Reviewer #1 (Public Review):

The authors look at a few different nematode species to compare the dynamics of anaphase. They find that in some species the spindle oscillates transversely in anaphase, and in other species it does not. They ask what accounts for this different behavior. To address this question, they use ablation of the central spindle, and conclude from the result, correctly, that after the ablation the centrosomes are pulled to the opposite poles of the cell in all species. However, the magnitude, half-time and initial velocity of the recoil differ.

To understand what accounts for the quantitative difference, the authors

1) use a simple viscoelastic model of a constant force, F, pulling against a spring (with constant stiffness k), while the object moves through the viscous medium.

2) estimate the cytoplasmic viscosity from tracking yolk granules,

3) estimate parameters F and k from fitting the exponential recoil curves. They find that the greatest correlation between having transverse oscillation or not is with lower or higher viscosity, not with magnitude of the force or stiffness of the spring.

Two major problems with this study can be identified:

1) Meaning and significance: It is not clear if the transverse oscillation have a functional significance. In fact, they are more likely than not simply a byproduct of complex nonlinear mechanics of the mitotic spindle. It is important to understand what we can learn about the spindle mechanics from these oscillations, but there may be no evolutionary significance here. If the authors were asking - how, in many different species, the spindle scales with the cell size in the same way (as was done in Farhadifar et al 2020, which the authors do not to cite) despite large parameter variations - that would be a different story. But asking which parameter change is responsible for the behavior change is less meaningful.

2) The study is not convincing, mainly because the model used for the fit is overly simplistic. The force is not constant, the spring stiffness is not constant, the mechanics is not, etc. There are a few different, very complex models, of the anaphase spindle with transverse oscillations - comparing to simulations of these models would be more convincing. Also, I am not quite sure whether the volume fraction of yolk is a useful parameter. Does not measuring MSD give us the diffusion coefficient and viscosity directly? I think using the factor depending on the volume fraction artificially inflates the viscosity differences. Lastly, I do not understand the theoretical argument based on comparison with Nedelec's model: in that model, increasing viscosity only slowed the oscillations down, not abolished them.

In short, much more thorough investigation would be needed to understand which differences between the species account for the presence or absence of the oscillations, and one may question whether the answer would have a deep impact on our understanding of spindle mechanics.

Reviewer #2 (Public Review):

A summary of what the authors were trying to achieve:

The authors have developed an approach to prediction of T cell receptor:peptide-MHC (TCR:pMHC) interactions that relies on 3D model building (with published tools) followed by feature extraction and machine learning. The goal is to use structural and energetic features extracted from 3D models to discriminate binding from non-binding TCR:pMHC pairs. They are not the first to make such an attempt (e.g., Lanzarotti, Marcotili, Nielsen, Mol. Imm. 2018), but they provide a detailed critical evaluation of the approach that sets the stage for future attempts. The hope is that structure-based approaches may have better power to generalize from limited training data and/or to model unseen pMHCs.

An account of the major strengths and weaknesses of the methods and results:

The authors first report (section 4.1) that their structural and energetic features contain information on binding mode, highlighting complexes with reversed binding polarity, for example, and partly discriminating MHC class I from MHC class II structures. This is encouraging but not terribly surprising. Also, with regard to MHC I vs II discrimination, it is not clear how the class II peptides are registered with respect to one another. This needs to be done by alignment on MHC and mapping of structurally-corresponding peptide positions, since the extent of N- and C-terminal peptide overhangs varies between structures and is largely irrelevant to the docking mode. Interactions between the TCR and MHC are ignored in the feature extraction process; it's possible that including these interactions could improve performance. The authors state: "To be noted that not all structures could be successfully modelled by TCRpMHC models, and so we could not submit them to the feature extraction pipeline." It's unclear what effect this could have on the results: if the modeling failures are cases of structures for which no good CDR templates could be identified, then perhaps this could bias the results.

Section 4.2 reports a negative result: unsupervised learning applied to the extracted features is unable to discriminate binding from non-binding complexes. This suggests that there is not likely to be a simple energetic feature, such as overall binding energy, that reliably discriminates the true binders. In Section 4.3, the authors turn to supervised learning, in which training examples inform prediction by a classifier. One finding is that the pure-sequence approach using Atchley-factor encoding of the TCR:pMHC outperforms the structure-based approaches, though not by much. A combined model incorporating Atchley factors and structural features does slightly better. These results are a little hard to interpret because we don't know how challenging the 10-fold internal cross-validation is. It doesn't sound like there is any attempt to avoid testing on TCR:pMHCs that are nearly identical to TCR:pMHCs in the training sets, and the structural database is highly redundant, containing many slight variants of well-studied systems. It's also not clear how overlap between the template database used for 3D modeling and the testing set was handled; my guess is that since the model building is an external tool this was not controlled. Together, these factors may explain why the results on independent test sets are, for the most part, significantly worse than the cross-validation results. Another take-home message from the independent validation is that the sequence-only method seems to outperform the sequence+structure or structure-only methods. Although these are described as "out-of-sample validation", it's not clear how different these independent TCR:pMHC examples are from the structure dataset on which the model was trained.

Sections 4.4 and 4.5 report that prediction accuracy varies significantly across epitopes, and this is in part determined by sequence similarity to the structural database (which provides templates for modeling and also constitutes the training set for the model). In section 4.6, the authors determine that the model does not appear to be able to predict binding affinity (as opposed to the binary decision, binding versus non-binding). Finally, in section 4.7 the authors benchmark the predictor against two publicly available, sequence-based predictors. When predicting for epitopes present in their training sets, all methods do reasonably well, with the edge going to the sequence-based ERGO method. When predicting for epitopes not present in their training sets, none of the methods perform very well. The authors state that "these results suggest that the structure-based models developed in this study perform as well as the state-of-the-art sequence-based models in predicting binding to novel pMHC, despite learning from a much smaller training set." This may be true, but the predictions themselves are not much better than random guessing (AUROCs around 0.5-0.6).

An appraisal of whether the authors achieved their aims, and whether the results support their conclusions:

I'm doubtful that the proposed methods will form the basis of a practical prediction algorithm. In the absence of ability to generalize to unseen epitopes, simpler sequence-based approaches that leverage the ever-growing dataset of TCR:pMHC interactions seem preferable. I still think the study has value as a template and roadmap for future efforts, and a baseline for comparison. For me, a key unanswered question is whether the model-derived structural features are just a different, slightly noisier way of memorizing sequence, or actually contain orthogonal information that can enhance predictions. It might be possible to gain insight into this question by looking more carefully at the impact of model-building accuracy on performance (the authors use sequence similarity as a proxy, but this is confounded by overlap between the training set and the template set used for modeling). If model-building really adds something, it seems plausible that it does so by accurately capturing physical features of the true binding mode.

A discussion of the likely impact of the work on the field, and the utility of the methods and data to the community:

As state above, I think the present work will have a positive impact on the field of TCR:pMHC prediction by critically evaluating the structure-based approach (and also by testing two previously published methods on independent data). I am less convinced of the utility of the specific methods than of the overall conceptual framework, evaluation procedures, and training/testing sets.

Any additional context you think would help readers interpret or understand the significance of the work:

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): **Summary:** Techniques to probe the local environment of membrane proteins are sparse, although the influence of lipids on the membrane protein's function are known since many years. Therefore, the paper by Umebayashi et al. is important. The environment-sensitive dye Nile red (NR) coupled to a membrane protein is an appropriate sensor for monitoring the local membrane fluidity. Linking of Nile red to the receptor via a flexible tether was achieved with the acyl carrier protein (ACP)-tag method. Experiments showed that depending on the ACP site a certain linker length is required to have NR inserted in the membrane and thus be an effective sensor for lipid disorder. This technology could be of general usability to study the environment of membrane proteins in the context of their function. As an example, the technique allowed insulin induced membrane disorder in the close insulin receptor vicinity to be observed. Further, results suggested that tyrosine activity is required for this disorder to happen. The experimental results appear to be complete and controls were made.

**Major comments:** 1) Sometimes technical terms are used without explanation: What is the GP value? What is ACP-IR? The spectrum was measured in number of rois? The reader can find those abbreveations out, but it would be nice to have them defined.

We have made a list of abbreviations.

2) Fig. 1d) is confusing. The ACP-IR labelling is evident in 3 panels, but there is no difference in the color (emission spectra of 1992-ACP-IR vs 2031-ACP-IR should be visible??). The DAPI staining is very different. When doing the latter, how difficult is it to get the staining equal?

The differences in spectra cannot be seen because we used pseudo colors for display of the DAPI and CoA-PEG-NR staining. The reviewer’s comments about the unequal DAPI staining is correct. The reason for this is most likely that the cell membrane is unequally permeabilized by PFA treatment. As the point of this figure is just to show that the plasma membrane is labeled, dependent upon the expression of the ACP-tagged insulin receptor, we don’t think that the variable intensities of the DAPI staining is important. DAPI is simply used to indicate the position of the cells.

3) How can one interpret Fig. 4: a) Control goes over 4 frames, at 240" insulin is added, and 10 frames should show a fluctuation difference?

We showed 4 frames after control treatment that showed no significant change was observed by control treatment. We expected that clear changes would be invoked by insulin treatment in GP images, however these changes, while visible in the GP images, are difficult to see for the untrained observer. This is the reason why we used the ZNCC method in the subsequent figures to better visualize the changes.

1. b) A color shift from blue to green is visible after insulin addition. But it is faint - difficult to assess from the pseudo color scheme. What does 1000 pixel top/1000 pixel bottom mean in c). Is it an attempt to better visualize the fluctuation? It is difficult to recognize a difference before and after adding insulin. d) It seems that the kymograph set should show this. What is the color scale? Why is 3 so untypical, i.e., no change? Box 6 is also peculiar: the left side does not show a strong change upon insulin administration, the right side does. Why? We appreciate the helpful comments for improving our manuscript.

As pointed out, the change of GP value is extremely small before and after insulin addition, so it is difficult to fully visualize the change with normal pseudo-color expression. To deal with this, we adopted the following two methods to visualize minute changes.

1) Visualization of local changes of the statistical GP value showed by ZNCC throughout the time-lapse images (Fig. 6 and Fig. S2B).

2) Visualization of the top/bottom 1000 pixels of the sorting ZNCC value in each image (Fig. 7 and Fig. S2C). The top 1000 pixels are the ones that showed the largest changes. The bottom 1000 pixels are the ones that showed the smallest changes.

Owing to these expressions, we found out that the level of the response against the insulin signal was spatially and temporally heterogeneous in the membrane.

As for the color scale, in order to clarify the meaning of the difference of color, we have added the description about the relationship between the color and the ZNCC value in the results section.

4) How is the kymogram calculated? The legend says 'The horizontal dimension represents the averaged ZNCC inside the rectangular area, and the vertical dimension represents time'. The averaged ZNCC is a single value, so it is not clear why the kymogram shows a variation from left to right. May it be the ZNCC was averaged just vertically?

We apologize that we did not provide information regarding making the kymograph.

In the yellow rectangular area (Fig. 6B), the ZNCC values of the pixels with the same x coordinate value were vertically averaged, which were represented as the horizontal direction of the kymograph. That is, one horizontal line of the kymograph holds the spatial distribution of the ZNCC value along the horizontal direction of the membrane, and the vertical direction shows their time changes. To make it easier to understand, we refined the description about the kymograph in the legend of Fig. 6.

5) When calculating cross-correlation values on images, they need to be aligned. What fraction of the total image does the selected 19x19 box represent? As described, I imagine that a rolling CC over 19x19 pixels is calculated over an image from the time lapse series comparing it with the reference Iave(x,y). Compared to the 3x3 median filtered CP image, the ZNCC image should then be much more blurred??

Below we provide more information regarding the calculation of ZNCC.

Each local window for ZNCC calculation is set to a 19x19 pixels centered on every single pixel excluding the edges of an image. The ZNCC value calculated in that window is set to a center pixel of that area. After that, a new window centered on the adjacent pixel is set and calculate the new ZNCC. That is, the calculation window is slid throughout the image. Also, the calculated ZNCC value is not set to all the pixels of the window, but is set to only the center pixel of the window, so there is no blur effect like median filtering.

The figure below shows a schematic view of our ZNCC calculation.

Schematic view of our ZNCC calculation

**Minor comment:** On page 16 supplementary is not spelled properly.

corrected

Reviewer #1 (Significance (Required)):

The key point of this paper is convincing and the new technology appears to have a lot of potential. It can be applied to study membrane protein function in the context of its environment, the lipid bilayer.

Membrane fluidity measurements have been developed (e.g., using fluorescent probes like laurdan). However, the trick to link a probe like nile red by ACP technology to the insulin receptor and to observe its activity is quite new.

A most recent description of such a technology is in TrAC Trends in Analytical Chemistry Volume 133, December 2020, 116092.

This is an interesting review, but not directly impacting on our work.

**Referees cross-commenting**

All comments are constructive and important. The paper is important but needs to be amended as proposed.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): **Summary:** In this manuscript, authors generated an ACP-attached Nile Red probe in order to specifically label Insulin receptor in the membrane. Owing to this specificity, one can measure the lipid membrane properties around a specific protein in the membrane. **Major comments:**

For the conclusions in the manuscript to be convincing, in my opinion, these additional data need to be added. Some of these are new experiments, and some are detailed analysis of existing data. The new experiments are not for new line of investigation, instead it is to confirm their statements and conclusions. The major point is the reliability of spectral shift. In usual environment sensitive probes, it is certain that they are in the membrane whatever is done to the membrane. However, when the probe is attached to a protein, it is not trivial to have the same confidence that the probe is always inside the membrane, and it is in the same plane of the membrane. 1992-ACP-IR is a good example; authors state that it binds to the protein outside the membrane, but when there is cholesterol addition and -maybe more interestingly- cholesterol removal, the dye still reacts and changes its emission (even PreCT changes its emission quite a bit at the 570 nm region). This is a clear indication of a change in localization of the probe upon some changes in the membrane. This implies that observed spectral shifts may not be due to lipid packing differences, but due to localization of the probes. For this reason, it is crucial to know where any environment sensitive probe localize in the membrane with respect to membrane normal, and this knowledge is more important for this probe. Related to this, the spectral difference upon insulin treatment and activation of insulin receptor could be due to changes in probe's localization in the membrane. Especially because authors show in Fig1e, the spectra can change depending on the probe localization. Relatedly, quantum yield of NR should be significantly different when it is inside vs outside membrane. Authors should show QY for 1992-ACP-NR and 2031-ACP-NR with different PEG lengths and upon insulin treatment.

We understand the logic of the request to measure the QY, since the QY of Nile red is much higher in organic solvents than in aqueous solutions, so it might be predicted that the QY of Nile red is higher in a lipid bilayer than when covalently bound to the protein in an aqueous environment. However, this argument depends upon the mechanism for the increase in quantum yield when going from aqueous to a non-polar solution. One possible explanation is based on the intrinsic properties of the dye under the two conditions. The alternative explanation would be that the dye would aggregate (be insoluble) in aqueous solution and therefore either not fluoresce or self-quench. In this case, we believe that the latter is the explanation because we and others have previously shown the turn-on properties of the probe when binding to proteins (SNAP-tag and others). It is not simple to measure QY in the cell under a microscope, but we have done something similar shown in supplementary figure 4. We labeled the three ACP-receptor complexes with PEG11-Nile red and co-stained with antibody to the Insulin Receptor. We then calculated a relative quantum yield. There were very little differences at all between the relative quantum yields, so we conclude that it is not the environment of the probe, which affects the quantum yield under these conditions, but the fact that it is covalently attached to a protein and incapable of forming aggregates. What distinguishes these constructs is the emission spectrum, not the quantum yield. In supplementary Table 2 we also did QY measurements in vitro and we could reproduce the increase of quantum yield by association with liposomes or in organic solvents. We tested whether non-covalent association with a protein would increase the QY by incubation with the lipid binding protein, BSA, in PBS. This was not the case, strongly pointing to the conclusion that it is the covalent association with the protein that increases the QY, not association with a protein. We believe that our demonstration of changes in fluorescent spectra with changes in cholesterol, large changes in fluorescent spectra with linker length for the 1992 construct and voltage sensitivity using patch-clamp prove that the Nile red is reporting on the membrane environment under the conditions we propose.

**Minor comments:** - Fig 1d requires quantification We do not agree on this. This is simply to show that the labeling is dependent upon expression of the relevant ACP-IR constructs. There is no detectable labeling of the control.

• Voltage sensitivity of different PEG length of 2031-ACP probe should be added. We have added this data in figure 2 panel E.

• Fig 3a graph should show all data points, not only bar graphs. Also, the band in 3a for +CoA-PEG-NR is dimmer than other bands, is it specific to this particular gel since quantification does not show any difference?

There is no significant difference- Fig 4d, colour code is needed.

Done

• Fig 5b and Fig3d are basically the same experiments in terms of control measurement, why is the difference in 3b is 0.04 GP unit while it is 0.007 GP unit?

We explain in the MS, but have improved the title of Y-axis in Fig.5 b graph so that the difference in what is plotted is clear. - Why is inhibitor data so noisy? We should discuss.

We don’t know the exact reason why inhibitor data is noisy, but we speculate that the actin cytoskeleton and phosphoinositide-dependent signaling could affect the membrane stability, and the membrane environment would be fluctuated in the presence of latrunculin B or PI3K inhibitor.

Reviewer #2 (Significance (Required)): Overall, this is a very useful approach, and this line of research will yield very useful tools to shed light on how lipids surrounding proteins can change their function. Major advance of the paper is the new chemical biology tool. There is also biological data on how insulin can change the insulin receptor's membrane environment which is contradictory to some old literature claiming that InsR becomes more "rafty" upon insulin treatment (e.g., PMID: 11751579).

If this type of tagging proves robust and reproducible (limitations and concerns listed above and below), it could be used by other researchers to tag their protein of interest and investigate the lipid environment around those proteins.

The downside of this method is that the probe requires ACP tag, a relatively less used tag than others in biology, therefore researchers interested in using this probe should have their proteins with ACP tag. Moreover, the linker length and ACP-tag position are quite crucial parameters (and probably should be optimized for each protein). Longer PEG lengths cannot report on changes efficiently (Fig3b), while shorter lengths are prone to artefacts as they can go out of membrane (Fig1 and Fig2). This might limit its widespread use.

The reason for using the ACP tag is that neither the SNAP tap nor the HALO tag working. The tethered Nile Red preferred to bind to the tqg rather than inserting into the membrane.

**Referees cross-commenting** I agree with all comments and concerns of other reviewers. I see the usability and potential of this new technology along with its limitations as all three reviewers pointed out.

Reviewer #3 (Evidence, reproducibility and clarity (Required)): See below. No concerns on any of these issues.

