The second is the number of biological replicates (N=6) we analyse, which allows us to differentiate biological variability from noise for a large number of genotypes. This is an important aspect of DMS experiments that has often been overlooked (i.e. there are many other studies where only a single replicate is analysed and biological heterogeneity is not taken into account). With six replicates in hand, we can directly estimate variability (as done e.g. in our DESeq2 analysis) and quantify uncertainty so as to guard against overfitting. In our view, this is arguably more important than sequencing depth in deriving appropriate fitness estimates. Finally, we can resolve intermediate phenotypes because we keep the time lag between initial exposure to kanamycin and assaying genotype frequencies relatively short (overnight growth, see Methods). Our experiment is effectively a multi-genotype competition experiment, and we provide a snapshot across the genotype pool at a given time. If we had measured after several days of culture, genotypes with greater relative fitness would have spread further through the population, at the cost of less fit genotypes, many of which would likely have been eliminated. We kept measurement lag relatively short on purpose so that we could see a clear differential response to kanamycin while still being able to catch more than just a handful of the very fittest genotypes.

In light of the above, it will be apparent that there are no simple answers to the reviewer’s questions about required sequencing depth, levels of stringency, etc. The ability to assign differential fitness across a large population of genotypes hinges on multiple interrelated considerations (sequencing depth, complexity of the final & starting pool, number of replicates). In revising the manuscript, we will highlight some of the key considerations just discussed, bearing in mind that the manuscript cannot possibly discuss all possible pitfalls and requirements of deep mutational scanning experiments in great detail.

Lastly, the evolvability of RNA is fascinating and there is much to learn. However, the authors don't discuss the implications of their findings for molecular evolution although they throw the term around. It would be exciting if there is a trend in the fitness landscape that could help explain the trajectory of RNA evolution in nature.

We agree with the reviewer that it would be exciting to link deep mutational scanning results more closely with observable patterns of RNA evolution. This is true both in relation to evolution of P1ex/group I introns specifically and evolution of dynamic RNA structures more generally. Regarding the latter, we note that selection against excess stability has previously been inferred for 5’ UTRs (see e.g. Gu et al. 2010 PLoS Comp Biol 6: e1000664), although our case is slightly different in that a helix still needs to form but be sufficiently unstable to enable swift dissociation. We also note that riboswitches might make for an excellent subject to study asymmetric constraint and selection against excess stability as they involve formation of competing helices (including participation of some but not all nucleotides in more than one helix), their structure/function is well understood, and many examples are known, providing opportunities for evolutionary analysis. We consider this outside the scope of the current study. We will, however, seek to analyse patterns of evolution in P1ex to establish whether they correspond in a meaningful way to the fitness trends we observe in the laboratory. To do so, we will analyse the distribution and evolutionary history of variants across orthologous introns in different Tetrahymena species/strains, with a focus on P1ex, P10 and the surrounding sequence. Fortunately for us, the 23S ribosomal RNA gene in which the intron is embedded has been used as a phylogenetic marker so that intron/exon sequence information is available for a reasonable number of species/strains (see Doerder 2018 J Eukaryot Microbiol 66:182-208). We will generate an alignment of these sequences and ask, for example, whether N2-N5 are subject to different constraints than N18-N21 mirroring our experimental findings. We have previously successfully quantified patterns of variation surrounding self-splicing introns in yeast mitochondria (Repar & Warnecke 2017 Genetics 205:1641-1648). Note here that extending this analysis beyond Tetrahymena is problematic. Specifically, the intron is absent from close relatives of Tetrahymena (Doerder 2018 J Eukaryot Microbiol 66:182-208) and P1-proximal structures of distant relatives are quite variable. In addition, we are looking at intronic regions that are not only adjacent to but also directly interact with exonic sequence. The exonic context in which the intron is embedded therefore matters but will be quite different for more distant group I introns. We therefore think that aligning and comparing distant orthologs has limited merit.

The authors use the abbreviation DMS for deep mutational scanning; the RNA structure field uses the reagent dimethylsulfate that is also abbreviated DMS. They may want to choose a different acronym or just avoid an acronym altogether.

We appreciate this point about false-friend acronyms. We will either find a different acronym or avoid it altogether.

Reviewer #1 (Significance (Required)):

As the importance of RNA structure for gene expression becomes more widely appreciated, interest in understanding the evolution of RNA structures is also increasing. Compared with the molecular evolution of proteins, evolution and fitness in RNA is far less understood, although the authors appropriately point to a number of recent studies on this topic. The main advance here is to use machine learning methods to analyze the results of a large genotypic screen, with the goal of more accurately capturing the fitness effects of sequences at varied distances from the parental sequence. The specific conclusions reached here such as the importance of metastability or the prominence of cold sensitive effects are not revolutionary, but the authors illustrate how such phenomena can be investigated more systematically and in more depth.

We thank the reviewer for highlighting that our analytical approach showcases how deep mutational scanning data can be analysed in an unbiased and systematic manner to better understand the relationship between genotype, molecular phenotype (e.g. structure), and fitness. The reviewer also rightly points to specific results we obtain regarding temperature-related effects and metastability of P1ex/P10. However, we believe that the most important contribution of this work is a more general one, namely our proof-of-principle demonstration that deep mutational scanning data can capture multiple conformational states simultaneously, and that these states can be deconvoluted from a single fitness landscape to attribute the fitness impact of individual mutations to specific RNA conformations. To our knowledge this had not been explicitly demonstrated before and our work provides an important cornerstone for future studies looking to interpret mutational effects in either RNAs or proteins in the light of dynamic structures.