Reviewer #3 (Significance (Required)): **Critique:** This MS reports a proof-of-principle for using site-directed environmentally sensitive probe technology to assess the local membrane environment of a receptor tyrosine kinase (IR) upon activation. This technology addresses a major gap in our arsenal of tools to study the mechanisms of membrane signaling as the parameters of interest are biophysical parameters rather than purely biochemical ones. How to do this with spatial and temporal resolution is a major challenge. This study builds on previous work by the Riezman group that develops an extrinsic labeling system to tether Nile Red to specific sites on the ectodomain of a signaling receptor and then probe local membrane environments as a function of receptor activity. This is a carefully done study is well-controlled, is clever in design and is well-described. Although the major issues to which such a general technology could contribute involve intracellular (and not extracellular) event, the advances described will be of general interest -- particularly that local membrane order decreases when IR becomes activated. Specific comments for the authors' consideration follow:

**Specific Comments:** (i) As a general comment, the authors are measuring extracellular plasma membrane leaflet properties that may or may not translate to what is happening in the local inner leaflet environment. A general reader may well miss the significance of this. This point needs to be more explicitly emphasized in the Discussion.

This has been discussed in the revised version.

(ii) Why not treat cells with a PLC inhibitor to block PIP2 hydrolysis and ask if that inhibits membrane disorder. It is PIP2 hydrolysis/resynthesis that regulates the actin cytoskeleton at signaling receptors and this seems an attractive candidate for study.

There is a long list of attractive post-signaling events of the insulin receptor and how this works in different cell types that could be tested. We believe that this is beyond the scope of this study and we encourage others to do this.

(iii) The data acquisition time is at least 4 min which is long enough for activated receptors to be recruited to sites of endocytosis. Can the authors exclude the possibility that what they are measuring isn't reflective of such spatial reorganization? Does a clathrin inhibitor block the observed change in local membrane order for activated IR? We determined localization to AP2 adaptor containing clathrin coated pits at the cell surface and showed that during the time-course of the experiment that there is no significant change in co-localization or evidence for endocytosis (new figure 9). Therefore, we decided not to do the clathrin inhibitor blocking experiment because we believe that it could only lead to indirect effects.

(iv) Receptor activation is accompanied by other transitions such as dimerization, etc. Can the authors exclude the possibility that what they are measuring is related to changes in depth of insertion of the NR probe into the plasma membrane outer leaflet that is a consequence of IR conformational transitions associated with activation? This is highly unlikely given the fact that fluidification of the membrane environment is found with all length linkers. Given the intervals in increases in linker length on the 2031 construct, which is the closest to the membrane, it is very difficult to conceive that any of the ones larger than 5 PEGs restrict significantly the membrane insertion of the dye. **Referees cross-commenting**

I think we have a consensus opinion

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Referee #3

Evidence, reproducibility and clarity

See below. No concerns on any of these issues.

Significance

Critique:

This MS reports a proof-of-principle for using site-directed environmentally sensitive probe technology to assess the local membrane environment of a receptor tyrosine kinase (IR) upon activation. This technology addresses a major gap in our arsenal of tools to study the mechanisms of membrane signaling as the parameters of interest are biophysical parameters rather than purely biochemical ones. How to do this with spatial and temporal resolution is a major challenge. This study builds on previous work by the Riezman group that develops an extrinsic labeling system to tether Nile Red to specific sites on the ectodomain of a signaling receptor and then probe local membrane environments as a function of receptor activity.

This is a carefully done study is well-controlled, is clever in design and is well-described. Although the major issues to which such a general technology could contribute involve intracellular (and not extracellular) event, the advances described will be of general interest -- particularly that local membrane order decreases when IR becomes activated. Specific comments for the authors' consideration follow:

Specific Comments:

(i) As a general comment, the authors are measuring extracellular plasma membrane leaflet properties that may or may not translate to what is happening in the local inner leaflet environment. A general reader may well miss the significance of this. This point needs to be more explicitly emphasized in the Discussion.

(ii) Why not treat cells with a PLC inhibitor to block PIP2 hydrolysis and ask if that inhibits membrane disorder. It is PIP2 hydrolysis/resynthesis that regulates the actin cytoskeleton at signaling receptors and this seems an attractive candidate for study.

(iii) The data acquisition time is at least 4 min which is long enough for activated receptors to be recruited to sites of endocytosis. Can the authors exclude the possibility that what they are measuring isn't reflective of such spatial reorganization? Does a clathrin inhibitor block the observed change in local membrane order for activated IR?

(iv) Receptor activation is accompanied by other transitions such as dimerization, etc. Can the authors exclude the possibility that what they are measuring is related to changes in depth of insertion of the NR probe into the plasma membrane outer leaflet that is a consequence of IR conformational transitions associated with activation?

Referees cross-commenting

I think we have a consensus opinion

Author Response

Reviewer #1 (Public Review):

This study addresses the important question of understanding the cellular physiology of cholinergic interneurons in the striatum. These interneurons play a key role in learning and performance of motivated behaviors, and are central to movement disorders, psychiatric disease, and addiction. Their unique physiology, which includes tonic pacemaking activity and active conductances that shape integration of dendritic inputs, is critical to their function but is still incompletely understood. The authors cleverly integrate a series of innovative electrophysiological and optical approaches to gain insight into dendritic physiology of these neurons. Their creative approach yields some interesting and novel findings. However, there are technical and conceptual concerns that need to be addressed before these results can be readily interpreted. Some refinement of analysis and presentation, and potentially some additional experiments, will therefore be required to strengthen the conclusions and facilitate interpretation of the results.

We believe that with several new sets of experiments and simulations, we have successfully refined the analysis and addressed the technical and conceptual problems. Indeed, we strengthened the conclusion with a novel pharmacological experiment that provided model-independent evidence of proximal-only boosting.

Major concerns:

1) This manuscript focuses on differential physiology of proximal and distal dendrites contribute to physiological activity and integration of inputs in cholinergic interneurons, suggesting that NaP and HCN currents act in concert to selectively boost inputs onto proximal dendrites (from thalamus), relative to inputs onto distal dendrites (from cortex). The results presented in Figures 1-4 are consistent with a distinct physiology of proximal-vs-distal dendrites based on purely electrical properties. Indeed, Figure 5 initially appears consistent with this model as well, since thalamic inputs (onto proximal dendrites) are boosted by an NaP conductance, while cortical inputs (onto distal dendrites) are not. This raises a key conceptual question: why are cortical inputs onto distal dendrites not boosted? Any depolarization of distal dendrites must pass through proximal dendrites before reaching the recording electrode at the soma. Shouldn't this signal be subject to the same active and passive conductances, and consequently the same boosting that shapes thalamic inputs onto proximal dendrites?

You are absolutely right in the case of a linear model (passive or quasi-linear). However, for a nonlinear system, there can be preferential boosting of proximal inputs. The new Appendix 2, addresses this point with computer simulations.

2) The quasi-linear approach to characterizing active and passive membrane properties is promising, and the choice of a cable-based model is well supported. However, the model itself is rather opaque, which limits confidence in the interpretation of the results. Additional analysis and description should be presented to alleviate concerns about whether the experimental data, which has a limited number of measurable values, may be over-fit by a model with too many free parameters. For example, why is the radius of the dendrite a free parameter that is allowed to vary in the full field vs proximal experiment (Lines 253-256) - and isn't it a serious red flag that the value returned for proximal dendrites is smaller than for the full field? Additional tables (e.g. fixed and free parameters and how they were determined), and figures (plots of how those parameters influence the fits, and how the parameters interact with one another) would considerably strengthen confidence in the conclusions drawn by the authors.

Thank you very much for this comment. We have added in the new ms a table with all the parameters fit in the various figures, and have discussed the possible pitfalls of overfitting. Most importantly, we have provided a new appendix (#1) to the manuscript that explains the effects of the various model parameters in a systematic fashion, beginning with a passive dendrites, followed by the effects of boosting and then the effect of restorative currents that give rise to resonances. This appendix addresses the questions raised by the reviewer regarding how the various parameters influence the fits.

We apologize, if we created a confusion, with respect to the meaning of the parameter r. It does not represent the radius of the dendrites (which is not explicitly represented at all, only implicitly through the space constant) but rather the electrotonic range of illumination. We indeed find that the fits consistently estimate a value of r for the proximal illumination which is smaller than that estimated for the full-field illumination, as it should.

Finally, our new pharmacological demonstration of differential boosting in the case of proximal vs. fullfield illumination (see above) is entirely independent of the quasi-linear model fit. So for the main thrust of the ms, which is to demonstrate a proximal localization of nonlinearities and its correspondence to the spatial localization of excitatory afferent inputs, this is now achieved, at least vis-à-vis the NaP current, independently of the qausilinear model. However, we still find the model useful as it is used to estimate the distribution of HCN currents and provides a framework to think about how to manipulate dendritic nonlinearities experimentally.

3) Technically, the use of ChR2 to modulate dendritic currents is creative. While the authors rightly acknowledge that activation/deactivation kinetics of the ChR2 channel will contribute to filtering, this important point should be expanded with additional analysis and potentially with new experiments. Of particular concern is the transition of ChR2 channels to an inactivated state over the comparatively long oscillating light pulse in Figure 3 Inactivation of ChR2 is prominent over this timescale and would precisely co-vary with the shift in oscillation frequency. To address this, the authors should present a direct measurement of this inactivation and account for it in their analysis of the chirp data. Alternatively, the chirp stimulus could be presented backwards (starting at high frequency), so that comparison of forwards-vs-backwards chirp recordings could disentangle this artefact. Either one or both of these additional experiments would be critical for interpreting the roll-off in photocurrent responses at high frequencies reported in Figure 3.

Touché! You were spot on with this critique and we were wrong. We have now conducted several new experiments (that appear in the main text and in Figure 3 and all its supplements) that show that including ChR2 kinetics explicitly in the model fits actually makes the fits more self-consistent and removes some of the glaring differences between the results from the somatic voltage perturbations (Figures 1–2) and the optogenetic illumination (Figure 3). So as per your request, we have now presented a direct measurement of the deactivation (Figure 3–figure supplement 1) and we have played the “chirp” backwards (Appendix 1–figure 2) to address the issue of inactivation.

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Reply to the reviewers

First we would like to express our deep gratitude to the reviewers for thoroughly and fairly reviewing our work.

Reviewer #1:

Major Concerns

1. A major concern I have is with the use of DAPT to modulate Notch signaling, and investigate the impact on integrins, Yap, cadherins, etc. Gamma-secretase, the target of DAPT, cleaves not only Notch receptors, but also IntegrinB1, Nectins, Cadherins, Ephrins and more. This recent review lists 149 substrates (Guner & Lichtenthaler Seminars in Cell & Developmental Biology 2020). The risk that some of the results reflect DAPT impact on IntegrinB1, Cadherins etc themselves is significant. The authors should validate their findings with more specific modulation of Notch activity, for example with a Notch blocking antibody, with siRNA, or with SAHM1. We agree with the reviewer´s comment and will add additional key experiments using SAHM1 as alternative inhibitor of Notch activity.

Furthermore, EGTA was used to "acutely destabilize VE-Cadherin". But EGTA chelates Calcium, which is essential for Notch structure, and EGTA is thus a well-known activator of Notch signaling (see eg Rand MD et al. (2000) Calcium depletion dissociates and activates heterodimeric notch receptors. Mol Cell Biol). The authors rightfully describe and cite this paper, but the use of EGTA nonetheless confounds interpretation. The authors check for NICD levels (at what timepoint?) but the staining is cytoplasmic (also not labelled in the figure per se, but described in the figure legend? - please label the staining in the panel). And in any case, NICD is very short-lived and nuclear staining cannot be taken as a hallmark of signaling activity. In particular if staining is performed at a time point at which the receptor and NICD may have been exhausted/depleted. The authors should validate these observations/conclusions with the Notch reporter to conclusively demonstrate whether EGTA does not activate Notch in their system.

To test whether transient treatment with EGTA causes Notch activation we will repeat this experiment with Notch reporter activity as readout.

Trans-endocytosis of NECD on different substrates: the authors suggest that trans-endocytosis of NECD by Dll4 increases on softer substrates. But the authors also show that soft substrates lead to spreading out of cells, which could confound interpretation (is overlapping membranes, not internalization). The authors could validate trans-endocytosis by FACS: check if red Dll4+ cells contain more NECD. It is also not clear to me in this experiment whether the authors are looking at green NECD, or Notch1 full length, since they write "overlap of Notch1 and Dll4", which would not reflect trans-endocytosis but interactions at the cell surface for both cells. Please also define "overlay intensity", or explain further.

We will validate the trans-endocytosis by flow cytometry. In addition, we describe the procedure for microscopic analysis more clearly (methods section, p 4; results section, p 17-19)

The authors conclude their introduction with a statement that mechanosensitivity of Notch is linked to endocytosis, but their conclusion from Fig 6C was that Notch stiffness-dependence was independent of endocytosis, using the rhDll4..?

We have now rephrased this sentence.

• *

Minor concerns

1. In the introduction, the authors describe Dll3 as a Notch ligand that activates Notch signaling in trans. To my knowledge, Dll3 has only been described as a cis-inhibitor of Notch signaling. (I think this may have arisen during repeated edits of the manuscript!) This has now been corrected in the current version.

In the introduction, the authors state that Notch1, Dll4 and Jag1 control angiogenesis, but then they only describe what Notch1/Dll4 do in the next few sentences. Perhaps one sentence to describe the role of Jag1 would help avoid the feeling of being "left hanging".

This has now been corrected in the current version.

Data presentation: please show all bar graphs with the individual replicates (dotplots).

We have now changed all bar graphs into scatter plots.

Data analysis/normalization: many graphs represent normalization of values in multiple steps which are not described in the methods/legends/results. For example, Notch reporter gene activity (Fig 1A) is Firefly divided by Renilla, and presumably normalized to the control condition at 1 (or an average of 1 for the three controls?). This is not explained. Also, it is not clear whether the data reported for the Control condition are Huvec on rhDll4 compared (normalized) to Huvec on control substrate (and similar for each other condition). What controls are included in this experiment? Please provide the full data to provide insight into the magnitude of activation by Dll4 itself. Perhaps "Control" is without rhDll4? But the bar underneath A/B implies this rhDll4 was used in all conditions.

We have edited our manuscript accordingly to avoid these ambiguities.

Statistics: data should be presented as means +/- standard deviation, not standard error of the mean (see for example Barde & Barde Perspect Clin Res. 2012): "SEM quantifies uncertainty in estimate of the mean whereas SD indicates dispersion of the data from mean. As readers are generally interested in knowing the variability within sample, descriptive data should be precisely summarized with SD."

We now use SD instead of SEM.

Statistics: In the Methods section, the authors state that one-way ANOVA was followed by Dunnett's multiple comparison test, and two-way ANOVA was followed by Tukey's multiple comparison test. Dunnett is used to compare every mean to a control mean, while Tukey is used to compare every mean with every other mean. Fig 1 describes using Dunnett for Fig 1B, but the end of the legend days Tukey was used. However Fig 1A,C show internal pairwise comparisons to plastic. Please be sure to explain which statistics were used where, and why, and if plastic was set as the comparator, please be explicit about this. Fig 3 uses "Sidak's corrected two-way ANOVA" and "Sidak's multiple comparison test"? I think Sidak is a method to correct alpha or p for multiple comparisons, as stated in the first instance, but it is described why this was used here, and not in other analyses, and whether the authors then applied Tukey's post-hoc test as described in the methods section? Similar comments for Fig 6. It is counter-intuitive that the plastic -1.5kPa PDMS difference with no error-bar overlap in 1A would be 1-star significance, while the plastic-70kPa difference with almost overlapping error bars in 1B would be 4-star significance. Please check/show values. In Fig 1B Figure legend, the authors write "Data is presented in a bar plot and compared with the integrin β____1 intensities without DAPT treatment", but this is not the statistical comparison presented. Fig 3B shows a very minor difference with overlapping error bars as 3-star significance? Is this correct?

We have checked all statistical issues and corrected where necessary. Since the sample size and variance were homogenous in all comparisons we now uniformly use ANOVA and Tukey´s multiple comparison test as post hoc to keep things simple.

How much nuclear NICD (NICD intensity) is there in control conditions? (Control missing from Fig 1B, D).

We will repeat the experiment and compare the NICD levels with those in non-activated cells on plastic.

A DAPI counterstaining for 1B/D right panels would facilitate evaluation of whether NICD nuclear intensity is increased. The same applies for nuclear YAP assessment in Fig 3B. I assume a nuclear counter-stain was done for quantification of nuclear NICD intensity, and nuclear YAP intensity, but this is not described in the Materials and Methods, please add a description of how intensity was quantified, and provide nuclear counterstain images. (Also, what is the unit on the y-axis of "intensity" graphs? Arbitrary units (a.u.)?

The counterstaining method with Hoechst as well as the use of the nuclear staining for quantitative analysis of images are now described in the Methods section and where needed in the figure legends. The y-axis of the intensity graphs now has a dimension (a.u.). We decided against overlay of the nuclear staining with the NICD or YAP images for graphical reasons (visibility of the respective staining).

How much "overall" integrin B1 is there in DAPT-treated conditions in Fig 2C? (related to the concept that DAPT could be cleaving integrin B1, it could be depleted at 24 hours..?)

We will additionally add this experiment and validate the effect of Noch inhibition on the overall intergrin level by the alternative inhibitor SAHM1

More details regarding the analysis procedure need to be added to the Methods Section. Were cells segmented and then mean intensity estimated for the whole cell? Was this done by means of Intensity Ratio Nuclei Cytoplasm Tool plugin for Fiji alone? Were images background corrected, corrected for inhomogeneous illumination, normalized? In the case of Integrin beta 1 active, the expression seems to be patterned, was intensity expressed as mean intensity of every pixel corresponding to cytoplasm? For VE Cadherin staining, how was intensity estimated (only pixels corresponding to membrane were considered or every pixel of the cell)? Many figures are originated from a confocal microscope: were z-stacks acquired and then maximum projections done? Were z-stacks acquired and then fluorescence quantified in 3D images? Was a single plane acquired or analyzed, and if that is the case, how was this plane chosen?

The requested information has now been inserted in the respective results and method sections.

In Fig 4A, how is VE-Cadherin intensity quantified? As an average per field of view? Or per cell? And if per cell, how was each cell delineated? And if not per cell, how were equal cell numbers ensured? In FRAP experiment, how was intensity quantified? Was it per cell, per field of view or per region? Was each bleached region analyzed separately, or each cell? The datapoints should be either added to Figure 4C or as supplementary to assess the fitting. How many bleached regions per cell were done and how many cells were analyzed? In FRAP experiment, was bleaching done with an increased pixel dwell time? Was laser intensity increased? Do you have an estimation of laser power (not percentage) or flux?

These issues are now described in more detail in the respective figure legend.

Figure S2 is not referenced in the manuscript - I think a reference to "Figure S3" in the NECD transendocytosis section (no page numbers or line numbering) should be to Fig S2 instead?

Sorry for this mistake! We corrected this now.

In Figure 5A NICD nuclear intensity normalized somehow (normalization not explained), and stiffness no longer appears to regulate NICD levels as shown in Figure 1B.

We have now described the normalization better in the figure legend. The difference to the results in Fig. 1B is that in Fig. 5A the cells were not activated by Dll4 sender cells or rhDll4 (endogenous Notch activity). This is now stated more clearly.

Fig 6B: From the immuno at right there is a clear stiffness-dependent difference in Transferrin uptake. How were "single cell uptake" and "number of particles" quantified? (How were cell bodies identified?) Uptake could also be verified with FACS.

In this point, we disagree with the reviewer: we really do not see a systematic difference in intensities between the different substrates. The process of image analysis is now better described in the figure legend. The result was so clear that we did not use FACS as complementary approach.

Fig 6C: there appear to be very different numbers of cells in the brightfield image at right. Are the 70, 1.5, and 0.5 kPa Notch reporter activities different from one another or only different from plastic? Might these results reflect cell density/increased Notch signaling due to more cell-cell contacts?

Unfortunately, with decreasing stiffness the PDMS gels become optically more and more cloudy, giving the false impression of a higher cell number. We tried to circumvent this by changing contrast and brightness of the images, but to no satisfying effect. We now mention this issue in the figure legend.

How was the Dll4 coating of the different substrates done?

The coating of the substrates is now described under a specific subheading in the Methods section.

It would be helpful to describe the composition of Collagen G (Collagen I) in the text (it is a risk to expect vendor information to remain available indefinitely).

The role and composition of the Collagen G coatings was included in the text (p 7). Further information on the manufacturer of the product used is included in the methods section.

Please list catalog numbers for all reagents, and dilutions used for antibodies.

We have added this information wherever possible.

Instead of using red and green for images, maybe cyan, yellow and/or magenta could be used to help the reader see what is being shown (especially if the reader might be color blind).

We will of course adhere to the respective policy of the publishing journal, once the manuscript is accepted.

Packages and tools such as Intensity Ratio Nuclei Cytoplasm Tool plugin for FIJI should be referenced.

We have now referenced respective tools.

Reviewer #2:

*Major comments: *

Is there difference on a growth rate of cells on softer vrs stiffer gels that could affect cell morphology/signaling pathways?

This is an important point and we will perform additional respective experiments.

Nuclear localization of NICD and YAP would be good to validate with western blot.

Quantification of Western Blots (especially after nuclear isolation) is – at least in our hands – much less sensitive and reliable then quantitative imaging. We do not think that this experiment would strengthen our study.

In Figure 3 and Figure 5, siRNA experiments would strengthen the data. DAPT is not only an inhibitor of Notch but affects to other proteins as well. This should be stated.

A similar point was raised by Reviewer#1 with the suggestion to use SAHM1 as an alternative to DAPT. As suggested we will add these experiments.

How was the mean VE-cadherin branch length determined? This term often refers to angiogenesis assay/sprout formation and maybe another one should be considered here to describe VE-cadherin junction morphology.

Add to all figure texts how many cells were used for the analyses*. *

The cell number is now added wherever appropriate.

In Fig. 6C the cell morphology of HUVECs look abnormal in comparison to other images and should be re-done.

In contrast to all other experiments the cells where not confluent in this case. The different morphology is a sign of the lack of neighbours, not of some problem with the cells.

Was all the data normally distributed and thus ANOVA was used? Please add more details on the statistics part. Did you remove outliers?

Like also suggested by Reviewer #1 we have added more information on statistics and streamlined this. The data are normally distributed, outliers wer not removed.

MTT assay of DAPT would need to be presented as it can be cytotoxic. Cells are not well visible in Fig 2C with DAPT. DAPI and F-actin staining would help to see the cell morphology.

We will add respective data on cell viability after DAPT (and SAHM1) treatment in a revised version of the manuscript.

Minor comments:

Please clarify how coating with rhDDL4 is done as this was unclear at least for this reviewer.

The coating of the substrates is now described under a specific subheading in the Methods section.

HUVECs are known to be hard to transfect. Please provide data on transfection efficiencies of all transiently transfected cells.

We did not systematically monitor transfection efficiencies in this context, since there was always an internal control (e.g. co-reporter in the reporter gene assay) or the data were obtained on a single cell based quantification. Generally, we yield transfection efficiencies around 30% with HUVECs.

Reviewer #3:

Major comments:

• *

1) The authors use recombinant Dll4 or Dll4-expressing ("sender") cells to activate Notch in co-cultured cells. This is per se fine however, one might over-estimate all other observed downstream effects as endogenous Notch activity is lower. It would be important to see how naïve HUVEC or other primary endothelial cells respond to changes in stiffness. qPCR of Notch target genes such as Hey1, Hey2, Hes5, Dll4 is frequently used as a readout of Notch activity in this context. Also. the Notch transcriptional reporter assay might be a suitable read-out-

In Fig.5A we show data on endogenous Notch activity (- EGTA) on substrates with different stiffness. In this case NICD levels in the nucleus do not differ. It will definitely be interesting to repeat this experiment based on the reporter gene assay.

2) As the authors mention in the Discussion, cell density could be of utmost importance given the fact that Notch signaling usually is assumed as an in trans signaling event between adjacent cell membranes. However, also other signaling modes (in cis, cis inhibition, JAG1 vs DLL4 ratio) might be important. As such, the authors should carefully document an report on cell density in all experiments. Secondly, the authors should use other conditions such as sparse cell density and thirdly the authors should measure transcriptional effects of stiffness on Notch ligand expression.

In all experiments (with the exception of Fig. 6C) we used confluent cells. With the sparse cells (Fig. 6C) we also observe stiffness dependency. Investigating Notch ligand expression is definitely a good idea and will be investigated in the revised manuscript.

3) The authors need to compare stiffness in their model with physiological conditions in developing tissues and ideally also in tumor which often have increased tissue stiffness.

*Good point! We have now integrated such comparisons in the Discussion. *

4) Is Notch activation due to changes in stiffness dependent on the presence of ligands or could it be that (unspecific) binding of Notch receptors to ECM could trigger cleavage just by conformational change?

Since there is no stiffness dependent response on collagen (Fig. 6C, left panel), an effect of unspecific binding is highly unlikely.

Author Response

Reviewer #1 (Public Review):

In this article, the authors investigated the role of sleep and brain oscillations in visual cortical plasticity in adult humans. The authors tested the effect of 2 hours of monocular deprivation (MD) on ocular dominance measured by binocular rivalry. In the main MDN session, MD was performed in the late evening, followed by 2 hours of sleep, during which EEG was measured. After the sleep session, ocular dominance was measured, which was followed by 4 hours of sleep, then ocular dominance was measured again in the morning. The results show that the effect of MD was preserved 6 hours after MD. The effect of MD correlated with sleep spindle and slow oscillation measures. The questions asked by the study are timely and findings are important in understanding the visual cortical plasticity in human adults, but I have some concerns regarding the experimental design, analysis, and interpretation of the results, which are listed below.

Thank you for the positive summary of our results.

• The authors investigated EEG activities in the central and occipital regions. The results of the relationship between slow oscillations / sleep spindles and deprivation index are very interesting. However, it appears that the activities were averaged across hemispheres in the occipital region. Previous studies (e.g. Lunghi et al., 2011; Binda et al., 2018) have demonstrated that MD is associated with up-scaling of the deprived eye and with down-scaling of the non-deprived eye (page 11). I wonder whether sleep slow oscillations and / or spindles are modulated locally in the deprived occipital region? To answer the first question raised by the authors (how MD affects subsequent sleep), wouldn't it be important to compare between deprived vs. non-deprived regions?

In humans, the pure monocular recipient cortical regions are very small and represent only very far visual periphery. These regions are impossible to be located by EEG and they are also difficult to locate also with high resolution fMRI (ref to Koulla CB). Visual cortical organization is based on the visual field map: neurons whose visu.al receptive fields lie next to one another in visual space are located next to one another in cortex, forming one complete representation of contralateral visual space, independently of the eye from which the visual information comes. However, at finer scales ocular dominance columns exist and Binda et al (2018) showed that in adult humans MD boosts the BOLD response to the deprived eye, changing ocular dominance of V1 vertices, consistent with homeostatic plasticity. All these are well known facts to the visual community, and we believe are not worthwhile to discuss them.

• To answer the second question (how sleep contributes to consolidation of visual homeostatic plasticity), the authors compared the deprivation index between two sessions, the main MDN and a control MDM session. The experimental designs for these two sessions were quite different. For example, MD was conducted in the evening in MDN, whereas it was conducted in the morning in MDM. Since there may be circadian effects on plasticity (Frank, 2016), the comparisons between these sessions may not be sufficient in investigating the effect of sleep itself (it could be merely due to circadian effect).

Thank you for raising this important issue. We performed the dark exposure experiment in the morning because we wanted to minimize the occurrence of sleep during the two hours spent by participants lying down in complete darkness. Preventing sleep under these conditions in the late evening would have been extremely challenging. In order to investigate a possible influence of the circadian rhythm on visual homeostatic plasticity and its decay over time, we have performed an additional experiment. In this experiment, we have tested the effect of 2h of monocular deprivation in the same participants either early in the morning or late at night (at a time of the day comparable to the MDnight and MDmorn conditions in the main study). We report the results of this control experiment in the supplementary materials (Figure S2). We found that the effect of monocular deprivation follows a similar timecourse for the two conditions (ocular dominance returns to baseline levels within 120 minutes after eye-patch removal). Moreover, we also report that the effect of MD is slightly (but significantly) larger in the morning, compared to the evening. The results of this experiment rules out a contribution of circadian effects and reinforces the evidence of a specific effect of sleep in maintaining visual homeostatic plasticity.

• The authors argue that NREM sleep consolidates the effect of MD. However, consolidation may last days to months or even years (Dudai et al., 2015). Since the effect is gone in 6 hours or so, it may be difficult to interpret it as consolidation. Although the findings of the effects of sleep on ocular dominance plasticity are interesting, the interpretations of the results may need to be clarified or revised.

We thank the reviewer for raising this issue. We agree that the data show a substantial delay in the decay process of the MD effects after the removal of the patch. The present data indicate that specifically the sleep condition and not merely darkness would be responsible for the maintenance of the MD-induced effect during the night. Therefore, we gladly adhere to the request and propose to say that sleep stabilizes/maintains the effects of MD as long as sleep itself persists. Having said that, we would like to point out that the MD boost in amblyopic patients gets consolidated for up to one year and increases across night sleep as we reported in Lunghi, Sframeli et al (2019). Although these data strongly suggest that real consolidation may occur, we agree with the reviewer that our data did not directly address this question and changed accordingly the manuscript.

Reviewer #2 (Public Review):

This manuscript is an interesting follow up on a substantial literature on the role of sleep in promoting critical period ocular dominance plasticity, and the role of sleep in promoting adult V1 plasticity following presentation of a novel visual stimulus. For nearly all of that literature (i.e. coming from cats and mice), the focus has mainly been on Hebbian mechanisms. The authors here propose to advance the field by investigating plasticity in adult human V1, which the authors consider to be homeostatic rather than Hebbian, and which the authors consider to be a form of sleep-dependent consolidation. This is an exciting goal, and the overall study designs and control will test the effects of brief MD and subsequent sleep or wake in the dark on V1 processing for the two eyes.

Thank you for the positive commentary on our study.

However, the outcomes of the study suggest that the changes observed in V1 across sleep may actually be the opposite of consolidation - rather it is decay of an effect on V1 function caused by prior wake experience (MD), which disappears over subsequent hours.

We thank the reviewer for raising this issue. We agree that the data show a substantial delay in the decay process of the MD effects after the removal of the patch. The present data indicate that specifically the sleep condition and not merely darkness would be responsible for the maintenance of the MD-induced effect during the night. Therefore, we gladly adhere to the request and propose to say that sleep stabilizes/maintains the effects of MD as long as sleep itself persists. We have revised the entire MS through the various sections to handle this important aspect and to consider that a classic correlate of memory consolidation during sleep (spindles density) also turns out to be associated with maintenance of the MD-induced ocular dominance effect.

The authors claim differences due to sleep, but there is not a direct statistical comparison between sleep and awake-in-the-dark controls.

We now directly compare the effect of monocular deprivation and its decay after two hours in the sleep vs dark exposure condition (MDnight vs MDmor). We now plot the results of the two conditions in the same graph (Figure 2). We found a significant interaction effect between the factors TIME (before and after) and CONDITION (MDnight and MDmor), indicating a specific role of sleep in prolonging the decay of short-term monocular deprivation.

There is also no quantification of sleep architecture across the sleep period, to determine whether REM or NREM play a role.

We have provided a summary table of sleep architecture in the revised version of the Supplementary Materials. The table shows descriptive statistics of sleep architecture on MDnight and CN. Also, we report the result of the paired comparison between the nights and the Spearman correlations between the deprivation indices (DI before and DI after) and the changes between the nights in sleep architecture. Tests indicate that MD does not produce any main effect on the sleep architecture and that there are no substantial associations found between sleep architecture parameters and deprivation indices. Thus, it appears that changes in SSO and spindle frequency and amplitude did not lead to an alteration in the amount of N2 or N3 sleep, as we might expect. At the beginning of the Results section we refer to the table and to the lack of statistically significant effects.

Finally, while there are tests of changes in NREM oscillations with previous plasticity in wake, there are no direct tests of changes across sleep - i.e. the very changes that could be considered consolidation.

We thank the reviewer for stimulating us to investigate whether there are any NREM parameters whose change within the sleep cycle can be related to the degree of plasticity maintenance observed at the end of the two hours of sleep.

For this aim, we 1) partitioned SSO and spindle events into tertiles according to their occurrence time, 2) estimated the average measures of events belonging to the first and last tertile, and considered the variation between tertiles as an estimate of the changes across sleep. We then tested whether there is a consistent relationship between measures of individual retained plasticity (DI after) and changes in SSO and sleep spindles across sleep.

We did the across sleep analysis of the SSO and spindles measurements and as previously explained none of the parameters showed associations across sleep with the individual DI after sleep. We report these results in the supplementary materials (Figure S8).

Finally is also not clear that the decay of response changes is due to homeostatic plasticity - it could be just that- decay of plasticity that occurred previously. The terminology used - e.g. consolidation, homeostatic vs. Hebbian - don't seem well founded based on data.

Thank you for raising an important point. In our study homeostatic plasticity refers to the effect of short-term monocular deprivation (so the plasticity occurred before sleep). We have rephrased the interpretation of our results in terms of stabilization/maintenance rather than consolidation of plasticity

About homeostatic vs Hebbian plasticity, there is a quite large agreement in the literature stating that indeed the effects are different. Now we make clear in the text that Hebbian plasticity is usually associated to the boost of most successful signals in driving a neuronal response or a behavior. Here the MD produced a boost of the unused, and probably silent, eye and as such the boost it is very difficult to explain in term of Hebbian plasticity. We make now this clear in the introduction.

Reviewer #3 (Public Review):

In this study, Menicucci et al. induced plastic changes in ocular dominance by applying an eye-patch to the dominant eye (monocular deprivation, MD). This manipulation resulted in a shift toward even more dominance of the deprived eye, as assessed though a binocular rivalry protocol. This effect was stabilized during sleep whereas it quickly decreases in waking (in the dark). The authors interpret the MD effect as the resultant of cortical plasticity over primary visual areas and its maintenance during sleep as the consolidation of these changes. The authors thus connect their work to the literature on sleep consolidation. They further show that the magnitude of the MD effect is positively correlated with sleep markers that are involved in memory consolidation (slow oscillations and sleep spindles).

However, I have first conceptual issues with this study. Indeed, previous findings on the replay of memories during sleep and their consolidation were mostly obtained in hippocampus-dependent forms of learning. Here, I do not really see what is it that would be replayed. Thus, I struggle understanding how rhythms, such as sleep spindles, that have been linked to the transfer of hippocampal memories to the neocortex, would be mechanistically associated with low-level plastic changes restricted to primary visual areas. In addition, the effects were observed over occipital electrodes, where sleep spindles are far fewer and lower in amplitude than other cortical regions. Furthermore, the association between MD-related plasticity and slow oscillations is interesting but, since these slow oscillations organize sleep slow waves, the lack of correlation with slow wave is surprising.

We agree with the review that many of our results are indeed surprising, especially those related to the involvement of the spindles and for these reasons we believe that eLife would be the appropriate journal to present our work. At present the fact that sleep spindles have been associated manly in mediating transfer of memory does not exclude a more general involvement in other sensory functions.

Connected to these conceptual issues, I think the present work has some important methodological limitations. First of all, the analyses included a rather small number of participants, which could make some analyses, in particular correlational analyses, severely underpowered.

We thank you for stimulating us to emphasize this limitation. In the section Participants within Materials and methods we pointed out that the complexity of the experimental design and the need to take into account the complexity of sleep expressed through different parameters, the sample size used and the need for corrections for multiple tests led to highlight only associations characterized by strong effect size.

Secondly, the approach used to explore the correlation between plasticity and sleep features focused on subset of electrodes (ROI) defined a priori. It is therefore difficult to conclude on the specificity of the results. Given the topographical maps provided by the authors, I am wondering if a more exhaustive analysis of the effect at the electrode level could not yield more robust findings.

The need for ROIs is based on the interindividual variability of brain structures, in particular the large anatomical variability of V1 orientation implying a variably oriented dipole and a variable maximal representation of visual potentials over electrodes from Oz to CPz. Moreover, we have to cope with the volume conduction effect that limits EEG spatial resolution.

With these limitations in mind, we very gladly adhere to the reviewer's request to evaluate the effects on individual electrodes in more detail. To this end we have prepared supplementary figures which show boxplots and scatterplots for the electrodes inside the ROIs to evaluate main effects and associations, respectively.

Finally, given the number of features tested, I think it is important to clarify the strategy used to correct for multiple comparisons.

We thank the reviewer for highlighting an unclear point. In the revised version of the Statistical analyses section, we have provided missing details of the procedure used for handling false positives due to multiple testing. Basically, we applied the FDR correction for each question we asked.