In light of comments by reviewer #2 below, it is worth reiterating the proof-of-principle nature of this study. Many of the specific results we obtain (e.g. importance of avoiding excess stability in P1ex) are not revolutionary. Indeed, we would be worried if they were. We chose to investigate P1ex because substantial prior work exists that has furnished us with solid positive controls. This independent prior validation allows us to both have great confidence in the data we generate and demonstrate cogently that the two conformational states at the beginning and end of the splicing reaction are captured in the data.

Finally, we believe our work, in covering a virtually complete genotype space, using multiple replicates to quantify uncertainty in fitness estimates, and using SHAP scores to interpret variant effects in genotype-specific context, sets a new high bar for this type of study and will provide valuable reference data and analytical recipes for future analyses. **

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

The manuscript by Soo et al probes the effect of mutations on the fitness of the Tetrahymena Group I self-splicing intron. They used high-throughput sequencing to simultaneously identify the effect of every possible sequence in a 4-bp helix. The approach is sound and the conclusions are generally supported. However, the analysis seems overly complicated given the dataset. Both the analysis and the accompanying writing make it difficult to understand what seems to be a fairly clear conclusion - that the relative stabilities of two alternative RNA helices are important for splicing.

We thank the reviewer for testifying to the validity of our approach and the soundness of our conclusions. Regarding the complexity of the analysis, the reviewer is right in that – for the conclusion that the relative stabilities of two alternative helices are important for fitness – a simpler analysis would have sufficed. However, as elaborated in response to point #11 above, our objective here is not merely to draw specific conclusions about the relative stabilities of P1ex and P10, but more general: a) to demonstrate that a single fitness landscape can be deconvoluted to implicate multiple conformations in fitness defects and b) to provide a basic but powerful recipe for doing so in an unbiased, systematic manner using machine learning.

We will strive to make the writing clearer so that readers can follow this reasoning and appreciate our analytical choices.

• **Major Comments** *

The authors state that this method can identify the impact of transient conformational states. However, the two conformational states in this study are not transient - in fact they are associated with two distinct chemical steps of splicing and are quite stable. It may be that the effect of important transient states would be observed, but this study does not demonstrate that.

We used the word “transient” to describe two alternative RNA structures formed during the life cycle of the intron. Both states (characterized by P1ex and P10 formation) are transient in as much as they disappear as splicing proceeds. In retrospect, we agree with the reviewer that this usage is too loose (given how the term is generally used in the literature) and might evoke the wrong connotations. We will therefore revise the manuscript to eliminate references to P1ex and P10 as transient states, but rather describe them as alternative conformations. Of course, the general point remains true: that deep mutational scanning data should in principle capture all fitness-relevant structural states even if these are transient (in the strict sense of the word).

"Fitness" ends up being on an arbitrary scale, which impairs some analysis. A similar high-throughput sequencing pipeline could have been used to directly monitor splicing of every mutant, though at this point that is outside the scope of this study. Even with the arbitrary units, it would be clearer if more time were spent comparing fitness to base-pair stability on an individual basis, rather than the broad analyses. (See minor comments for details.)

The reviewer is right in saying that a high-throughput pipeline could have been designed to monitor splicing of each genotype directly (rather than assaying fitness of the cell population that represents a particular genotype).We chose not to do so. One reason for this is that monitoring splicing directly would have necessitated design of a more complicated assay. This is because, to monitor splicing efficiency, one would have to monitor both pre-mRNA and mRNA for different genotypes. The former is straightforward (using primers that span the exon-intron junction) but the latter is not: successful splicing removes the genotype-specific information from the mRNA (that information being solely encoded in the intron). This a solvable problem in principle. One might, for example, introduce barcodes of sufficient complexity in the mRNA that can be linked back to the intron genotype, but doing so would have introduced a further source of error and complicated analysis. We therefore opted for monitoring genotypic fitness by sequencing the plasmids from which the RNAs originate. This does mean that our measurements of fitness are not coupled to a specific molecular phenotype (such as splicing efficiency) – we presume (but are not entirely sure) this is what the reviewer refers to when talking about fitness being on an “arbitrary scale”. However, fitness derived in this manner has the advantage of providing information that does not start from a mechanistic preconception. We ask how variant affects survival and reproduction of the cell without presuming specific mechanism and the results can therefore capture any mechanism, including those that we did not consider initially. The challenge then becomes to tease out possibly multiple mechanisms from unbiased data.

We will tackle the reviewer’s final comment, regarding analysis of base-pair stability, below in response to one of the minor comments (point #20).

\*Minor Comments** *

The sentence in the abstract beginning "Using an in vivo report system..." is very difficult to comprehend. This is due both to the length of the sentence and the word usage. The final sentence of the abstract is similarly difficult. In general, the writing overemphasizes complexity at the cost of clarity.

We will revise the entire manuscript to make the writing both clearer and more concise.

Analysis of results in terms of "epistasis" obscures what could be a straightforward observation. This is the same as saying that mutants are not independent, or that their energetic costs are not additive. This follows obviously from the observation that the nucleotides being mutated are base-paired.

Making explicit reference to “epistasis” is a considered choice. Framing results in terms of epistasis might be less familiar to readers grounded in RNA or protein biophysics/biochemistry, but is very much at the heart of thinking about the genotype-phenotype relationship from an evolutionary perspective, where global descriptions of epistasis are commonplace and usually provide the starting point for thinking about genotype-phenotype relationships, evolution and evolvability. So what seems unnecessarily obscure when seen through the lens of one field, is natural when considered in the context of another. Importantly, it is also the central approach adopted by many if not most prior deep mutational scanning studies (see e.g. Hayden et al. 2011; Pressman et al. 2019; Zhang et al. 2009; Li et al. 2016; Puchta et al. 2016; Domingo et al. 2018; Li and Zhang 2018; Weinreich et al. 2013; Lalić and Elena 2015; Bendixsen et al. 2017 as cited on page 3 of the manuscript) so we think this framing is helpful to compare our results to prior work.

We expect that the readership will include many researchers interest in mapping genotype-phenotype-fitness relationships who will expect to see global analyses and descriptors of the type we present. We will, however, revise the manuscript to ensure that our description of the findings remains accessible to readers from other fields.

More specifically, we also note that the fact that mutations are not independent (i.e. epistasis exists) might be trivial from the fact that P1ex is a base-paired helix. The magnitude and direction (“sign”) of epistasis, however, are not. In fact, as we describe, contrary to prior DMS on RNA helices, we find a lot of positive epistasis, reflecting, as we argue, selection against excess stability of P1ex to allow subsequent formation of P10.

The novel information is the sensitivity of fitness to base pairing. This is best shown in an analysis like Figure 3A (see below), not broad measures of epistasis.

Please see responses to points #11, #12, and #16 above for an elaboration of what we consider to be the main merits of this study and why providing broad measures of epistasis is a sensible choice.

Figure 1C isn't necessary for the reader to understand the process.

We are happy to follow editorial guidance as to whether this panel is superfluous and should be removed or is worth including.

It is unclear what figure 2C is showing. It appears that the replicates are similar to each other, that 30 deg C and 37 deg C are also similar, but that +/- Kan are different. This probably doesn't need a figure in the main text.

This figure does indeed capture what the reviewer describes: genotype pools in +/-kan are least similar to each other, while 30/37ºC are similar but distinct in the +kan condition and effectively indistinguishable in the -kan condition, in line with expectations. We agree with the reviewer that this information per se is something that would typically be found in a supplementary figure. However, we would advocate for retention of this panel in the main manuscript in this instance because of the way in which it was derived: using the Bray-Curtis dissimilarity index. To our knowledge, this is the first time that Bray-Curtis dissimilarity has been used to quantify, in a principled way, the similarity between genotype pools. Borrowed from the ecology literature, the index captures both richness (number of different species/genotypes in the ecosystem/genotype pool) and relative abundance to provide an integrated measure of genotype diversity. We believe that this measure will be useful for future studies and rather than relegating the figure to the supplement, we would aim to briefly highlight its methodological novelty. *

*

Figure 3A could be the most informative part of the manuscript. However, predicted minimum free energy should be on the x-axis as the independent variable. The expectation then is that you would see a peak in fitness at some free energy, with fitness falling off both with increased and decreased stability. Furthermore, there should be more analysis along these lines. The authors should calculate helical stability for both P1ex and P10 for every mutant and compare with fitness. Mutations which affect both could also be separated out. Figure 4C comes the closest to this but views it only in terms of GC pairs; there is no reason not to quantify the energetic effects given that predictions of stability for helices is quite good. Deviations from a model invoking only helical stabilities would indicate another factor is involved (alternative base-pairing or tertiary structure, for example).

We agree with the reviewer that the axes in Figure 3A should be flipped and we will do so in the revised manuscript. We also agree that, when it comes to helical stability of P1ex, the simple expectation would be to see a peak at a certain stability with drop-offs either side, as intimated by Figure 4C. We further agree with the reviewer that Figure 4C is rather indirect and can be made more quantitative by considering helical stability across all genotypes directly. To this end, we will use one of the many tools available that allow prediction of helical stability from primary sequence (e.g. the enf2 function in RNAStructure, as used by Torgerson et al 2018 RNA, see point #24 below) and replace Figure 4C with a more quantitative fitness landscape based on these computations. To provide added confidence in the computations of helical stabilities from primary sequence in the context of our structure, we will also calculate helical stabilities from molecular dynamics simulations for the subset of genotypes we considered previously (Figure 4E/F) and see how inferred stabilities compare.

There appears to be a missing verb in the legend for figure 3A, second sentence.

We will fix this error.

Figure S5 appears to be redundant with Figure 1.

At first glance, Figure S5 does indeed appear redundant with Figure 1 but it is not. Figure S5 shows the relevant sequence of the group I intron and bordering exons in its native context, i.e. when embedded in the 23S ribosomal RNA gene of Tetrahymena thermophila, whereas Figure 1 shows the genotype of the mutant intron embedded in knt. The sequences are different. We will revise the legend to Figure S5 to make this clearer.

Figure S6 is a better analysis than what appears in the main text, and could be expanded to all base pairs.

We will expand Figure S6 to include all base pairs as suggested. We disagree that this is a better analysis compared to what appears in the main text. Rather, it provides a complementary, hypothesis-driven view whereas the analysis in the main text is more systematic and unbiased in approach. *

*

Reviewer #2 (Significance (Required)):

This manuscript largely focuses on the technical approach. The shift in analytic strategy described above would increase the conceptual impact. The conclusions are consistent with and fit in with recent uses of high-throughput sequencing to study RNA systems. For example Pitt & Ferré-D'Amaré, Science (2010) and Kobari et al, NAR (2015) describe fitness landscapes of the ligase and HDV ribozymes, respectively. Torgerson et al RNA (2018) make similar measurements on the glycine riboswitch, including a treatment of relative helix stability for two mutually exclusive conformations. The overall results are of interest to researchers in the field of noncoding RNA.