For example, “at which time points does dominance remain significantly different from baseline?” or, “which EEG feature and in which area of the scalp shows changes significantly dependent on plasticity induced by monocular deprivation?” For each of these questions, we made a group of tests (for the first example, dependent on the number of points at which ocular dominance was assessed until the morning; for the second example, on the number of EEG features examined multiplied by the number of areas in which they were assessed) to which Benjamini & Hochberg's FDR correction was then applied.

Author Response

Reviewer #1 (Public Review):

The role of the parietal (PPC), the retrospenial (RSP) and the the visual cortex (S1) was assessed in three tasks corresponding a simple visual discrimination task, a working-memory task and a two-armed bandit task all based on the same sensory-motor requirements within a virtual reality framework. A differential involvement of these areas was reported in these tasks based on the effect of optogenetic manipulations. Photoinhibition of PPC and RSP was more detrimental than photoinhibition of S1 and more drastic effects were observed in presumably more complex tasks (i.e. working-memory and bandit task). If mice were trained with these more complex tasks prior to training in the simple discrimination task, then the same manipulations produced large deficits suggesting that switching from one task to the other was more challenging, resulting in the involvement of possibly larger neural circuits, especially at the cortical level. Calcium imaging also supported this view with differential signaling in these cortical areas depending on the task considered and the order to which they were presented to the animals. Overall the study is interesting and the fact that all tasks were assessed relying on the same sensory-motor requirements is a plus, but the theoretical foundations of the study seems a bit loose, opening the way to alternate ways of interpreting the data than "training history".

1) Theoretical framework:

The three tasks used by the authors should be better described at the theoretical level. While the simple task can indeed be considered a visual discrimination task, the other two tasks operationally correspond to a working-memory task (i.e. delay condition which is indeed typically assessed in a Y- or a T-maze in rodent) or a two-armed bandit task (i.e. the switching task), respectively. So these three tasks are qualitatively different, are therefore reliant on at least partially dissociable neural circuits and this should be clearly analyzed to explain the rationale of the focus on the three cortical regions of interest.

We are glad to see that the reviewer finds our study interesting overall and sees value in the experimental design. We agree that in the previous version, we did not provide enough motivation for the specific tasks we employed and the cortical areas studied.

Navigating to reward locations based on sensory cues is a behavior that is crucial for survival and amenable to a head-fixed laboratory setting in virtual reality for mice. In this context of goal-directed navigation based on sensory cues, we chose to center our study on posterior cortical association areas, PPC and RSC, for several reasons. RSC has been shown to be crucial for navigation across species, poised to enable the transformation between egocentric and allocentric reference frames and to support spatial memory across various timescales (Alexander & Nitz, 2015; Fischer et al., 2020; Pothuizen et al., 2009; Powell et al., 2017). It furthermore has been shown to be involved in cognitive processes beyond spatial navigation, such as temporal learning and value coding (Hattori et al., 2019; Todd et al., 2015), and is emerging as a crucial region for the flexible integration of sensory and internal signals (Stacho & ManahanVaughan, 2022). It thus is a prime candidate area in the study of how cognitive experience may affect cortical involvement in goal-directed navigation.

RSC is heavily interconnected with PPC, which is generally thought to convert sensory cues into actions (Freedman & Ibos, 2018) and has been shown to be important for navigation-based decision tasks (Harvey et al., 2012; Pinto et al., 2019). Specific task components involving short-term memory have been suggested to cause PPC to be necessary for a given task (Lyamzin & Benucci, 2019), so we chose such task components in our complex tasks to maximize the likelihood of large PPC involvement to compare the simple task to.

One such task component is a delay period between cue and the ultimate choice report, which is a common design in decision tasks (Goard et al., 2016; Harvey et al., 2012; Katz et al., 2016; Pinto et al., 2019). We agree with the reviewer that traditionally such a task would be referred to as a workingmemory task. However, we refrain from using this terminology because it may cause readers to expect that to solve the task, mice use a working-memory dependent strategy in its strictest and most traditional sense, that is mice show no overt behaviors indicative of the ultimate choice until the end of the delay period. If the ultimate choice is apparent earlier, mice may use what is sometimes referred to as an embodiment-based strategy, which by some readers may be seen as precluding working memory. Indeed, in new choice-decoding analyses from the mice’s running patterns, we show that mice start running towards the side of the ultimate choice during the cue period already (Figure 1—figure supplement 1). Regardless of these seemingly early choices, however, we crucially have found much larger performance decrements from inhibition in mice performing the delay task compared to mice performing the simple task, along with lower overall task performance in the delay task, indicating that the insertion of a delay period increased subjective task difficulty. As traditional working-memory versus embodiment-based strategies are not the focus of our study here and do not seem to inform the performance decrements from inhibition, we chose to label the task descriptively with the crucial task parameter rather than with the supposedly underlying cognitive process.

For the switching task, we appreciate that the reviewer sees similarities to a two-armed bandit task. However, in a two-armed bandit task, rewards are typically delivered probabilistically, whereas in our task, cue and action values are constant within each of the two rule blocks, and only the rule, i.e. the cuechoice association, reverses across blocks. This is a crucial distinction because in our design, blocks of Rule A in the switching task are identical to the simple task, with fixed cue-choice associations and guaranteed reward delivery if the correct choice is made, allowing a fair comparison of cortical involvement across tasks.

We have now heavily revised the introduction, results, and discussion sections of the manuscript to better explain the motivation for the tasks and the investigated brain areas. These revisions cover all the points mentioned in this response.

Furthermore, we agree with the reviewer that the three tasks are qualitatively different and likely depend on at least partially dissociable circuits. We consider the large differences in cortical inhibition effects between the simple and the complex tasks as evidence for this notion. We also want to highlight that in fact, we performed task-specific optogenetic manipulations presented in the Supplementary Material to further understand the involvement of different areas in task-specific processes. In what is now Figure 1—figure supplement 4, we restricted inhibition in the delay task to either the cue period only or delay period only, finding that interestingly, PPC or RSC inhibition during either period caused larger performance drops than observed in the simple task. We also performed epoch-specific inhibition of PPC in the switching task, targeting specifically reward and inter-trial-interval periods following rule switches, in what is now Figure 1—figure supplement 5. With such PPC inhibition during the ITI, we observed no effect on performance recovery after rule switches and thus found PPC activity to be dispensable for rule updates.

For the working-memory task we do not know the duration of the delay but this really is critical information; per definition, performance in such a task is delay-dependent, this is not explored in the paper.

We thank the reviewer for pointing out the lack of information on delay duration and have now added this to the Methods section.

We agree that in classical working memory tasks where the delay duration is purely defined by the experimenter and varied throughout a session, performance is typically dependent on delay duration. However, in our delay task, the delay distance is kept constant, and thus the delay is not varied by the experimenter. Instead, the time spent in the delay period is determined by the mouse, and the only source of variability in the time spent in the delay period is minor differences in the mice’s running speeds across trials or sessions. Notably, the differences in time in the delay period were greatest between mice because some mice ran faster than others. Within a mouse, the time spent in the delay period was generally rather consistent due to relatively constant running speeds. Also, because the mouse had full control over the delay duration, it could very well speed up its running if it started to forget the cue and run more slowly if it was confident in its memory. Thus, because the delay duration was set by the mouse and not the experimenter, it is very challenging or impossible to interpret the meaning and impact of variations in the delay duration. Accordingly, we had no a priori reason to expect a relationship between task performance and delay duration once mice have become experts at the delay task. Indeed, we do not see such a relationship in our data (see plot here, n = 85 sessions across 7 mice). In order to test the effect of delay duration on behavioral performance, we would have to systematically change the length of the delay period in the maze, which we did not do and which would require an entirely new set of experiments.

Also, the authors heavily rely on "decision-making" but I am genuinely wondering if this is at all needed to account for the behavior exhibited by mice in these tasks (it would be more accurate for the bandit task) as with the perspective developed by the authors, any task implies a "decision-making" component, so that alone is not very informative on the nature of the cognitive operations that mice must compute to solve the tasks. I think a more accurate terminology in line with the specific task considered should be employed to clarify this.

We acknowledge that the previous emphasis on decision-making may have created expectations that we demonstrate effects that are specific to the ‘decision-making’ aspect of a decision task. As we do not isolate the decision-making process specifically, we have substantially revised our wording around the tasks and removed the emphasis on decision-making, including in the title. Rather than decision-making, we now highlight the navigational aspect of the tasks employed.

The "switching"/bandit task is particularly interesting. But because the authors only consider trials with highest accuracy, I think they are missing a critical component of this task which is the balance between exploiting current knowledge and the necessity to explore alternate options when the former strategy is no longer effective. So trials with poor performance are thus providing an essential feedback which is a major drive to support exploratory actions and a critical asset of the bandit task. There is an ample literature documenting how these tasks assess the exploration/exploitation trade-off.

We completely agree with the reviewer that the periods following rule switches are an essential part of the switching task and of high interest. Indeed, ongoing work in the lab is carefully quantifying the mice’s strategy in this task and exploring how mice use errors after switches to update their belief about the rule. In this project, however, a detailed quantification of switching task strategy seemed beyond the scope because our focus was on training history and not on the specifics of each task. While we agree with the reviewer about the interesting nature of the switching period, it would be too much for a single paper to investigate the detailed mechanisms of each task on top of what we already report for training history. Instead, we have now added quantifications of performance recovery after rule switches in Figure 1— figure supplement 2, showing that rule switches cause below-chance performance initially, followed by recovery within tens of trials.

2) Training history vs learning sets vs behavioral flexibility:

The authors consider "training history" as the unique angle to interpret the data. Because the experimental setup is the same throughout all experiments, I am wondering if animals are just simply provided with a cognitive challenge assessing behavioral flexibility given that they must identify the new rule while restraining from responding using previously established strategies. According to this view, it may be expected for cortical lesions to be more detrimental because multiple cognitive processes are now at play.

It is also possible that animals form learning sets during successive learning episodes which may interfere with or facilitate subsequent learning. Little information is provided regarding learning dynamics in each task (e.g. trials to criterion depending on the number of tasks already presented) to have a clear view on that.

We thank the reviewer for raising these interesting ideas. We have now evaluated these ideas in the context of our experimental design and results. One of the main points to consider is that for mice transitioned from either of the complex tasks to the simple task, the simple task is not a novel task, but rather a well-known simplification of the previous tasks. Mice that are experts on the delay task have experienced the simple task, i.e. trials without a delay period, during their training procedure before being exposed to delay periods. Switching task expert mice know the simple task as one rule of the switching task and have performed according to this rule in each session prior to the task transition. Accordingly, upon to the transition to the simple task, both delay task expert mice and switching task expert mice perform at very high levels on the very first simple task session. We now quantify and report this in Figure 2—figure supplement 1 (A, B). This is crucial to keep in mind when assessing ‘learning sets’ or ‘behavioral flexibility’ as possible explanations for the persistent cortical involvement after the task transitions. In classical learning sets paradigms, animals are exposed to a series of novel associations, and the learning of previous associations speeds up the learning of subsequent ones (Caglayan et al., 2021; Eichenbaum et al., 1986; Harlow, 1949). This is a distinct paradigm from ours because the simple task does not contain novel associations that are new to the mice already trained on the complex tasks. Relatedly, the simple task is unlikely to present a challenge of behavioral flexibility to these mice given our experimental design and the observation of high simple task performance in the first session after the task transition.

We now clarify these points in the introduction, results, and discussion sections, also acknowledging that it will be of interest for future work to investigate how learning sets may affect cortical task involvement.

3) Calcium imaging data versus interventions:

The value of the calcium imaging data is not entirely clear. Does this approach bring a new point to consider to interpret or conclude on behavioral data or is it to be considered convergent with the optogenetic interventions? Very specific portions of behavioral data are considered for these analyses (e.g. only highly successful trials for the switching/bandit task) and one may wonder if considering larger or different samples would bring similar insights. The whole take on noise correlation is difficult to apprehend because of the same possible interpretation issue, does this really reflect training history, or that a new rule now must be implemented or something else? I don't really get how this correlative approach can help to address this issue.

We thank the reviewer for pointing out that the relationship between the inhibition dataset and calcium imaging dataset is not clear enough. We restricted analyses of inhibition and calcium imaging data in the switching task to the identical cue-choice associations as present in the simple task (i.e. Rule A trials of the switching task). We did this because we sought to make the fairest and most convincing comparison across tasks for both datasets. However, we can now see that not reporting results with trials from the other rule causes concerns that the reported differences across tasks may only hold for a specific subset of trials.

We have now added analyses of optogenetic inhibition effects and calcium imaging results considering Rule B trials. In Figure 1—figure supplement 2, we show that when considering only Rule B trials in the switching task, effects of RSC or PPC inhibition on task performance are still increased relative to the ones observed in mice trained on and performing the simple task. We also show that overall task performance is lower in Rule B trials of the switching task than in the simple task, mirroring the differences across tasks when considering Rule A trials only.

We extended the equivalent comparisons to the calcium imaging dataset, only considering Rule B trials of the switching task in Figure 4—figure supplement 3. With Rule B trials only, we still find larger mean activity and trial-type selectivity levels in RSC and PPC, but not in V1, compared to the simple task, as well as lower noise correlations. We thus find that our conclusions about area necessity and activity differences across tasks hold for Rule B trials and are not due to only considering a subset of the switching task data.

In Figure 4—figure supplement 4, we further leverage the inclusion of Rule B trials and present new analyses of different single-neuron selectivity categories across rules in the switching task, reporting a prevalence of mixed selectivity in our dataset.

Furthermore, to clarify the link between the optogenetic inhibition and the calcium imaging datasets, we have revised the motivation for the imaging dataset, as well as the presentation of its results and discussion. Investigating an area’s neural activity patterns is a crucial first step towards understanding how differential necessity of an area across tasks or experience can be explained mechanistically on a circuit level. We now elaborate on the fact that mechanistically, changes in an area’s necessity may or may not be accompanied by changes in activity within that area, as previous work in related experimental paradigms has reported differences in necessity in the absence of differences in activity (Chowdhury & DeAngelis, 2008; Liu & Pack, 2017). This phenomenon can be explained by differences in the readout of an area’s activity. We now make more explicit that in contrast to the scenario where only the readout changes, we find an intriguing correspondence between increased necessity (as seen in the inhibition experiments) and increased activity and selectivity levels (as seen in the imaging experiments) in cortical association areas depending on the current task and previous experience. Rather than attributing the increase in necessity solely to these observed changes in activity, we highlight that in the simple task condition already, cortical areas contain a high amount of task information, ruling out the idea that insufficient local information would cause the small performance deficits from inhibition. Our results thus suggest that differential necessity across tasks and experience may still require changes at the readout level despite changes in local activity. We view our imaging results as an exciting first step towards a mechanistic understanding of how cognitive experience affects cortical necessity, but we stress that future work will need to test directly the relationship between cortical necessity and various specific features of the neural code.

Reviewer #2 (Public Review):

The authors use a combination of optogenetics and calcium imaging to assess the contribution of cortical areas (posterior parietal cortex, retrosplenial cortex, S1/V1) on a visual-place discrimination task. Headfixed mice were trained on a simple version of the task where they were required to turn left or right depending on the visual cue that was present (e.g. X = go left; Y = go right). In a more complex version of the task the configurations were either switched during training or the stimuli were only presented at the beginning of the trial (delay).

The authors found that inhibiting the posterior parietal cortex and retrosplenial cortex affected performance, particularly on the complex tasks. However, previous training on the complex tasks resulted in more pronounced impairments on the simple task than when behaviourally naïve animals were trained/tested on a simple task. This suggests that the more complex tasks recruit these cortical areas to a greater degree, potentially due to increased attention required during the tasks. When animals then perform the simple version of the task their previous experience of the complex tasks is transferred to the simple task resulting in a different pattern of impairments compared to that found in behaviorally naïve animals.

The calcium imaging data showed a similar pattern of findings to the optogenetic study. There was overall increased activity in the switching tasks compared to the simple tasks consistent with the greater task demands. There was also greater trial-type selectivity in the switching task compared to the simple task. This increased trial-type selectivity in the switching tasks was subsequently carried forward to the simple task so that activity patterns were different when animals performed the simple task after experiencing the complex task compared to when they were trained on the simple task alone

Strengths:

The use of optogenetics and calcium-imaging enables the authors to look at the requirement of these brain structures both in terms of necessity for the task when disrupted as well as their contribution when intact.

The use of the same experimental set up and stimuli can provide a nice comparison across tasks and trials.

The study nicely shows that the contribution of cortical regions varies with task demands and that longerterm changes in neuronal responses c can transfer across tasks.

The study highlights the importance of considering previous experience and exposure when understanding behavioural data and the contribution of different regions.

The authors include a number of important controls that help with the interpretation of the findings.

We thank the reviewer for pointing out these strengths in our work and for finding our main conclusions supported.

Weaknesses:

There are some experimental details that need to be clarified to help with understanding the paper in terms of behavior and the areas under investigation.

The use of the same stimuli throughout is beneficial as it allows direct comparisons with animals experiencing the same visual cues. However, it does limit the extent to which you can extrapolate the findings. It is perhaps unsurprising to find that learning about specific visual cues affects subsequent learning and use of those specific cues. What would be interesting to know is how much of what is being shown is cue specific learning or whether it reflects something more general, for example schema learning which could be generalised to other learning situations. If animals were then trained on a different discrimination with different stimuli would this previous training modify behavior and neural activity in that instance. This would perhaps be more reflective of the types of typical laboratory experiments where you may find an impairment on a more complex task and then go on to rule out more simple discrimination impairments. However, this would typically be done with slightly different stimuli so you don't introduce transfer effects.

We agree with the reviewer that investigating the effects of schema learning on cortical task involvement is an exciting future direction and have now explicitly mentioned this in the Discussion section. As the reviewer points out, however, our study was not designed to test this idea specifically. Because investigating schema learning would require developing and implementing an entirely new set of behavioral task variants, we feel this is beyond the scope of the current work. As to the question of how generalized the effects of cognitive experience are, our data in the run-to-target task suggest that if task settings are sufficiently distinct, cortical involvement can be similarly low regardless of complex task experience (now Figure 3—figure supplement 1). This finding is in line with recent work from (Pinto et al., 2019), where cortical involvement appears to change rapidly depending on major differences in task demands. However, work in MT has shown that previous motion discrimination training using dots can alter MT involvement in motion discrimination of gratings (Liu & Pack, 2017), highlighting that cortical involvement need not be tightly linked to the sensory cue identity.

It is not clear whether length of training has been taken into account for the calcium imaging study given the slow development of neural representations when animals acquire spatial tasks.

We apologize that the training duration and the temporal relationship between task acquisition and calcium imaging was not documented for the calcium imaging dataset. Please see our detailed reply below the ‘recommendations for the authors’ from Reviewer 2 below.