We thank the reviewer for highlighting the paper by Torgerson et al, of which – embarrassingly – we were not aware. We will make reference to this paper in a revised manuscript and highlight that riboswitches might be a good model system to further explore asymmetric constraint and selection against excess stability in an evolutionary context (also see our response to point #9 above).

As highlighted earlier, we think the main conceptual impact of our work lies not in the description of helical stabilities. Rather, it lies in a) providing a rigorous proof-of-principle that deep mutational scanning can capture multiple conformational states simultaneously, and b) that, using an unbiased machine learning approach, these states can be deconvoluted from a single fitness landscape to attribute the fitness impact of individual mutations to specific RNA conformations. A shift in analytical strategy to “cut to the chase” and narrowly focus on helical stability would be misguided in this context, as we seek to provide not only insights into the data at hand but also lay out a sound and general recipe for analysing similar datasets in the future.

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Referee #2

Evidence, reproducibility and clarity

Summary

The manuscript by Soo et al probes the effect of mutations on the fitness of the Tetrahymena Group I self-splicing intron. They used high-throughput sequencing to simultaneously identify the effect of every possible sequence in a 4-bp helix. The approach is sound and the conclusions are generally supported. However, the analysis seems overly complicated given the dataset. Both the analysis and the accompanying writing make it difficult to understand what seems to be a fairly clear conclusion - that the relative stabilities of two alternative RNA helices are important for splicing.

Major Comments

1.The authors state that this method can identify the impact of transient conformational states. However, the two conformational states in this study are not transient - in fact they are associated with two distinct chemical steps of splicing and are quite stable. It may be that the effect of important transient states would be observed, but this study does not demonstrate that.

2."Fitness" ends up being on an arbitrary scale, which impairs some analysis. A similar high-throughput sequencing pipeline could have been used to directly monitor splicing of every mutant, though at this point that is outside the scope of this study. Even with the arbitrary units, it would be clearer if more time were spent comparing fitness to base-pair stability on an individual basis, rather than the broad analyses. (See minor comments for details.)

Minor Comments

1.The sentence in the abstract beginning "Using an in vivo report system..." is very difficult to comprehend. This is due both to the length of the sentence and the word usage. The final sentence of the abstract is similarly difficult. In general, the writing overemphasizes complexity at the cost of clarity.

2.Analysis of results in terms of "epistasis" obscures what could be a straightforward observation. This is the same as saying that mutants are not independent, or that their energetic costs are not additive. This follows obviously from the observation that the nucleotides being mutated are base-paired. The novel information is the sensitivity of fitness to base pairing. This is best shown in an analysis like Figure 3A (see below), not broad measures of epistasis.

3.Figure 1C isn't necessary for the reader to understand the process.

4.It is unclear what figure 2C is showing. It appears that the replicates are similar to each other, that 30 deg C and 37 deg C are also similar, but that +/- Kan are different. This probably doesn't need a figure in the main text.

3.Figure 3A could be the most informative part of the manuscript. However, predicted minimum free energy should be on the x-axis as the independent variable. The expectation then is that you would see a peak in fitness at some free energy, with fitness falling off both with increased and decreased stability. Furthermore, there should be more analysis along these lines. The authors should calculate helical stability for both P1ex and P10 for every mutant and compare with fitness. Mutations which affect both could also be separated out. Figure 4C comes the closest to this but views it only in terms of GC pairs; there is no reason not to quantify the energetic effects given that predictions of stability for helices is quite good. Deviations from a model invoking only helical stabilities would indicate another factor is involved (alternative base-pairing or tertiary structure, for example).

4.There appears to be a missing verb in the legend for figure 3A, second sentence.

5.Figure S5 appears to be redundant with Figure 1.

6.Figure S6 is a better analysis than what appears in the main text, and could be expanded to all base pairs.

Significance

This manuscript largely focuses on the technical approach. The shift in analytic strategy described above would increase the conceptual impact. The conclusions are consistent with and fit in with recent uses of high-throughput sequencing to study RNA systems. For example Pitt & Ferré-D'Amaré, Science (2010) and Kobari et al, NAR (2015) describe fitness landscapes of the ligase and HDV ribozymes, respectively. Torgerson et al RNA (2018) make similar measurements on the glycine riboswitch, including a treatment of relative helix stability for two mutually exclusive conformations. The overall results are of interest to researchers in the field of noncoding RNA.

Our expertise is in RNA biochemistry and biophysics. We are not qualified to evaluate the details of several of the computational pipelines described.

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Referee #1

Evidence, reproducibility and clarity

The authors constructed a virtually complete fitness landscape of the P1 extension region (4-base-paired helix) in the group I intron from Tetrahymena thermophila, using a kanamycin resistance reporter to evaluate the fold-change in fitness, which is related to self-splicing activity. This was a clever choice of system because it was known from earlier work that the P1 extension adopts two different conformations during self-splicing. The fitness of each variant was determined from the number of reads acquired from the sequencing data sets and analyzed through an extensive computational pipeline.

The strength of the paper is that this machine learning approach can be used to calculate how individual variants contribute to the fitness landscape and assess the directions of epistasis across a large number of identified genotypes. The authors argue that machine learning more successfully models subtle effects that arise from interactions between RNA residues, and that the power to analyze deep mutational sequencing experiments can better rationalize fitness constraints arising from multiple conformational states. The results are mostly consistent with previous studies even though the authors collected the data in a more advanced and complicated way. They are also able to rationalize complex phenotypes - for example, the observed fitness defects are more prevalent under an unfavorable growth condition (30{degree sign}C), because the lower temperature hinders conformational exchange. Although such cold sensitive effects are well known in RNA, it is gratifying that this can be captured in the fitness landscape.

Despite these strengths, there are several weaknesses that should ideally be addressed before publication.

1.The results would be more convincing if the authors directly measure the self-splicing activity of a few key variants, such as the C2C21 mutant, to determine whether these mutations alter the self-splicing mechanism of the Tte-119(C20A) master sequence in the way that they infer from their model. In interpreting their results, they may want to consider misfolding of the intron core (coupled to base pairing of P1) and reverse self-splicing. Reversibility in the hairpin ribozyme, for example, turned out to be the key for understanding the effects of certain mutations.

2.Related to the point above, interesting conclusions regarding the relationships between base identity and epistasis that arise from metastability should be strengthened with additional examples. For example, the authors can explain why a reverse base-pairing variant (C3G20) exhibits negative epistasis but is not similar to that of the G3C20 construct. This would ideally use the data from the screen but also be validated by checking the self-splicing activity of a few individuals at low and high temperature.

3.They should validate the screen by showing that kanamycin resistance does indeed correlate strictly with self-splicing activity, and not some other feature such as RNA turnover. (It would also not be a bad idea to check this in the cell, which can be done by primer extension or Northern blotting.)

4.The benefit of the machine learning model is that it can extract signals that may be hard to detect otherwise. The downside is that it doesn't produce a physical model, as far as I am aware. The parameters are themselves not meaningful - except to the degree that trends in the fitness estimates can be explained after the fact. This is something that should ideally be explained more directly in the manuscript.

5.The authors claim that by evaluating a large number of sequences at two conditions, they can capture variants with intermediate phenotypes (Fig. 1). This is not necessarily true. If the original screen allows only the most active variants to survive on kan+ medium, then the signature of intermediate phenotypes may not be encoded in the original data, and thus not retrievable even with sophisticated algorithms, which may also be prone to overfitting. At what limit of stringency will the screen fail to yield information about intermediate fitness? How deeply must one sequence to recover this information, especially if noisy or degraded? Some discussion of these effects would be helpful.

6.Lastly, the evolvability of RNA is fascinating and there is much to learn. However, the authors don't discuss the implications of their findings for molecular evolution although they throw the term around. It would be exciting if there is a trend in the fitness landscape that could help explain the trajectory of RNA evolution in nature.

7.The authors use the abbreviation DMS for deep mutational scanning; the RNA structure field uses the reagent dimethylsulfate that is also abbreviated DMS. They may want to choose a different acronym or just avoid an acronym altogether.

Significance

As the importance of RNA structure for gene expression becomes more widely appreciated, interest in understanding the evolution of RNA structures is also increasing. Compared with the molecular evolution of proteins, evolution and fitness in RNA is far less understood, although the authors appropriately point to a number of recent studies on this topic. The main advance here is to use machine learning methods to analyze the results of a large genotypic screen, with the goal of more accurately capturing the fitness effects of sequences at varied distances from the parental sequence. The specific conclusions reached here such as the importance of metastability or the prominence of cold sensitive effects are not revolutionary, but the authors illustrate how such phenomena can be investigated more systematically and in more depth.

Reviewer #3

Introduction:

1) For those not familiar with personality/trait constructs, harm avoidance should be defined.

2) The authors unnecessarily make a distinction between emotion and cold cognition, or emotion and non-emotional perception. I don't think this distinction needs to be made and furthermore, the separation of emotion and cognition is a little antiquated in what we know about holistic processing of the brain.

3) There is no mention of the amygdala or bed nucleus of the stria-terminalis in discussions of anxiety and especially in anticipation. Nor is there any mention of anticipatory or arousal components of anxiety.

4) There are two competing points brought up in the introduction, regarding the pre-SMA: 1) that the pSMA is involved in time tracking and 2) that the pSMA is involved in threat related shock. This appears to be problematic due to the proposed hypotheses. Perhaps, the authors could adjust the hypotheses to illustrate why only time perception is a main effect hypothesis and time and anxiety are an interaction hypothesis.

5) Hypothesis 5 is unclear, I assume the brain (neural changes) are being correlated with time estimation (behavioral index?), but it is unclear.

Methods:

1) Nim-Stim images need to be described in more detail in the methods and not just in the figure caption.

2) The experimental methods specifics needs to be more clear regarding the differences in stimulus duration. This is an important distinction between the two studies and not enough details are given. It should be clearly worded and not left up to the reader to try and interpret the table.

3) Why did the number of shocks differ between participants? That seems like a confound for the neural interpretation. The authors need to explain.

4) There is no mention of fMRI screening for Study 1.

5) Why a power calculation for Study 2, but not 1?

6) The methods section is written such that the amount of explanation between the two studies needs to be resolved. They are quite different, i.e., how many total shocks in Study 1? There are inconsistencies throughout.

7) Why are different analysis methods used to examine behavioral effects? ANOVA vs. paired sample t test? Details like this need to be explained throughout the manuscript if the authors are trying to compare two data sets.

8) It isn't clear or mentioned that Study 1 was a pilot study for Study 2 until the neuroimaging analysis section. This needs to be explained and more detail should be included much earlier in the manuscript.