The authors are presenting the study in terms of decision-making, however, it is unclear from the data as presented whether the findings specifically relate to decision making. I'm not sure the authors are demonstrating differential effects at specific decision points.

We understand that the previous emphasis on decision-making may have created expectations that we demonstrate effects that are specific to the ‘decision-making’ aspect of a decision task. As we do not isolate the decision-making process specifically, we have substantially revised our wording around the tasks and removed the emphasis on decision-making, including in the title. Rather than decision-making, we now highlight the navigational aspect of the tasks employed.

While we removed the emphasis on the decision-making process in our tasks, we found the reviewer’s suggestion to measure ‘decision points’ a useful additional behavioral characterization across tasks. So, we quantified how soon a mouse’s ultimate choice can be decoded from its running pattern as it progresses through the maze towards the Y-intersection. We now show these results in Figure 1—figure supplement 1. Interestingly, we found that in the delay task, choice decoding accuracy was already very high during the cue period before the onset of the delay. Nevertheless, we had shown that overall task performance and performance with inhibition were lower in the delay task compared to the simple task. Also, in segment-specific inhibition experiments, we had found that inhibition during only the delay period or only the cue period decreased task performance substantially more than in the simple task, thus finding an interesting absence of differential inhibition effects around decision points. Overall, how early a mouse made its ultimate decision did not appear predictive of the inhibition-induced task decrements, which we also directly quantify in Figure 1—figure supplement 1.

Reviewer #1 (Public Review):

The role of the parietal (PPC), the retrospenial (RSP) and the the visual cortex (S1) was assessed in three tasks corresponding a simple visual discrimination task, a working-memory task and a two-armed bandit task all based on the same sensory-motor requirements within a virtual reality framework. A differential involvement of these areas was reported in these tasks based on the effect of optogenetic manipulations. Photoinhibition of PPC and RSP was more detrimental than photoinhibition of S1 and more drastic effects were observed in presumably more complex tasks (i.e. working-memory and bandit task). If mice were trained with these more complex tasks prior to training in the simple discrimination task, then the same manipulations produced large deficits suggesting that switching from one task to the other was more challenging, resulting in the involvement of possibly larger neural circuits, especially at the cortical level. Calcium imaging also supported this view with differential signaling in these cortical areas depending on the task considered and the order to which they were presented to the animals. Overall the study is interesting and the fact that all tasks were assessed relying on the same sensory-motor requirements is a plus, but the theoretical foundations of the study seems a bit loose, opening the way to alternate ways of interpreting the data than "training history".

1) Theoretical framework:<br /> The three tasks used by the authors should be better described at the theoretical level. While the simple task can indeed be considered a visual discrimination task, the other two tasks operationally correspond to a working-memory task (i.e. delay condition which is indeed typically assessed in a Y- or a T-maze in rodent) or a two-armed bandit task (i.e. the switching task), respectively. So these three tasks are qualitatively different, are therefore reliant on at least partially dissociable neural circuits and this should be clearly analyzed to explain the rationale of the focus on the three cortical regions of interest. For the working-memory task we do not know the duration of the delay but this really is critical information; per definition, performance in such a task is delay-dependent, this is not explored in the paper.

Also, the authors heavily rely on "decision-making" but I am genuinely wondering if this is at all needed to account for the behavior exhibited by mice in these tasks (it would be more accurate for the bandit task) as with the perspective developed by the authors, any task implies a "decision-making" component, so that alone is not very informative on the nature of the cognitive operations that mice must compute to solve the tasks. I think a more accurate terminology in line with the specific task considered should be employed to clarify this.

The "switching"/bandit task is particularly interesting. But because the authors only consider trials with highest accuracy, I think they are missing a critical component of this task which is the balance between exploiting current knowledge and the necessity to explore alternate options when the former strategy is no longer effective. So trials with poor performance are thus providing an essential feedback which is a major drive to support exploratory actions and a critical asset of the bandit task. There is an ample literature documenting how these tasks assess the exploration/exploitation trade-off.

2) Training history vs learning sets vs behavioral flexibility:<br /> The authors consider "training history" as the unique angle to interpret the data. Because the experimental setup is the same throughout all experiments, I am wondering if animals are just simply provided with a cognitive challenge assessing behavioral flexibility given that they must identify the new rule while restraining from responding using previously established strategies. According to this view, it may be expected for cortical lesions to be more detrimental because multiple cognitive processes are now at play.

It is also possible that animals form learning sets during successive learning episodes which may interfere with or facilitate subsequent learning. Little information is provided regarding learning dynamics in each task (e.g. trials to criterion depending on the number of tasks already presented) to have a clear view on that.

3) Calcium imaging data versus interventions:<br /> The value of the calcium imaging data is not entirely clear. Does this approach bring a new point to consider to interpret or conclude on behavioral data or is it to be considered convergent with the optogenetic interventions? Very specific portions of behavioral data are considered for these analyses (e.g. only highly successful trials for the switching/bandit task) and one may wonder if considering larger or different samples would bring similar insights. The whole take on noise correlation is difficult to apprehend because of the same possible interpretation issue, does this really reflect training history, or that a new rule now must be implemented or something else? I don't really get how this correlative approach can help to address this issue.

Reviewer #1 (Public Review): 

This study compares concentrations of immune mediators in vaginal samples of young women who report having had or report not having had vaginal sex. The study finds that the concentration of many immune markers is higher in samples of women who report having had sex than in samples of women who report not yet having had sex. While the results are interesting and suggestive, I do not believe this result necessarily indicates that vaginal sex increases levels of these immune mediators (a causal relationship) and that the evidence presented here is strong enough to draw this conclusion. 

This study presents many methodological strengths. The sample size is amply sufficient to achieve high statistical power for this research question. A particular strength of this analysis is the relatively large number of participants who provided paired before and after sex samples. These samples are particularly valuable because stronger conclusions can be drawn from them, as their comparison is less likely to be confounded by unmeasured confounders. The statistical methods are largely appropriate for the research question, with the use of random effects to account for the correlation in multiple measures per participant. 

The reason I would not draw causal conclusions from this analysis is that there is a high potential for unmeasured confounding of the association between sex and the concentration of immune mediators. The variables that were included in the multivariable analysis were for the most part not confounders, so the authors cannot claim that their results are free from potential confounding. Confounders are in general variables which are common causes of both the exposure of interest (vaginal sex) and the outcome (level of immune markers), and which are not on the causal pathway and are not a downstream effect of the outcome (inverse causality). The only variable included that is potential confounders is age. Most other variables (pregnancy, contraception, Nugent score, Chlamydia infection, and HSV-2 seropositivity) are either potential mediators of the effect of sex or downstream effects of the level of immune markers. It does not follow that adjustment for these variables would necessarily lead to an underestimation of the causal effect, as it is possible some of these variables have complex relationships with immune mediators, so it is difficult to predict how adjusting for these variables would influence results. Some of these variables are also potentially colliders, so adjustment for them may lead to bias (see an introduction to this topic in Holmberg MJ, Andersen LW. Collider Bias. JAMA. 2022;327(13):1282-1283. doi:10.1001/jama.2022.1820). There is no consideration of general social determinants of health that are more likely to be confounders because they potentially influence both sexual behavior and the immune system: socioeconomic status, ethnicity, education, employment, housing, food security, access to health care, etc. There is overwhelming evidence that young people who are sexually active tend to have very different socioeconomic characteristics than young people who are not sexually active. It is therefore difficult to assess whether the higher level of immune markers in women who are sexually active truly represents a causal effect of sex or simply reflect differences in the type of women who have sex. 

The paired analysis also suggests that the main analysis is likely to be confounded. The evidence from the paired analysis is much stronger than the evidence from the unpaired main analysis because the paired analysis inherently adjusts for many unmeasured confounders that lead to women having sex by a certain age; the differences in paired samples are likely much closer to the causal effect of sex than the differences from the unpaired samples. We see that, in the paired analysis, the differences in levels of immune mediators before and after sex is systematically much smaller and non-significant for most immune markers. This suggests to me that the main analysis is confounded and overestimates the effect of sex on immune markers. If there is a causal effect, it is likely to be much smaller than the one estimated in the main unpaired analysis. 

The authors argue that the smaller effects seen in the paired analysis might be due to an effect of time, where samples closer to the start of sex show smaller differences. However, I would need more evidence to be convinced of this. Notably, they use a spline analysis in Figure 4 to show the effect of time since vaginal sex. However, I would have liked to see the p-values for the time-dependent spline effect, in order to see whether the data supports that a difference in slopes before and after sex significantly improves the model. I suspect many of the splines are not significant and may not lend strong support to the hypothesis that time since sex has an effect. It is however difficult to assess this visually without a formal test. 

While the results from the systematic review and meta-analysis are interesting and show that at least two other studies have shown similar results, I wonder whether these other studies do not have similar issues of confounding. The other previous studies have even fewer paired samples, so are likely to have weaker evidence than the current study. 

In summary, I think this study has some important methodological strengths in terms of sampling and study design. However, I believe the interpretation of the results should be more tempered and cautious; while there are differences in levels of immune markers in women who have had and not had sex, there is not to my mind sufficient evidence that this difference is the result of a causal effect of initiation of vaginal sex, as there is likely to be some collider bias and unmeasured residual confounding in the analysis.

Author Response

Reviewer #2 (Public Review):

In this study, Radtke et al. use a model of helminth infection in IL-4-IRES-eGFP (4get) mice, in which transcription at the Il4 locus is reported by eGFP, in order to define the transcriptional signatures and clonal relatedness between Il4-licensed, CD4+ T cells in the mesenteric lymph nodes (mLN) and lungs. By infecting 4get mice with the hookworm Nippostrongylus brasiliensis, which is well described to induce a robust type 2 immune response, the authors isolated and sorted eGFP+CD4+ T cells from the mLN and lungs at 10day post infection and performed single cell RNA-seq analysis using the 10X Chromium platform. Transcriptional profiling of activated CD4+ T cells with scRNA-seq has been performed in a murine model of allergic asthma, including the lung and lung-draining lymph nodes, but this study involved unbiased capture of all activated CD4+ T cells (Tibbitt et al., Immunity, 2019). Radtke et al. have used a distinct model with Nippostrongylus brasiliensis and have focused on sorting Il4-licensed, CD4+ T cells, allowing for a greater number of captured CD4+ T cells with a "type 2" lymphocyte program for single cell analysis. Furthermore, this study sought to identify distinct and overlapping transcriptional signatures and clonal relatedness between Il4-licensed, CD4+ T cells in two "distant" tissues. In support of such an approach, there is growing evidence for tissue-specific and model-specific features of CD4+ T cell differentiation (Poholek, Immunohorizons, 2021; Hiltensperger et al., Nature Immunol, 2021; Kiner et al., Nature Immunol, 2021).

Upon dimension reduction, the authors found mLN- and lung-specific clusters, including two juxtaposed clusters that form a "bridge" between the mLN and lung compartments, suggesting immigrating and/or emigrating cells. Consistent with previous studies, the dominant lung cluster (L2) exhibited unique expression of Il5 and Il13, enhanced IL-33 and IL-2 signaling, and exhibited an effector/resident memory profile. The authors did find a small cluster in the mLN (ML4) with an effector/resident memory signature that also expressed CCR9, suggesting the potential for homing to the gut mucosa. Whether this population is specific to the mLN or would also be found in the lung-draining lymph nodes remains unclear. In the mLN, the authors also describe an iNKT cell cluster with CCR9 expression and a CD4+ T cell cluster with a myeloid gene signature, but the significance of these populations remains unclear.

The authors then use RNA velocity analysis to infer the developmental trajectory of Il4licensed, CD4+ T cells from the two tissue sites. Consistent with previous studies, the authors found that T cell proliferation was associated with fate decisions. Furthermore, among the two lung CD4+ T cell clusters, L1 represents highly differentiated, effector Th2 cells while L2, which is juxtaposed to the mLN clusters, represents a population likely entering the lung with the potential to differentiate into L1 cells.

Next, the authors perform TCR repertoire analysis. The authors identified a broad TCR repertoire with the majority of distinct TCRs being found in only one cell. Among the TCRs found in more than one cell, a substantial number of clones can be found in both tissue sites, which is consistent with the findings that individual CD4+ T cells clones can produce different types of effector cells (Tubo et al., Cell, 2013). The authors find significant overlap of clones between the mLN and lung. In addition, they also identify clones enriched in a particular site and suggest that this represents local expansion. However, an alternative possibility is that certain CD4+ T cell clones are expanded at a particular site because the specific TCR preferentially instructs a particular cell fate. For example, fate-mapping of individual naïve CD8+ T cells suggests that certain T cell clones exhibit a greatly heightened capacity to form tissue-resident memory T cells over other cell fates (Kok et al., J Exp Med, 2020). Lastly, the authors analyze CDR3 sequences, finding the most abundant CDR3 motif belonging to the invariant TCRa chain of iNKTs. Among conventional CD4+ T cells, the abundant CDR3 motifs were not restricted to an exact TCRa/TCRb combination beyond a slight preferential usage of the Trbv1 gene. While TCR repertoire analysis allows for defining clonal relatedness among Il4-licensed, CD4+ T cells, the importance and relevance of the above findings to the in vivo type 2 immune response remain unclear.

There are several limitations of the study:

(1) The authors use the term "Th2 cells" to describe all Il4-licensed, CD4+ T cells. While CD4+ T helper cell nomenclature has evolved, Th2 cells and Tfh2 cells are generally used to describe distinct subsets driven by unique transcriptional programs (Ruterbusch et al., Annu Rev Immunol, 2020). While previous data suggested that Tfh2 cells are precursors to effector Th2 cells, subsequent studies support a model in which Tfh2 and Th2 cells represent distinct developmental pathways and should be designated as distinct subsets (Ballesteros-Tato et al., Immunity, 2016; Tibbitt et al., Immunity, 2019). Consequently, the authors' broad use of "Th2 cells" and a description of "Th2 cell heterogeneity" includes CD4+ T cell subsets with distinct developmental pathways that includes canonical Th2 cells as well as Tfh2 and iNKT cells. The clarity of the manuscript would be improved by describing eGFP+CD4+ cells as Il4licensed, CD4+ T cells rather than Th2 cells.

We thank the reviewer for the helpful comment and state now that our IL-4 reporter positive population also includes cells that don’t meet the Th2 criteria in the introduction (lines 76-78).

(2) The authors used perfused lungs to isolate Il4-licensed, CD4+ T cells for scRNA-seq of "Th2 cells" in the lung tissue. However, previous studies indicate that leukocytes, including CD4+ T cells, in lung vasculature are not completely removed by perfusion, which confounds the interpretation of a tissue cell profile due to contaminating circulating cells (Galkina, E et al., J Clin Invest, 2005; Anderson, KG et al., Nat Protoc, 2014). This is particularly true in the lung and relevant as the authors found a lung cluster (L2) with a circulating signature and suggested that L2 may represent a recent immigrant "Th2 cells". Thus, it is unclear whether L2 cluster identifies immigrant Th2 cells or simply reflect the circulating Th2 cells trapped in the lung vasculature. The study would benefit of using the intravascular staining to discriminate cells within the lungs from those in the circulation (Anderson, KG et al., Nat Protoc, 2014) for the proper isolation of Il4-licensed lung CD4+ T cells to truly define immigrant "Th2 cells" within the lung parenchyma.

According to the reviewers suggestion we performed an intravascular staining to discriminate cells within the lungs from those in the circulation (new Figure 2—figure supplement 1). According to the vascularity staining method (with slightly increased time between i.v. and sacrifice compared to Anderson, KG et al., Nat Protoc, 2014 for higher probability of successful staining) the L2 lung cluster is a mixture of circulating cells and immigrating cells which we describe in the text (lines 210-213). The finding that the cells from the vasculature and the cells we classified as “migrating” seem to cluster together based on the similarity of their expression profiles on our UMAP further supports the classification of the L2 tissue fraction as “recent immigrants”. We thank the reviewer for this helpful comment which improved the quality of the manuscript.

(3) The authors describe T cell exchange/trafficking across organs. However, in general, interorgan trafficking refers to lymphocyte trafficking between distinct non-lymphoid tissues, rather than trafficking between lymph nodes and peripheral tissues (Huang et al., Science, 2018). Rather than inter-organ trafficking, the authors have described shared and distinct features of Il4-licensed, CD4+ T cells from a draining lymph node of one organ (gut) and a distant non-lymphoid organ (lung). The experimental approach used makes interpretation of some of the findings challenging. Specifically, canonical effector Th2 cell differentiation is well described to occur via two checkpoints, including the draining lymph node and the peripheral (non-lymphoid) tissue (Liang et al., Nature Immunol, 2011; Van Dyken et al., Nature Immunol, 2016; Tibbitt et al., Immunity, 2019). In the draining lymph node, Th2 cells acquire the capacity to express IL-4 alone, but do not complete effector Th2 cell differentiation until trafficking to the inflamed peripheral tissues and receiving additional inflammatory signals. Consequently, it is unclear whether the differences identified in the mesenteric lymph node and lungs simply reflect well-described differences between the two Th2 cell checkpoints or organ-specific differences (gut vs lung). Il4-licensed, CD4+ T cells from the intestinal mucosa and lung-draining lymph node would also be needed to truly define organ-specific differences during helminth infection.

According to the reviewers suggestion, we avoid the term “inter-organ trafficking” and replaced it by “at distant sites” in the title. As the reviewer points out we chose the setup of comparing a lymphoid and a non-lymphoid organ to acquire a broad picture of Th2 developmental stages in Nb infection. The limited overlap in clusters on the UMAP shows that expression profiles between MLN and lung strongly differ. However, this notion is not in conflict with cells of both organs being in a different developmental stage. We added information to highlight it in the manuscript (lines 99-101). Lung and MLN (rather than medLN and MLN) were selected to enable clonal relatedness/distribution analysis of T cells at distant sites. As part of the revision we additionally provide newly generated single cell sequencing data that compares medLN and MLN cells at day 10 after Nb infection and find that UMAP clusters are largely overlapping between medLN and MLN (new Figure 1—figure supplement 3). This suggests that there is no broad medLN/MLN site specific signature present that would force the medLN and MLN cells to cluster apart. Addition of the newly generated medLN/MLN data on the lung/MLN UMAP based on shared anchors (Stuart et al. Cell. 2019) also leads to a clear separation between all LN and lung cells supporting that cells don’t cluster due to a site-specific respiratory tract vs intestinal tract signature but likely based on developmental stages (new Fig. 1C,D). An exception are defined effector clusters that show signs of a site-specific signature (L1 expresses Ccr8, MLN4 and MLN6 express Ccr9, differences are also suggested by clustering described in lines 247-252). A similar phenotype to the one observed on the transcriptional level is observed when we cluster medLN/MLN and lung cells based on scRNAseq suggested surface marker expression after flow cytometric analysis, extending analysis to medLN on protein level (new Fig. 3). It would have also been interesting to include lamina propria T cells as the reviewer suggested but we were not able to extract high quality cells at day 10 after Nb infection which is a common limitation in the Nb model.