9) For information: Siemens Skyra and Prisma scanners have built in dummy scans at the beginning of sequences to allow for equilibration.

10) The neuroimaging methods require much more detail, i.e., SPM version used, etc., etc.

11) ROIs description needs more detail, i.e., a 10mm sphere. 10mm what? Radius, circumference? That's a huge ROI for subcortical regions.

Reviewer #2

The manuscript "Anxiety makes time pass quicker: neural correlates" outlines an interesting and potentially important set of experiments aimed at replicating a previously reported effect of distorted time perception while under threat of electric shock while adding fMRI measurement of brain activity during the task. The manuscript has multiple strengths, in my opinion, including the use of a cleverly designed paradigm coupled with sophisticated neuroimaging methods, pre-registered predictions and analysis plan, and a potentially informative mechanistic focus. The study is also well grounded in the literature and the manuscript well written. I have some concerns, however, with the current version of the manuscript. These concerns mostly center on the strength of evidence afforded by the current design and the interpretability of the design and results. I outline these concerns, point by point below.

1) The choice to pre-register the predictions and analysis plan is laudable. For clarity, I believe the authors should indicate, up front, what aspects of the study were pre-registered rather than simply saying that it is pre-registered.

2) There are potentially important differences between the study pre-registration and the reported hypotheses and analysis. Sticking rigidly to the pre-registration is certainly not necessary to benefit from a pre-registration but I believe all potentially substantive deviations from the pre-registration should be identified and explained in the manuscript for transparency. For example, the specific brain regions mentioned in Prediction 2 are not consistent between the manuscript and pre-registration.

3) In the pre-registration, I didn't see Prediction 4 (interaction of time-related and anxiety-related neural processing) but this may be attributable to inconsistent wording between the pre-registration and manuscript.

4) The pre-registration discusses planned hypotheses and analysis involving functional connectivity but I do not see this mentioned in the manuscript.

5) Some description of why faces (versus anything else) were used as stimuli is needed for readers to understand the task.

6) Related to point 6 above, it is reported that the durations of stimuli were randomized but I did not see a description of randomization of the face stimuli themselves. This is needed (if I didn't just miss it).

7) The authors indicated that the study was powered to detect the effect of threat on (I assume) behavior. I would guess that this is one of the largest effects that could be tested for in this study. In fact, the study appears underpowered to detect anything but very large effects. This could explain why many effects tested were not found (especially the interactions). I believe this should be explicitly acknowledged as a limitation for readers to be able to appropriately evaluate the strength of evidence for the claims made.

8) Given the short ITIs in the task, perhaps the effects attributed to anxiety caused by threat of shock are in actuality effects due to continued processing of the previous aversive shock. I know the authors said they regressed out the effect of shock from the brain measures but it is unclear how one would regress out the effects of processing of previous shocks. Perhaps this potential confound has been addressed in previous reports of this task but I think some brief attention to the issue here would help readers to evaluate the results.

9) Given the fact that shocks always occurred during the ITI and never during the cue, readers may be left wondering if the participants were indeed anxious versus, e.g., distracted, during the temporal decision task since they technically are not even yet at risk of receiving a shock at that moment of the task. Some clarification of this point would be helpful.

10) Related to and overlapping with some of the points above, I request that the authors add a statement to the paper confirming whether, for the experiment, they have reported all measures, conditions and data exclusions and how they determined their sample sizes. The authors should, of course, add any additional text to ensure the statement is accurate. This is the standard reviewer disclosure request endorsed by the Center for Open Science [see http://osf.io/hadz3 ]. I include it, where appropriate, in every review.

Reviewer #1

This manuscript reports a pair of studies investigating the neural correlates of the temporal underestimation that has been shown to accompany anxiety in previous studies. Hypotheses were pre-registered, including increased activation in the anterior cingulate during threat and that "threat-related bold signal changes will correlate with the threat related behavioural changes". The current work found threat-related activity in the anterior cingulate gyrus, and that greater mid-cingulate activity for longer estimates of stimulus duration, with a trend toward overlap between these contrasts, which was subthreshold after correcting for multiple comparisons. In addition, activity associated with state anxiety and temporal estimation overlapped in the insula and putamen. The authors interpret these findings as consistent with the overloading hypothesis that vigilance during state anxiety and duration perception rely on overlapping areas, resulting in inaccurate duration perception during anxiety. However, these results should be interpreted with caution given that, as the authors note, there was no interaction between threat and perceived duration, and no correlation "between the underestimation of time during threat and either insula or midcingulate activation in the interaction contrast". Given the relatively small sample size, these null findings may have been the result of low power. Nevertheless, the current study will likely serve as a useful starting point for future work on this topic.

Below are my comments on the manuscript:

1) In the pre-registration, hypothesis 2 refers to the ACC and frontopolar areas, while in the manuscript I am not seeing the frontopolar areas. I know this region is particularly susceptible to dropout, so it is possible you were unable to adequately test this hypothesis – if so, this should be stated in the manuscript. In addition, the manuscript lists right IFG in the hypotheses, but I am not seeing results reported for this region.

2) It would be good to explain why you chose to use 10 mm spheres centered on your ROIs, rather than using all voxels that met the p>.05 threshold in the clusters identified in Study 1.

Minor comments:

The abstract starts off talking about how anxiety can be adaptive, however, unless I missed something, they don't explicitly tie this thought into temporal underestimation. From the perspective of someone who is naive to literature on temporal underestimation, it seems that causing temporal underestimation would be maladaptive, if it causes one to underestimate how long you've been worrying about something. I would suggest either making the relationship between these ideas more explicit in the text, or either removing this first sentence or moving it to a less prominent spot.

If there was a methodological reason for switching to a train of shocks (ex. an expectation that it would elicit more anxiety) in Study 2, it may be helpful for future researchers to state it. If it was simply a matter of equipment available at the second site, then no changes are needed.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This manuscript reports a pair of studies investigating the neural correlates of the temporal underestimation that has been shown to accompany anxiety in previous studies. Hypotheses were pre-registered, including increased activation in the anterior cingulate during threat and that "threat-related bold signal changes will correlate with the threat related behavioural changes". The current work found threat-related activity in the anterior cingulate gyrus, and that greater mid-cingulate activity for longer estimates of stimulus duration, with a trend toward overlap between these contrasts, which was subthreshold after correcting for multiple comparisons. In addition, activity associated with state anxiety and temporal estimation overlapped in the insula and putamen. The authors interpret these findings as consistent with the overloading hypothesis that vigilance during state anxiety and duration perception rely on overlapping areas, resulting in inaccurate duration perception during anxiety.

The reviewers and I identified several strong points:

1) The current study may serve as a useful starting point for future work.

2) Interesting set of experiments aimed at replicating a previously reported effect of distorted time perception while under threat of electric shock while adding fMRI measurement of brain activity during the task.

3) Clever paradigm.

4) Pre-registered predictions and analytic plan.

5) Grounded in the literature.

Yet, on balance, there was consensus that the study provides only an incremental advance, largely owing to limitations of the approach.

Major/general concerns are:

1) Insufficient power. E.g.

-"The authors indicated that the study was powered to detect the effect of threat on (I assume) behavior. I would guess that this is one of the largest effects that could be tested for in this study. In fact, the study appears underpowered to detect anything but very large effects. This could explain why many effects tested were not found (especially the interactions). I believe this should be explicitly acknowledged as a limitation for readers to be able to appropriately evaluate the strength of evidence for the claims made."

-"The results should be interpreted with caution given that, as the authors note, there was no interaction between threat and perceived duration, and no correlation "between the underestimation of time during threat and either insula or midcingulate activation in the interaction contrast". Given the relatively small sample size, these null findings may have been the result of low power."

2) Writing style. The reviewers found the lack of attention to polishing the manuscript distracting, e.g. "The methods section appears to be written by two different authors with major inconsistencies in style and phrasing"

3) Missing details. Crucial methodological details are lacking or inconsistent, making it difficult to fully evaluate the approach

Reviewer #3

The authors provide a clear and effective response to the demand for robust real-time pose estimation software with closed-loop feedback capabilities. In addition, we appreciate the effort that the authors have put into making the software user-friendly and extensible. The paper is very well written and contains many tools for those in the field to effectively use.

A small weakness is the authors have demonstrated the LED flash latency but do not show an application such as optogenetic stimulation or behavioural manipulation using the system. Also, most of their benchmark numbers are based on videos and not camera streams, this does not fully address potential hardware issues. I believe the heavy dependence on video data and not actual ground truth live video feed is something that should be checked to present accurate numbers.

Their Kalman filter approach seems useful but the deviations in pose estimation prediction from the normal pose estimation are sometimes 30 px or more. People may make trade-offs between latency and accuracy when using this software. Another important factor for real-time tracking is the accuracy of the pose estimation, it determines whether the system is really useful in true application.

It would be nice to see a bit more validation of the software in a realistic live stream context. The quality of their code is quite high.

1) The authors emphasize that their software enables "low-latency real-time pose estimation (within 15 ms, at >100 FPS)". Upon inspection of table 2, it appears that this range of latency and speed combinations is primarily achieved using 176x137 px images on Windows/Linux GPU based hardware, with corresponding FPS dropping to well below 100 for larger images in the DLCLive benchmarking tool on all platforms except for Windows. As the range in framerate/latency combinations appears to vary quite a bit between setups and frame sizes, we would suggest including a more realistic range for the latency and framerate in the abstract or at least mention the heavily down-sampled video used.

2) In table 2, the mean and SD latency appear to be stable across modes, frame sizes, and GPU setups. However, there appears to be a notable spike in the latency range (14 {plus minus} 73) for the image acquisition to LED time on Windows computers that stands out from other latency figures. This latency range is concerning for the consistency of real-time feedback applications on a platform and at a frame size that is likely to be commonly used. Would the authors be able to explain a possible reason for this large SD?

3) The DLG values appear to have been benchmarked using an existing video as opposed to a live camera feed. It is conceivable that a live camera feed would experience different kinds of hardware-based bottlenecks that are not present when streaming in a video (e.g., USB2 vs. USB3 vs. ethernet vs. wireless). Although this point is partially addressed with the demonstration of real-time feedback based on posture later in the manuscript, a replication of the DLG benchmark with a live stream from a camera at 100 FPS would be helpful to demonstrate frame rates and latency given the hardware bottlenecks introduced by cameras.

4) In Figure 3, the measurement of the latency from frame to led is not very clear. The DLC will always give pose estimation even when the tongue is not appeared in the image so the LED will always be turning on very quickly after obtaining the pose from the image.