(4) The study includes a single time point (day 10) whereas Tibbitt et al. performed scRNAseq in the lung and lung-draining lymph node at multiple time points during type 2 immunity (Tibbitt et al., Immunity, 2019). As a result, it remains unclear how similarities or differences between the mesenteric lymph node and lung response would change over the duration of helminth infection, especially given the helminth life cycle involves multiple infection stages.

As part of the revision we screened for surface marker expression in the single cell sequencing dataset on transcript level and stained these on protein level (new Fig. 3 and Figure 3—figure supplement 1). This allows to follow the populations defined by scRNAseq longitudinally (d0, d6, d8, d10) by flow cytometry during Nb infection. We compared medLN, MLN and lung. The dynamic of the response in the medLN and the MLN seems similar with a small delay in the MLN compared to medLN.

Nb with its relatively well defined migratory path through the body provides a relevant complex model antigen naturally present in the respiratory tract and the intestine during infection. However, analysis of complexity and relevance does often invoke limitations. While stage 4 larvae are found in lung and gut and certainly provide a shared antigen basis between both sites (migration stage from lung to intestine; Camberis et al. Curr Protoc Immunol. 2003), we also think that there is a reasonable number of antigens shared between different larval stages and antigen (either actively secreted or from dying larvae) that are systemically distributed. However, there are probably immunogenic differences between larval stages but to analyze these is beyond the scope of the manuscript.

While i.e. Tibbitt et al. nicely define cell clusters with a limited number of cells they don’t include any TCR analysis and clonal information. Not much was known about the expansion of T cells in the different clusters in one organ and between organs and we provide relevant data in this regard. Furthermore, HDM as an allergy model might invoke different Th2 differentiation pathways as. i.e. Tfh13 cells are found in allergic settings but not in worm models (Gowthaman U, Science. 2019). With our approach on single cell level we were able to show effective distribution of a number of T cell clones in a highly heterogeneous immune response and describe and functionally validate successfully expanded clones / expanded TCR chains later on (i.e. new Fig. 6). This kind of analysis has not been performed for a worm model before.

(5) The study analyzed one scRNA-seq experiment that included two mice without validation via flow cytometry or other method to infer a role of a particular finding to the type 2 immune response in vivo.

As noted above, we screened for surface marker expression in the single cell sequencing dataset on transcript level and measured these on protein level by flow cytometry as the reviewer suggested. This allows to follow the populations defined by scRNAseq longitudinally (d0, d6, d8, d10) during Nb infection (new Fig. 3). Furthermore, we added a newly generated set of scRNAseq data which confirms and extends findings made in the initial sequencing experiment (Fig. 1C,D and Figure 1—figure supplement 3). We also included validation experiments based on the performed TCR analysis and retrovirally expressed three TCRs from our study and confirm Nb specific expansion for one of them in vivo (new Fig. 6 and Figure 6—figure supplement 1).

I'm not sure I agree here as one can take other annotations from various texts throughout a course and link them together to create new ideas and knowledge within the margins themselves. Of course, at some point the ideas need to escape the margins to potentially take shape with a class wiki, new essays, papers, journal articles or longer pieces.

Use of social annotation across several years of a program this way may help to super-charge students' experiences.

I agree with Minha's assessment of the project. Her research question is phrased perfectly for the overall topic of these combined videos. I can't stop, and I think I won't stop thinking about what it truly means for me to age. Each voice represents a background that provides a resource for both the voice owner and the audience to answer this question. Aging for me means being more cautious with words and actions. I consciously do this because I see everyone around me go through this process and talk about it. Aging for me means looking at my grandparents and and thinking what I will do and what I will look like when I reach their age. I thought about this question a few times when I was much younger, then there was a long period of me not worrying about it at all, and in college, the question came back to me at higher rate of frequencies. I often ask myself if my future kids/grandkids (if I ever have them) would care about me and life after death was something that seems to be in my head for the longest time. Aging for me means carrying new responsibilities. I know that there are things that was acceptable when I was one year younger and became inapplicable for me the year after, and vice versa. "What it means to age?" is repeatedly asked throughout the video, motivating us to give it a try and craft our own response. This research question has well summarized for the bigger and better understanding of the purpose that these 'storytellers' and collaborators embed in this project. Same with taylortots, I may revisit this project from time to time with newer perspectives about the definition of growing old. Thank you for the insightful post!

Author Response

Reviewer #1 (Public Review):

In this study, the authors set out to clarify the relationship between brain oscillations and different levels of speech (syllables, words, phrases) using MEG. They presented word lists and sentences and used task instructions to attempt to focus listeners' attention on different levels of linguistic analysis (syllables, words, phrases).

1) I came away with mixed feelings about the task design: following each stimulus (sentence or word list), participants were asked to (a) press a button (i.e. nothing related to what they heard, (b) indicate which of two syllables was heard, (c) indicate which of two words was heard, (d) indicate which pair of words was present in the correct order. This task is the critical manipulation in the study, as it is intended to encourage (or in the authors' words, "require") participants to focus on different timescales of speech (syllable, word, and phrase, respectively). I very much like the idea of keeping the physical stimuli unchanged, and manipulating attention through task demands - an elegant and effective approach. At the same time, I have reservations about the degree to which these task instructions altered attention during listening. My intuition is that, if I were a participant, I would just listen attentively, and then answer the question about the specific level. For example, I don't know that knowing I would be doing a "word pair" task, I would be attending at a slower rate than a "word" task, as in both cases I would be motivated to understand all of the words in the sentence. I fully acknowledge my introspection (n=1) may be flawed here, but nevertheless, any additional support validating the effect of these instructions would help the interpretation of the MEG results.

The reviewer points out that to do any task on sentences (such as a word task and a syllable task) participants’ strategy could be to understand the full meaning of the sentence and infer the lower level properties based on the understanding of the full sentence. We fully share this introspection, which would suggest that extracting sentence meaning is partly automatic (or at least a default mode of processing) and independent of the behavioral relevance. While the reviewer sees this as a downside of the design, this is part of what our study tried to disentangle (automatic versus task-dependent processing at lower frequency time-scales). If, as the reviewer points out, all processing of sentences would be automatic we should not find any effect of task (as the task should not affect the tracking response at all). We found that overall the tracking response is robust to task-induced manipulation of attention – the main effect that MI to phrases is higher for sentences than for word lists is robust across passive and task conditions. But that is not the whole story on the source level, where we do find some task effects, which indicates that task instructions do matter. This means that participants changed their strategy depending on the instructions, but that overall, tracking of linguistic structures such as phrases is automatic. We show that for the IFG MI phrasal time scales are tracked stronger during the phrase task versus the other tasks. This is also reflected in stronger STG-IFG connectivity during the phrasal versus passive task. These results speak against the interpretation of the reviewer that “task instructions“ do not “ altered attention during listening”. While there are these subtle task differences, especially in IFG, overall our findings do speak for an automatic tracking of phrasal rate structure in sentences independent of task. We therefore concluded that “automatic understanding of linguistic information, and all the processing that this entails, cannot be countered to substantially change the consequences for neural readout, even when explicitly instructing participants to pay attention to particular time-scales” (line 548-549).

The analysis steps generally seem sensible and well-suited to answering the main claims of the study. Controlling for power differences between conditions through matching was a nice feature.

2) I had a concern about accuracy differences (as seen in Figure 1) across stimulus materials and tasks. In particular, for the phrase task, participants were more accurate for sentence stimuli than word list stimuli. I think this makes a lot of sense, as a coherent sentence will be easier to remember in order than a list of words. But, I did not see accuracy taken into account in any of the analyses. These behavioral differences raise the possibility that the MEG results related to the sentence > word list contrast in phrases (which seems one of the most interesting findings in IFG) simply reflect differences in accuracy.

With the caveat of the concern regarding accuracy differences, the research goals were clear and the conclusions were generally supported by the analyses.

Thank you for pointing this out. We have now taken accuracy into account in our analysis. It did not change any of our main findings or conclusions, and strengthened the argument that tracking of phrases in sentences vs. word lists is stronger. The influence of task difficulty is a relevant point to investigate (also see point 1 of reviewer 2 and point 4 of reviewer 3). To do so we added accuracy (per participant per condition) as a factor in the mixed model (as well as all interactions with task and condition) for the MI, power, and connectivity analyses at the phrasal rate/delta band. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see below figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition (as the reviewer also indicated in point 1).

After correcting for accuracy there was also a significant task condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracy task condition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant condition accuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant task condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

Reviewer #2 (Public Review):

In a MEG study, the authors investigate as their main question whether neural tracking at the phrasal time scale reflects linguistic structure building (testing different conditions: sentences vs. word-lists) or an attentional focus on the phrasal time scale (testing different tasks, passive listening, syllable task, word task, word combination/phrasal scale task). They perform the following analyses at brain areas (ROIs: STG, IFG, MTG) of the language network: (1) Mutual information (MI) between the acoustic envelope and the delta band neuronal signals is analyzed. (2) Power in the delta band is analyzed. (3) Connectivity is analyzed using debiased WPLI. For all analyses, linear mixed-models are separately conducted for each ROI. The main finding is that the sentence compared to the word-list condition is more strongly tracked at the phrasal scale (MI). In STG the effect was task-independent; in MTG the effect only occurred for active tasks; and in IFG additionally, the word-combining/phrasal scale task resulted in higher tracking compared to all other tasks. The authors conclude that phrasal scale neural tracking reflects linguistic processing which takes place automatically, while task-related attention contributes additionally at IFG (interpreted as combinatorial hub involved in language and non-language processing). The findings are stable when power differences are controlled. The connectivity analysis showed increased connectivity in the delta band (phrasal time scale) between IFG-STG in the phrasal-scale compared to the passive task (adding to the IFG MI findings). (Additionally, they separately analyze neural tracking at the syllabic and word time scale, which however is not in the main focus).

Major strength/weaknesses of the methods and results:

1) A major strength of the results is that part of them replicate the authors' earlier findings (i.e. higher tracking at the phrasal time scale for sentences compared to word-lists; Kaufeld et al., 2020), while they complement this earlier work by showing that the effects are due to linguistic processing and not to an attentional focus on the phrasal time scale due to the task (at least in STG and MTG; while the task plays a role for the IFG tracking). Another strength is that a power control analysis is applied, which allows excluding spurious results due to condition differences in power. A weakness of the method is that analyses were applied separately per ROI, and combined across correct/incorrect trials (if I understood correctly), no trial-based analysis was conducted (which is related to how MI is computed). Furthermore, several methodological details could be clarified in the manuscript.

The authors achieved their aims by providing evidence that neuronal tracking at the phrasal time scale in STG and MTG depends on the presence of linguistic information at this scale rather than indicating an attentional focus on this time scale due to a specific task. Their results support the conclusion. Results would be strengthened by showing that these effects are not impacted by different amounts of correct/incorrect trials across conditions (if I understood that correctly).

We thank the reviewer for her comments. It is correct that we collapsed across the correct and incorrect trials. This had various reasons (also see point 2 and 9 of reviewer 1 and point 4 of reviewer 3). First, our tasks function solely to direct participants’ attention to the various linguistic representations (syllables, words, phrases) and the timescales that they occur on. The three tasks are in a sense more control tasks to study the tracking response, and manipulate attention as tracking during spoken language comprehension occurs, rather than a case where the neural response to the tasks is itself to be studied. For example, in a typical working memory paradigm, it is only during correct trials that the relevant cognitive process occurs. In contrast, in our paradigm, it is likely that that spoken stimuli are heard and processing, in other words, sentence comprehension and word list perception occur, even during incorrect trials in the syllable condition. As such, we do not expect MI tracking responses to explain the behavioral data. However, we agree it is crucially important to show that MI differences are not a function of task performance differences.

Second, there are clear differences in difficulty level of the trials within conditions. For example, if the target question was related to the last part of the audio fragment, the task was much easier than when it was at the beginning of the audio fragment. In the syllable task, if syllables also were (by chance) a part-word, the trial was also much easier. If we were to split up in correct and incorrect we would not really infer solely processes due to accurately processing the speech fragments, but also confounded the analysis by the individual difficulty level of the trials.

To acknowledge this, we added this limitation to the methods. The methods now reads: “Note that different trials within a task were not matched for task difficulty. For example, in the syllable task syllables that make a word are much easier to recognize than syllables that do not make a word. Additionally, trials pertaining to the beginning of the sentence are more difficult than ones related to the end of the sentence due to recency effects.”.

To still investigate if overall accuracy influenced the results we did add accuracy (across participants) to the mixed models. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see on the right attached figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure below; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

After correcting for accuracy there was also a significant task*condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracytaskcondition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition*accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant conditionaccuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant taskcondition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

The findings are an important contribution to the ongoing debate in the field whether neuronal tracking at the phrasal time scale indicates linguistic structure processing or more general processes (e.g. chunking).

Reviewer #3 (Public Review):

This manuscript presents a MEG study aiming to investigate whether neural tracking of phrasal timescales depends on automatic language processing or specific tasks related to temporal attention. The authors collected MEG data of 20 participants as they listened to naturally spoken sentences or word lists during four different tasks (passive listening vs. syllable task vs. word tasks vs. phrase task). Based on mutual information and Connectivity analysis, the authors found that (1) neural tracking at the phrasal band (0.8-1.1 Hz) was significantly stronger for the sentence condition compared to the word list condition across the classical language network, i.e., STG, MTG, and IFG; (2) neural tracking at the phrasal band was (at least tend significantly) stronger for phrase task than other tasks in the IFG; (3) the IFG-STG connectivity was increased in the delta-band for the phrase task. Ultimately, the authors concluded that neural tracking of phrasal timescales relied on both automatic language processing and specific tasks.

Overall, this study is trying to tackle an interesting question related to the contributing factors for neural tracking of linguistic structures. The study procedure and analyses are well executed, and the conclusions of this paper are mostly well supported by data. However, I do have several major concerns.

1. The title of the manuscript uses the description "tracking of hierarchical linguistic structure". In general, hierarchical linguistic structures involve multiple linguistic units with different timescales, such as syllables, words, phrases, and sentences. In this study, however, the main analysis only focused on the phrasal band (0.8-1.1 Hz). It seemed that there was no significant stimulus- or task-effect on the word band or syllabic band (supplementary figures). Therefore, it is highly recommended that the authors modify the related descriptions, or explain why neural tracking of phrases can represent neural tracking of hierarchical linguistic structures in the current study.

We thank the reviewer for this comment. We meant to refer to the task manipulation directing attention to different levels of representation across the linguistic hierarchy. We have changed the title to “Neural tracking of phrases during spoken language comprehension is automatic and task-dependent.” We hope this resolves any inadvertent confusion we created. Furthermore, throughout the manuscript we ensure to talk about effect occurring for phrasal tracking at low frequency bands at not across any hierarchical linguistic structure. We agree that our findings cannot speak for any task-dependent effects along the hierarchy, only that at the phrasal level there is a difference between sentences and word lists.

1. In Methods, the authors employed MI analyses on three frequency bands: 0.8-1.1 Hz for the phrasal band, 1.9-2.8 Hz for the word band, and 3.5-5.0 Hz for the syllabic band (line 191-192). As the timescales of linguistic units are various and overlapped in natural speech, I wonder how the authors define the boundaries of these frequency bands, and whether these bands are proper for the naturally spoken stimuli in the current study. These important details should be clarified.

The frequency bands of the MI analysis were based on the stimuli, or in other words, are data driven. They reflect the syllabic, word, and phrasal rates in our stimulus set (calculated in Kaufeld et al., 2020). They were calculated by annotating the sentences by syllables, words, and phrasal and converting the rate of the linguistic units to frequency ranges. The information has been added to the manuscript. We acknowledge that unlike our stimulus set in natural speech the boundaries of these bands can overlap and now also state this (“While in our stimulus set the boundaries of the linguistic levels did not overlap, in natural speech the brain has an even more difficult task as there is no one-to-one match between band and linguistic unit [26]”, line number 211-213).

1. What is missing in the manuscript are the explanations of the correlation between behavioral performance and neural tracking. In Results, the behavioral performance shows significant differences across the active tasks (Figure 1), but the MI differences across the tasks are relatively weak in IFG (Figure 3). In addition, the behavioral performance only shows significant differences between the sentence and word list conditions during the phrasal task, but the MI differences between the conditions are significant in MTG during the syllabic, word, and phrasal tasks. Explanations for these inconsistent results are expected.

We answer this point together with point 4 below where we analyze the behavioral performance and the MEG responses.

1. Since the behavioral performance of these active tasks is likely related to the temporal attention to relevant timescales of different linguistic units, I wonder whether there exist underlying neural correlates of behavioral performance (e.g., significant correlation between performance and mutual information). If so, it may be interesting and bring a new bright spot for the current study.

The influence of task difficulty is a relevant point to investigate (also see point 1 of reviewer 2 and point 4 of reviewer 3). To do so we added accuracy (per participant per condition) as a factor in the mixed model (as well as all interactions with task and condition) for the MI, power, and connectivity analyses at the phrasal rate/delta band. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see the below figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure attached; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition.

After correcting for accuracy there was also a significant task*condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

While the findings can explain some behavioral effects, we agree with the reviewer that the behavioral results and the MI results don’t align. We note that our use of tasks to guide attention to different timescales and linguistic representations differs from the use of, for example, a working memory task where only the correct trials contain the relevant cognitive process. In working memory type paradigms, the MEG data should indeed explain the behavioral response. Our study was designed to test for effects of task demands on the neural tracking response to speech and language. As we are only using the tasks to control attention, we do not attempt to explain behavior through the MEG data or differences in MI.

Thus, the phrasal tracking cannot explain all of the behavioral results (point 3). It is at this point unclear what could have caused this effect, but it quite likely that neural sources outside the speech and language ROIs we selected are in play. We discuss this now.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracytaskcondition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition*accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant conditionaccuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant taskcondition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

Author Response

Reviewer #1 (Public Review):

The authors examined the relationships between humans' heartbeats and their ability to perceive objects using touch.

Strengths: This study is a large and sophisticated one, with great attention to detail and systematic analysis of the resulting data. The hypotheses are clear and the study was carried out well. The presentation of the data visually is very informative. With such a large and high-quality set of data, the conclusions that we can draw should be clear and strong.

Weaknesses: The main drawbacks for me were first, exactly how the data were analysed, and second that there seem to be too many results reported to get an overall view of what the study has found.