5) In "Real-time feedback based on posture", the Kalman filter approach to reduce latency through forward prediction is innovative and likely of use for rapid characterization of general behaviours. In Figure 8C, the deviation of pose predictions from non-forward predicted poses appears to follow the general trend of the trajectory but appears to deviate by as many as 50 pixels from the non-forward predicted poses. While this tolerance may be acceptable for general pose estimation, many closed-loop pose estimation implementations may focus on rapid and accurate feedback based on very small movements (e.g. small muscular movements). For example, movements differing in magnitude by a few pixels may distinguish spontaneous twitches from conditioned behaviours. Considering that the demonstrated setup achieves a mean image to LED latency of 82 ms without the Kalman filter, it appears that many users would have to make a large trade-off between accuracy and latency in order to use the system with a conventional webcam and reasonably priced setup. Although the methods discussed are state-of-the-art and impressive considering the hardware used, it may be helpful to include a discussion of how the Kalman filter approach may be improved in the future to improve pose estimation accuracy while maintaining low latency.

6) The software is compared favourably to existing real-time tracking software in terms of latency (refs 12-14). The efficacy of the existing realtime pose estimation software has been validated on animal movements using closed-loop conditioning paradigms. If feasible, a demonstration of the software reinforcing an animal based on real-time pose estimation (e.g. a similar paradigm to that used in the DLG benchmark video) would provide useful context as to whether the pose estimation strategies discussed are effective in closed-loop experiments. In particular, this would be important to evaluate given the novel Kalman filter approach - which influences the accuracy of pose estimation. We list this closed loop experiment as optional given the pandemic conditions we face. In contrast to the live animal reinforcement experiment, we do feel that real world streaming video to output trigger latencies are required (pt #3).

Reviewer #2

Kane et al. introduce a new set of software tools for implementing real-time, marker-less pose tracking. The manuscript describes these tools, presents a series of benchmarks and demonstrates their use in several experimental settings, which include deploying very low-latency closed-loop events triggered on pose detection. The software core is based on DeepLabCut (DLC), previously developed by the senior authors. The first key development presented is a new python package – DeepLabCut-Live! – which optimises pose inference to increase its speed, a key step for real-time application of DLC. The authors then present a new method for exporting trained DLC networks in a language-independent format and demonstrate how these can be used in three different environments to deploy experiments. Importantly, in addition to developing their own GUI, the authors have developed plugins for Bonsai and AutoPilot, two software packages already widely used by the systems neuroscience community to run experiments.

The tools presented here are truly excellent and very exciting. In my view DLC has already started a revolution in the quantification of animal behaviour experiments and DeepLabCut-Live! is exactly what the community has been hoping for – to deploy the power of DLC in real-time to perform closed-loop experiments. I have very little doubt that the tools described in this manuscript and their future versions will be a mainstay of systems neuroscience very quickly and for years to come. Key to this is that the software is entirely OpenAccess and easy to deploy with inexpensive hardware. I commend, and as a DLC user, I certainly thank the authors for their efforts. I have a couple of comments below on the manuscript itself, which the authors might want to consider. As for the software itself, all of the benchmarks look good and the case studies make a compelling case for its applicability in real-life – and the beauty of it is that because its Open Access, any issues and improvements needed will be quickly spotted by the community, and I expect duly addressed by the authors judging from their track-record on DLC.

Main comments:

1) One important parameter that is not really discussed throughout the manuscript is the accuracy of pose estimation. I realize that this might be more of a discussion on DLC itself, but still, when relying on DLC to run closed-loop experiments this becomes a critical parameter. While offline we can just go back, re-train a new network and try again, in a real-time experiment, classification errors might be very costly. The manuscript would benefit from discussing these errors and how they can be best minimised. It would also be helpful to show rates for positive and false negative classification errors for the networks and use-cases presented here, to highlight the main parameters that determine them and perhaps show how classification errors vary as a function of these parameters (e.g., do any of the procedures to decrease inference latency, such as decreasing image resolution or changing the type of network, affect classification accuracy?). Along the same lines, while the use of Kalman Filters to achieve sub-zero latencies is very exciting, it is unclear how robust this approach is. This applies not only to the parameters of the filter itself, but also on the types of behaviour that this approach can work with successfully. Presumably, this requires a high degree of stereotypy and reproducibility of the actions being tracked and I feel that some discussion on this would be valuable.

2) A related point is that some applications are likely to depend on the detection of many key-points and it is unclear how the number of key-points affects inference speed. For example, the 'light detection task' using AutoPilot uses a single key-point, how would the addition of more key-points affect performance in this particular configuration?

Reviewer #1

The authors present a new software suite enabling real-time markerless posture tracking - with the aim of making low-latency feedback in behavioral experiments possible. They demonstrate the software's capability on a variety of hardware and software platforms – including GPUs, CPUs, different operating systems, and the Bonsai data acquisition platform. Moreover, they demonstrate the real-time feedback capabilities of DeepLabCut-Live!.

While there have been other methods that have been introduced recently that have incorporated real-time feedback on top of DeepLabCut, this software shows improved latency, has cross-platform capabilities, and is relatively easy to use. The software was thoroughly benchmarked (with one small exception that I'll outline below), and although I wasn't able to directly test it myself, I was easily able to download the code, and the documentation was sufficient for me to understand how it works. I have every confidence that this is a piece of software that will be extensively used by the field.

My one comment is that it would have been good to have some analysis as to how the network accuracy (i.e., real space – not pixel space – error in tracking) scales with resolution, as the fundamental tracking trade-off isn't image size vs. speed, it's accuracy vs. speed. I wouldn't call this an essential revision, but I think that including these curves would greatly help potential users make important hardware and software decisions. Granted, this difference will alter depending on the network, but even getting a sense from the Dog and Mouse networks here would likely be sufficient to provide a general sense.