First, there are always a number of choices that researchers can make when analysing their data. Too many choices in fact. So we always need to see a consistent, principled, and transparent account of how those choices were made and what the effects on the data were. At present, I think this needs to be improved, partly in the justification of the analyses that were done; partly by re-doing some analyses and the presentation of results.

Second, I admit to being a little lost when trying to understand all of the analyses - why there were done, what choices were made, and what the findings were. In some cases, it felt a little bit like the analyses were decided on only quite late - after exploring the data. One clear way to address this would be to divide the main results into two kinds: confirmatory (those that the authors expected to do before the study was run), and exploratory (those that the authors decided to do only after seeing the data). This would be both good practice and would help to focus the reader on what are the most critical findings.

Achievements: I think the presentation of results needs to be strengthened before I can decide whether the aims are achieved.

Impact: This will also depend on the revision of the results.

We thank the Reviewer for these comments. In the original manuscript we thought we have been clear as to those analyses that were planned and those that were exploratory. The planned analyses are in keeping with the previous studies in the literature on which this study was based (Al et al. 2020; Al et al. 2021; Grund et al. 2021). The only exploratory analysis was the inclusion of touch variance as a co-variate. We had not expected that participants would differ so much in how long they held their touch.

Reviewer #2 (Public Review):

In this article, the authors set out to discover whether the cardiac cycle influences active tactile discrimination, to better understand the putative relationship between interoception rhythms and exteroceptive perception. While numerous articles have looked at these relationships in the passive domain, here the authors designed an innovative active sensing task to better understand the interaction of sensorimotor processes with the cardiac rhythm.

The authors report a series of consecutive analyses. In the first, they find that while active discriminative touch is not modulated by the cardiac cycle, non-discriminative touch is such that the start, median duration, and end time of touches are shifted forward along the cardiac cycle towards diastole. Next, the authors examined the proportion of total start and end touches within systole versus diastole and found that across both discrimination and control conditions, touch was roughly 10-25% more likely to terminate during diastole. Further, examining the median holding time, the authors found that touches initiated during systole were lengthened in duration, consistent with a perceptual inhibition by this phase. This last effect appeared to be greatest for the highest stimulus difficulty levels, further supporting the notion that some cardiac inhibition of sensory processing may be at stake. Finally, when examining physiological responses, the authors found that cardiac inter-beat intervals were lengthened during active touch, consistent with the hypothesis that the brain may exploit strategic cardiac deceleration to minimize inhibitory effects.

Overall, the key effects of the manuscript are fascinating and robust. A major strength of the approach here is the task itself, which utilizes a well-controlled stimulus with multiple levels of task difficulty, as well as an elegant positive control condition. This enabled the authors to look rigorously at difficulty and stimulus condition interactions with the cardiac phase. This clearly pays off in the analyses, as the authors are able to construct a more informative story about how precisely cardiac timing events modulate perception.

Statistically speaking, I found the overall approach to be rigorous and sound. The study is well powered for a psychophysical investigation of this nature, and the interpretation of results is based on robust effects in the presence of a strong positive control.

We thank the reviewer for these positive comments on the original version of this paper.

Reviewer #3 (Public Review):

The manuscript presents a carefully designed and well-controlled study on active tactile perception and its relationship to internal bodily rhythms - the cardiac cycle. This work builds on previous studies which also showed that active perception/voluntary actions occur in certain phases of the cardiac cycle, but the previous research failed to show/was not designed to show the significance of these synchronizations for perception or behaviour. To my knowledge, this is the first report that seems to experimentally show that active perception in the cardiac diastole leads to behavioural advantages - better tactile discrimination.

The manuscript itself is very clearly written, the introduction is concise but sufficient, while the results section is very well organised and I especially like how the authors guide the reader through the analysis and additional steps taken to understand the findings even better.

Yet, despite careful study design, effective visualisations, and elegantly constructed story, there are some analytical choices that, in my opinion, are not sufficiently justified or explained (e.g., selecting a diastolic window equal in length to the duration of systole, instead of using the whole duration of diastole). Such analytical decisions could have (at least some) effects on the obtained results and thus conclusions drawn.

We thank the Reviewer for these comments. The analyses referred to here were planned and specifically the choice of the windows for defining systole and diastole were identical to the studies in the literature on which this study was based (Al et al. 2020; Al et al. 2021).

Reviewer #2 (Public Review):

Context:<br /> The authors propose a new analysis of an already well-studied conceptual model of adaptation to a new environment. Individual genotypes are characterized by some (breeding value for) phenotype under gaussian stabilizing selection (meaning that fitness is a gaussian function of phenotype, centered around some optimum value). The scenario assumed is that an isolated population of fixed size is initially at equilibrium (between mutation, selection and genetic drift). This population is diploid and sexual with many unlinked loci acting additively on phenotype (across loci and between homologous chromosomes). This view simplifies the analysis but is also not inconsistent with various empirical analysis of locus specific effects on quantitative traits (the empirical support is discussed and reviewed in both introduction and discussion).

Then a change in the environment induces a shift in the optimum without affecting any other parameter (strength of selection, population size, mutation effects, existing phenotypes), see figure 1. We wish to know how the population responds to this change, both in terms of phenotype distributions, and the underlying genetic basis (how alleles of various effects change in frequency and contribute to the phenotypic response).

This process has been at the core of the modelling of adaptation for more than a century, as it is maybe the most natural conceptual framework to describe adaptation to a new environment (a "niche shift" so to speak). It is relevant to both the study of demographic/ecological and phenotypic responses to changing conditions, and to the genomics of the changes associated with this process.<br /> However, in spite of this long history (reviewed in introduction in broad lines), we do not have an exact mathematical description of this process. The reason is that the problem is in fact very complex: the genome is a sea of various genes, each bearing various alleles (depending on the individual), that further interact mutually by selection (even though loci are additive on phenotype), because fitness is not a linear function of phenotype. The simple population genetics with two alleles and one locus seem far away...

I think it is fair to say that the main route to handle this problem, in predominantly sexual species, has been through the approximations of quantitative genetics. There, each locus is assumed of small effect and linkage disequilibrium between them is neglected. This has led to empirically testable, and often quite accurate, predictions on the response to selection in terms of mean phenotypic change. Yet, even under this broad approximation strategy, there are various ways to derive predictions, each neglecting one force or another (genetic drift most of the time), or looking at the process over short or longer timescales.

Aim and achievements:<br /> The authors include their work within this broad framework, but set to derive new approximations that are intended to cover several of the existing approach as subcases, and especially to handle genetic drift effects in finite populations (large ones), and short vs. longer timescales. I believe they succeed quite well in doing so: they provide clear approximation methods (in appendix mostly) and substantial simulations to show their accuracy. The derivations are fairly technical but most of the time they manage to give an intuition of where they come from and illustrate this intuition via figures in the main text. They produce a prediction of two main observable dynamics: that of the (breeding value for) phenotype itself (its mean over time, variance, third moment), and that of the genetic contribution of various loci and alleles along the genome (depending on the allelic effect on phenotype). They also describe two timescales where the dynamics are fairly different, a short timescale where the mean phenotype is shifting (quite rapidly over tens/hundreds generations) towards the new optimum, and a longer timescale where the higher moments and mostly the genetic basis changes while the mean phenotype merely wanders in a narrow vicinity of the new optimum. The connection between the two timescales is important as it is the slight differences in allele fates during the first one that result in differences in long term behavior in the longer one (illustrated in figure 3).

The main achievement on the phenotypic response is mostly to reobtain previous approximations under somewhat different or broader assumptions. This is not useless as it may explain why these known predictions (the "Lande model") are surprisingly robust to deviations from the required conditions (e.g. figure 2). However, I think that some extra exploration of the parameter space (away from the required conditions) would allow to really see when the Lande model does fail on mean phenotype dynamics over short timescales, as anticipated. The question of whether this range is relevant remaining open to empirical measurement.<br /> Therefore, the main contribution of this ms is not on phenotypic responses but on the underlying genetic basis, and what we may expect to observe when measuring QTL's or GWAS between two populations separated by an environmental shift in the past: are there many loci contributing limited difference, or fewer loci contributing most of it. In that respect, eqs 20-21 and 25-26-27, and figures 5 and 6 display the main findings and thei check by simulations. These findings, although stemming from quite elaborate derivations, yield a fairly simple and yet accurate outcome, at least in the parameter range studied. Various other parameter sets are also checked against simulations in the appendix, and the simulation code is made available for any further check (as exploring all the possible parameters is a fairly taunting task, for an article of its own probably).

Limits:<br /> I believe the main limit of this work is fairly explained in the discussion: to achieve mathematical tractability (a full numerical treatment being inherently impossible given the many parameters), many simplifying assumptions must be made (simple fitness landscape, simple effect of the environmental change, simple demography etc.). This means that it is possible that empirical observations will differ from the predictions for various reasons. However, quantitative genetics have already proven reasonably robust and accurate in predicting observed phenotypic dynamics, using comparable approximations so it is not madness to hope that the same will happen concerning the genetic basis of adaptation. Also, I would suspect that the methods proposed in appendix will most likely extend fairly easily to some deviations from the model's assumption: change in phenotypic variance with the new environment (a form of plasticity), or in width of the fitness function, or change the population size, without too much effect on the main conclusions. Still, some other limits may not be overcome as easily (e.g. pleiotropy among multiple traits, or non-stationary optimum), but it seems (a priori) that part of the approach could still be adapted for these situations. The main "wall-hitting" limit of the paper is inherent in the very basis of the approach, namely assuming mild changes occurring in weakly linked polymorphic and numerous loci as opposed to strong changes occurring on more tightly linked and fewer loci. These limits are all fairly described in discussion.

Overall, this paper is not an easy read, but not by lack of clarity, rather because the problem at hand is complex, and there is a lot of material to describe. Each part flows quite well in my opinion, but there are many parts to read.

Potential impact:<br /> I believe that because it yields relatively simple analytic outcomes (at least the predictions in main text), the paper could be useful to data analysis, mostly in the field of genomics of adaptation where it may provide testable predictions for GWAS and QTL data. It could also be used to infer genetic distributions (v(a),f(a)) from observed QTL or GWAS data, if the model is deemed valid.

In the field of theoretical population genetics, it may also provide a methodology to capture sexual adaptation dynamics in other contexts by mixing various approximation methods: connecting distinct timescales, connecting deterministic approximations for phenotype and diffusion approximations for allele frequencies. This may not be the first time of course (see e.g. "stochastic house of cards" and their extensions), but it is here used in the context of adaption dynamics rather than equilibria, for the first time I think.

Predict With The Objetive of Validating And Changing Your Mental Model, trying to be as comprehensive as possible. Try to Think About the powers that rules and how their oppositions can react to their actions.

Do not make your prediction long in extension. The further you try to get the chances that you would make a critical error in your prediction grows exponentially

Some propms always have reveal valuable and memorable information about the period.

Changing Your Mental Model, Not To Get IT

Author Response

Reviewer #2 (Public Review):

This is an interesting and well-performed study that adds to the literature base. The authors investigated the role of a discrete brain pathway in binge drinking of alcohol. They adopted a multidisciplinary approach that overall suggested that alcohol-induced changes at synapses of anterior insula (AI) cortex inputs to the dorsolateral striatum (DLS) maintain binge drinking. Further, they suggest this may be a biomarker for the development of alcohol use disorder (AUD).

Strengths:

1. Extends previous studies and builds further evidence for AI→DLS involvement in aberrant alcohol intake.

2. Adopts elegant approaches to isolate the defined connections. This included in vivo optogenetic stimulations (both open and closed loop), recording of defined synapses in slice preparations, applying in vivo optogenetic stimulation parameters to isolated brain slices

3. Well-controlled for the most part, although at times the authors assert "specific" effects without unequivocal proof. For example, the insula also projects to the ventral striatum and this pathway has been implicated in regulation of alcohol intake in rodent models (Jaramillo et al., 2018), and is activated in heavy drinking humans during high threat related alcohol cue presentation (Grodin et al., 2018).

4. Measures the microstructure of drinking behavior in subjects.

5. Employed an artificial neural network and machine learning to interrogate data. After training the network it could predict both the fluid consumed (water vs alcohol) and the virus type based on drinking microstructure data.

6. Applied a series of behavioral tests to confirm that stimulating the defined pathway was not in and of itself reinforcing, anxiogenic or altered locomotion.

Weaknesses:

1. Only used male mice, in humans binge drinking in females is a major problem and rates of AUD between males and females have been converging in recent times (Grant et al., 2015).

We took age-matched female mice that were injected with AAV-ChR2 into AIC and had them undergo the same 3 weeks of Drinking in the Dark to replicate the male data displayed in Figure 1 with an experimental focus on AIC inputs. We then performed whole cell patch clamp electrophysiology in DLS brain slices from these female mice. We measured optically evoked input-output responses (oEPSCs), AMPA/NMDA current ratios (oNMDA/oAMPA), and paired pulse ratios (oPPR). These data are presented in supplemental figure 4. In contrast to males, we did not observe any effect of alcohol consumption on AIC inputs into the DLS of female mice compared to males. We also combined both male and female datasets to statistically determine if we had sex differences for these specific measures by the existence of a main effect and/or a sex x fluid interaction. We report these statistics in text from lines 180 to 195, where we note that we did not have a sex x fluid effect for oEPSCs but did note that we had a sex x fluid effect for our oNMDA/oAMPA synaptic plasticity measure. This finding further justifies the behavioral data and circuit manipulations being conducted in solely male mice.

While this is a fascinating sex difference and important data for the field, this manuscript is not specifically about exploring sex differences per se. We believe we have done our due diligence and correctly reported the existence of sex differences, or the possibility of sex differences, but the electrophysiological findings that we later modulate in vivo are only present in males. We point out that future work is needed to determine the contribution of circuit-specific changes in females at these synapses. Ultimately it will take much more work to fully elucidate sex difference circuit-specific mechanisms that we feel are far beyond the scope of this manuscript.

1. At times over-interpreted, especially with regards to specificity.

We are not exactly sure what the reviewer is referring to with “regards to specificity,” but we have done our best to address what we think they are asking and hope that we have adequately addressed this critique. We added sentences (lines 173-178) regarding alcohol-induced plasticity at other inputs to DLS that were not tested and (lines 442 - 446) how we are not sure whether these synapses control consumption of other non-alcohol substances (but point out our prior sucrose drinking data from Muñoz et al., Nat. Comm. 2018).

1. Lacks a mechanism, although the authors do acknowledge this.

This is just a first step towards discovering a mechanism. We previously identified an unusually alcohol-sensitive synapse and are now elucidating its behavioral role and some associated plasticity at that synapse that may be part of a mechanism. With our new single session alcohol data to compare our 3 week drinking data to, we are closer to beginning the process of discovering a mechanism. Additional work that is beyond the scope of this manuscript is needed.

1. I would like some more discussion about the potential for this to be a biomarker in humans.

We have removed language in the body of the manuscript and expanded on the implications of our findings at the end of our results and discussion from lines 514 to 548.

Reviewer #3 (Public Review):

Haggerty et al. assess how the projection from the agranular insular cortex to the dorsolateral striatum contributes to binge drinking in mice. The authors use whole-cell patch-clamp electrophysiology to examine synaptic adaptations following binge drinking (Drinking-in-the-Dark) in male mice, finding a constellation of changes that include increased AMPA and NMDA receptor function at insula synapses onto striatal projection neurons. They go on to assess a causal role for this projection in regulating binge drinking using optogenetics, finding that stimulating insula->striatal transmission in vivo reduces total ethanol consumed during DID, along with several specific behavioral measurements of drinking microstructure. One of the most interesting of these findings is a decrease in "front-loading", or drinking during the very beginning of the session, a phenotype that has been associated with problematic drinking and alcohol use disorder in humans. Finally, the authors use machine learning to build a predictive model that can reliably discern stimulated mice from controls. These studies improve our understanding of the neurocircuitry that mediates binge drinking and synaptic and circuit adaptations that occur following binge drinking. Experiments are blinded and performed in a rigorous manner, including physiological validation experiments in support of the in vivo optogenetic manipulation. Despite many strengths, there are significant limitations and gaps in the electrophysiology studies included in this version of the manuscript. As acknowledged by the authors, there are curious findings that are seemingly at odds with each other, and further studies addressing cell type specificity and/or feedforward inhibition would significantly improve the interpretation of this work. Furthermore, the manuscript would be significantly improved by an expanded Introduction containing more specific background information along with a standalone Discussion to place these findings within the broader literature. Lastly, a major limitation of these studies is the low number of mice used for the in vivo optogenetic control experiments and the exclusion of female mice throughout.

Major concerns:

1) Expanded Introduction and Discussion. The Introduction does not discuss and/or downplays historical literature investigating neuroadaptations following binge drinking. Studies examining changes in glutamate receptor function within striatal circuits should be discussed in greater detail, rather than the broad pass and review citation included. Behavioral studies examining how the function of the insula and DLS regulate ethanol exposure should also be discussed, especially including work examining the insula to accumbens pathway. It would also be worthwhile to reference human studies implicating the insula and DLS in AUDs.

We have expanded the introduction and discussion to include these topics.

2) It is difficult to form a comprehensive picture of the electrophysiological changes reported in Figure 1. The data seems to indicate increased AMPAR function, even more increased NMDAR function, decreased glutamate release probability, and decreased population spikes. These conflicting findings are acknowledged and there are two possible factors mentioned in the manuscript - differential engagement of MSN populations and changes in feedforward inhibition through local interneurons. I disagree with the authors' dismissal of potential MSN subtype-specific effects contributing to these discrepancies. Although AIC inputs innervate D1 and D2 MSNs comparably under control conditions, it is quite possible that the pathways are differentially altered following DID, as has been observed in many reports of alcohol or drug exposure (e.g. Cheng et al. Biological Psychiatry 2017). On the other hand, I wholeheartedly agree with the authors that AIC-driven feedforward inhibition through local interneurons (or even MSNs) could explain the curious divergence between the synaptic and population-level changes depicted in Figure 1. I think additional experiments addressing to help connect the dots are critical in interpreting the changes described in this manuscript. The authors could consider targeted recordings from specific cell types (e.g. D1, D2, and/or interneurons), measurements of AMPA/NMDA receptor subunit stoichiometry, and/or additional experiments in conditions where feedforward transmission is blocked (e.g. PTX or TTX/4AP).

The reviewer has excellent points that will help elucidate a mechanism. Many of these suggestions are planned experiments in our laboratory, but are, in our opinion, beyond the scope of the present manuscript. Please see our response to Reviewer #2’s 3rd stated weakness. We have revised the text to incorporate some of the points raised here.

3) N=2 mice in the ICSS experiment in Figure 4J is not sufficient to interpret, and including error bars on this data set is misleading. There also appears to be a difference in distance traveled between GFP and ChR2 mice in Figure 4C, but statistics are not reported. It is also hard to understand what that might mean given the way these data are normalized.

For this revised manuscript we reran this experiment with 6 animals per group and updated Figure 4 I and J and the accompanying methods section titled “Intracranial self-stimulation” to reflect the change. We also note that the new, correctly powered experiment confirmed the previous claim that AIC inputs to the DLS do not modulate operant responding behaviors.

Author Response

Reviewer #2 (Public Review):

The authors have used every possible combination and permutation of treatments at different stages of diapause and post diapause development in the mouse and used conditional gene knockouts at different stages to tease out the interactions of Foxa2 with Msx1 and LIF in the reactivation and implantation process in mice. The authors extend diapause further after treatments with progesterone and an estrogen-degrading chemical to show that this will prolong diapause in the presence of Msx1. Overall this study advances our knowledge of the cross-talk between uterine endometrium and the blastocyst during and after the remarkable phenomenon that is diapause.

Strengths

Demonstrating that Msx1 is critical to maintaining diapause, and that diapause is maintained in Foxa2 deficient mice have clarified their interactions. It is interesting that LIF triggers implantation on day 8 but cannot support the pregnancy to full term. Suppression of the estrogen effects by progesterone or fulvestrant increases the duration of diapause. Demonstrating that Foxa2 induces diapause via interactions with MSX1 shows Foxa2 plays such an important role in the control of diapause and adds another 'cog' to the complex wheel of its control.

Weaknesses

There is an assumption that everyone will understand the various manipulations that are done in this study - some effort needs to be made to clarify each experimental stage. How long are the embryos viable after the extension of the diapause by the various manipulations.

The very positive review by a well-known expert in the field of diapause is reassuring, and we agree with her suggestions to improve the quality of the manuscript. As recommended, we now provide a scheme to summarize our findings to illustrate the length of embryo dormancy (see Fig. 7).

Reviewer #3 (Public Review):

Matsuo et al. have authored a manuscript describing the effects of depletion of the forkhead box gene, Foxa2, on embryogenesis and gestation in the mouse. The effects of this treatment are the induction of the diapause arrest in the development of the embryo and consequent dormancy. The manuscript is wellprepared, and the figures, for the most part, are didactic and interpretable. Although the conclusions are interesting, the principal weaknesses of the manuscript are the lack of novelty and the perceived absence of some controls and follow-up experiments.

Controls and Follow-ups:

1) The Cre/lox system depletes rather than deletes genes. Although in situ data are presented, these are not judged to be quantitative. The usual qPCR analysis of tissues could have established the quantity of depletion. Stupid but can be done. This is important because the frequency of implantation sites in both Cre/lox models (lines 111-113) may be attributable to the residual expression of Foxa2.

The Foxa2f/fPgrCre/+ and Foxa2f/fLtfCre/+ mouse models used in the current study have been used in the previous studies (refs 7 and 8 in the manuscript). The deletion efficiency of Foxa2 in Foxa2f/fPgrCre/+ mice was examined by RT-PCR and IHC (figure 2 in ref 7); while the deletion efficiency in Foxa2f/fLtfCre/+ mice was examined by IHC (figure S1 in ref 8). The deletion efficiency has been proven by hundreds of publications since the generations of Pgr-cre in 2005 and Ltf-cre mice in 2014.

Although these mouse lines have been used before, we confirmed the deletion of Foxa2 at the beginning of our study at protein levels (fig 1c) and RNA levels (fig 1d). We understand that the reviewer is trying to link the observation that some of the knockout animals still carried implantation sites on day 8 of pregnancy with the possibility that the deletion of Foxa2 is not complete. However, it is not uncommon to observe such phenotypes that are not fully penetrant even in systemic knockout mouse models. Nonetheless, we now provide real time PCR results of uterine Foxa2 on day 4 of pregnancy in all mouse models used in the current manuscript in the new supplemental figure 1.

2) The most novel and salient finding of the present study is that the depletion of Foxa2 results in embryos that are in a state that "morphologically resembled dormant blastocysts". A useful experiment would have been to transplant these embryos to normal recipients or to culture them in vitro to determine whether they were capable of reactivation from the dormant state.

Whether dormant embryos in Foxa2f/fPgrCre/+ and Foxa2f/fLtfCre/+ uteri can be reactivated is the main question we studied. The results in figures 4-6 address this question. The blastocysts in Foxa2f/fPgrCre/+ and Foxa2f/fLtfCre/+ uteri can be activated on day 4 as shown in figure 4b. Without any support, blastocysts in Foxa2f/fLtfCre/+ uteri still can be reactivated on day 8 (figure 4b). In the following experiments and results shown in figures 5 and 6, we tried to improve the uterine environment by supplementing progesterone and estrogen. Dormant embryos are successfully re-activated by a LIF injection and the pregnancies proceeded to full terms.

This reviewer suggests using normal recipients to test the reactivation of dormant embryos. Given dormant embryos can be reactivated in a knockout uterine environment, embryo transfer experiments using normal recipients are an addition measure to test the integrity of embryonic dormancy. The embryo transfer experiments may be futile attempt in our studies because of the following reasons.

The numbers of mated mutant females that yield blastocysts are relatively meager and so are the numbers of blastocysts recovery, especially from diapausing donors. It is well known that implantation rates after blastocyst transfer are compromised due the surgical trauma and anesthesia. Therefore, the results from these experiments may not provide meaningful information.

Furthermore, during the pandemic our mouse colonies were drastically reduced, and we are still recovering from this downturn during this “New Normal”. Notably, pregnancy rate fluctuates throughout the year even if mice are housed in a controlled environment, and pregnancy rate is often relatively poor in mutant mice which of course depend on the genetic background and diets (DOI: 10.1126/scisignal.aam9011). Most importantly, viability of diapausing embryos is amply evident from our experiments (Figs. 4-6)

3) Figure 3C indicates that embryos recovered on Day 8 had an extensive proliferation of ICM cells, but not trophoblast. Previous studies have explored the progression of entry and exit from diapause in the mouse (DOI: 10.1093/biolre/ioz017) showing that reactivation of the embryo from diapause commences in the ICM and then proceeds to the trophoblast. It therefore may be possible that proliferation in the trophoblast is not suspended, rather than the recovered blastocyst has resumed development and that mitotic activity has not yet reached the trophoblast.

It is common to see KI67 expression in the ICM of dormant embryos. Figure 4D from the paper quoted by this reviewer presents Ki67 staining on embryos undergoing diapause at different stages. In our study, we showed Ki67 staining on dormant embryos collected on day 8, which equals D7.5 in their figure. Our data in figure 3C is consistent with observation shown. Without LIF, embryos remain dormant in Foxa2f/fPgrCre/+ and Foxa2f/fLtfCre/+ uteri.

4) In Figure 4B, neither the Ltf nor the Pgr Cre treated uteri appear normal on Day 8. This is not consistent with the conclusion in lines 170 et seq. of the manuscript. It is difficult to discern normality from Figure 4C, but it is clear that the PgrCre-lox uterus does not conform to the controls. It is later noted that there is edema in the uteri at this time in the Day 8-treated PgrCre/lox mice (lines 217-218).

We have clarified our description.

Lines 173-176: Notably, implantation sites with a normal appearance were observed in Foxa2f/fLtfCre/+ uteri when LIF was given on day 8 of pregnancy (Figure 4b), albeit Foxa2f/fPgrCre/+ uteri with edema have only faint blue bands. Histology of implantation sites confirmed this observation.

In line 217, we stated that “the uterine edema in Foxa2f/fPgrCre/+ females two days after LIF injection on day 8…”. Figure 4B showed that Foxa2f/fPgrCre/+ uteri with edema have some very faint blue bands suggesting implantation-like reaction. But we do not think they are real implantation, which is confirmed by figures 4c and e.

5) In Figure 6B, the implantation sites appear substantially smaller in mice of both mutant genotypes. Supplemental Figure 4 suggests that this is not the case. It is unclear whether the samples chosen for figures are representative of the uteri and whether variation in the size of implantation sites was observed.

In figure 6B, the Foxa2f/f uteri samples were collected on day 10 of pregnancy, which is same as when Foxa2f/fPgrCre/+ and Foxa2f/fLtfCre/+ tissues were collected. Since embryos implanted in Foxa2f/f uteri on day 4 night but in Foxa2f/fPgrCre/+ and Foxa2f/fLtfCre/+ uteri on day 8 after LIF injections, the implantation sites are bigger in Foxa2f/f uteri. However, in supplemental figure 4 the implantation sites were collected from Foxa2f/f females on day 6 of pregnancy, which show similar size as compared to implantation sites collected from Foxa2f/fPgrCre/+ and Foxa2f/fLtfCre/+ females 2 days after LIF injection.

Reviewer #2 (Public Review):

Transgenerational effects (TE) (usually defined as multigenerational effects lasting for at least three generations) generated a lot of interest in recent years but the adaptive value of such effects is unclear. In order to understand the scope for adaptive TE we need to understand i) whether such effects are common; ii) whether they are stress-specific; and iii) if there are trade-offs with respect to performance in different environments. The last point is particularly important because F1, F2 and F3 descendants may encounter very different environments. On the other hand, intergenerational effects (lasting for one or two generations) are relatively common and can play an important role in evolutionary processes. However, we do not know whether intergenerational and transgenerational effects have same underlying mechanisms.

This study makes a big step towards resolving these questions and strongly advances our understanding of both phenomena. Much of the previous work on mechanisms of multigenerational effects has been conducted in C. elegans and this works uses the same approach. They focus on bacterial infection, Microsporidia infection, larval starvation and osmotic stress. I did not quite understand why the authors chose to focus on P. vranovensis rather than P. aeruginosa P14 that has been used in previous studies of transgenerational effects in C. elegans. However, this is a minor point because I guess they were interested in broad transgenerational responses to bacterial infection rather than in strain-specific ones. The authors used different Caenorhabditis species, which is another strength of this study in addition to using multiple stresses.

They found 279 genes that exhibited intergenerational changes in all C species tested, but most interestingly, they show that a reversal in gene expression corresponds to a reversal in response to bacterial infection (beneficial in two species and deleterious on one). This is very intriguing! This was further supported by similar observations of osmotic stress response.

They also report that intergenerational effects are stress-specific and there have deleterious effects in mismatched environments, and, importantly, when worms were subject to multiple stresses. It is quite likely that offspring will experience a range of environments and that several environmental stresses will be present simultaneously in nature. I really liked this aspect of this work as I think that tests in different environments, especially environments with multiple stresses, are often lacking, which limits the generality of the conclusions.

Another interesting piece of the puzzle is that beneficial and deleterious effects could be mediated by the same mechanisms. It would be interesting to explore this further. However, this is not a real criticism of this work. I think that the authors collected an impressive dataset already and every good study generates new research questions.

Given these findings, I was particularly keen to see what comes of transgenerational effects. The general answer was that there aren't many, and the authors conclude that all intergenerational effects that they studied are largely reversible and that intergenerational and transgenerational effects represent distinct phenomena. While I think that this is a very important finding, I am not sure whether we can conclude that intergenerational and transgenerational effects are not related.

In my view, an alternative interpretation is that intergenerational effects are common while transgenerational effects are rare. Because intergenerational effects are stress-specific, transgenerational effects could be stress-specific as well.

Perhaps different mechanisms regulate intergenerational responses to, say, different forms of starvation (e.g. compare opposing transgenerational responses to prolonged larval starvation (Rechavi et al. doi:10.1016/j.cell.2014.06.020) and rather short adulthood starvation (Ivimey-Cook et al. 2021 https://doi.org/10.1098/rspb.2021.0701). Perhaps some (most?) forms of starvation generate only intergenerational responses and do not generate transgenerational responses. But some do. Those forms of starvation that generate both intergenerational and transgenerational effects could do so via same mechanisms and represent the same phenomenon. I am by no means saying this is the case, but I am not sure that the absence of evidence of transgenerational effects in this study necessarily suggests that inter- and trans-generational effects are different phenomena.

The only concern real concern was the lack of phenotypic data on F3 beyond gene expression. Ideally, I would like to see tests of pathogen avoidance and starvation resistance in F3. However, given the amount of work that went into this study, the lack of strong signature of potential transgenerational effects in gene expression, and the fact that most of these effects were shown previously to last only one generation, I do not think this is crucial.

It would be very interesting to compare gene expression and other phenotypic responses in F1 and F3 between P. vranovensis and PA14. Also, it would be interesting to test the adaptive value of intergenerational and transgenerational effects after exposure to both strains in different environments. This is would be very informative and help with understanding the evolutionary significance of transgenerational epigenetic inheritance of pathogen avoidance as reported previously. Why response to P. vranovensis is erased while response to PA14 is maintained for four generations? Are nematodes more likely to encounter one species than the other? Again, however, this is not something necessary for this study.

The main strengths of this paper are i) use of multiple stresses; ii) use of multiple species; iii) tests in different environments; and iv) simultaneous evaluation of intergenerational and transgenerational responses. This study is first of a kind, and it provides several important answers, while highlighting clear paths for future work. Excellent work and I think it will generate a lot of interest in the community.

Reviewer #2 (Public Review):

This paper seeks to test the extent to which adaptation via selective sweeps has occurred at disease-associated genes vs genes that have not (yet) been associated with disease. While there is a debate regarding the rate at which selective sweeps have occurred in recent human history, it is clear that some genes have experienced very strong recent selective sweeps. Recent papers from this group have very nicely shown how important virus interacting proteins have been in recent human evolution, and other papers have demonstrated the few instances in which strong selection has occurred in recent human history to adapt to novel environments (e.g. migration to high altitude, skin pigmentation, and a few other hypothesized traits).

One challenge in reading the paper was that I did not realize the analysis was exclusively focused on Mendelian disease genes until much later (the first reference is not until the end of the introduction on pages 7-8 and then not at all again until the discussion, despite referring to "disease" many times in the abstract and throughout the paper). It would be preferred if the authors indicated that this study focused on Mendelian diseases (rather than a broader analysis that included complex or infectious diseases). This is important because there are many different types of diseases and disease genes. Infectious disease genes and complex disease genes may have quite different patterns (as the authors indicate at the end of the introduction).

The abstract states "Understanding the relationship between disease and adaptation at the gene level in the human genome is severely hampered by the fact that we don't even know whether disease genes have experienced more, less, or as much adaptation as non-disease genes during recent human evolution." This seems to diminish a large body of work that has been done in this area. The authors acknowledge some of this literature in the introduction, but it would be worth toning down the abstract, which suggests there has been no work in this area. A review of this topic by Lluis Quintana-Murci1 was cited, but diminished many of the developments that have been made in the intersection of population genetics and human disease biology. Quintana-Murci says "Mendelian disorders are typically severe, compromising survival and reproduction, and are caused by highly penetrant, rare deleterious mutations. Mendelian disease genes should therefore fit the mutation-selection balance model, with an equilibrium between the rate of mutation and the rate of risk allele removal by purifying selection", and argues that positive selection signals should be rare among Mendelian disease genes. Several other examples come to mind. For example, comparing Mendelian disease genes, complex disease genes, and mouse essential genes was the major focus of a 2008 paper2, which pointed out that Mendelian disease genes exhibited much higher rates of purifying selection while complex disease genes exhibited a mixture of purifying and positive selection. This paper was cited, but only in regard to their findings of complex diseases. A similar analysis of McDonald-Kreitman tables3 was performed around Mendelian disease genes vs non-disease genes, and found "that disease genes have a higher mean probability of negative selection within candidate cis-regulatory regions as compared to non-disease genes, however this trend is only suggestive in EAs, the population where the majority of diseases have likely been characterized". Both of these studies focused on polymorphism and divergence data, which target older instances of selection than iHS and nSL statistics used in the present study (but should have substantial overlap since iHS is not sensitive to very recent selection like the SDS statistic). Regardless, the findings are largely consistent, and I believe warrant a more modest tone.

There are some aspects of the current study that I think are highly valuable. For example, the authors study most of the 1000 Genomes Project populations (though the text should be edited since the admixed and South Asian populations are not analyzed, so all 26 populations are not included, only the populations from Africa, East Asia, and Europe are analyzed; a total of 15 populations are included Figures 2-3). Comparing populations allows the authors to understand how signatures of selection might be shared vs population-specific. Unfortunately, the signals that the authors find regarding the depletion of positive selection at Mendelian disease genes is almost entirely restricted to African populations. The signal is not significant in East Asia or Europe (Figure 2 clearly shows this). It seems that the mean curve of the fold-enrichment as a function of rank threshold (Figure 3) trends downward in East Asian and European populations, but the sampling variance is so large that the bootstrap confidence intervals overlap 1). The paper should therefore revise the sentence "we find a strong depletion in sweep signals at disease genes, especially in Africa" to "only in Africa". This opens the question of why the authors find the particular pattern they find. The authors do point out that a majority of Mendelian disease genes are likely discovered in European populations, so is it that the genes' functions predate the Out-of-Africa split? They most certainly do. It is possible that the larger long-term effective population size of African populations resulted in stronger purifying selection at Mendelian disease genes compared to European and East Asian populations, where smaller effective population sizes due to the Out-of-Africa Bottleneck diminished the signal of most selective sweeps and hence there is little differentiation between categories of genes, "drift noise"). It is also surprising to note that the authors find selection signatures at all using iHS in African populations while a previous study using the same statistic could not differentiate signals of selection from neutral demographic simulations4.

The authors find that there is a remarkably (in my view) similar depletion across all but one MeSH disease classes. This suggests that "disease" is likely not the driving factor, but that Mendelian disease genes are a way of identifying where there are strongly selected deleterious variants recurrently arising and preventing positively selected variants. This is a fascinating hypothesis, and is corroborated by the finding that the depletion gets stronger in genes with more Mendelian disease variants. In this sense, the authors are using Mendelian disease genes as a proxy for identifying targets of strong purifying selection, and are therefore not actually studying Mendelian disease genes. The signal could be clearer if the test set is based on the factor that is actually driving the signal.

One of the most important steps that the authors undertake is to control for possible confounding factors. The authors identify 22 possible confounding factors, and find that several confounding factors have different effects in Mendelian disease genes vs non-disease genes. The authors do a great job of implementing a block-bootstrap approach to control for each of these factors. The authors talk specifically about some of these (e.g. PPI), but not others that are just as strong (e.g. gene length). I am left wondering how interactions among other confounding factors could impact the findings of this paper. I was surprised to see a focus on disease variant number, but not a control for CDS length. As I understand it, gene length is defined as the entire genomic distance between the TSS and TES. Presumably genes with larger coding sequence have more potential for disease variants (though number of disease variants discovered is highly biased toward genes with high interest). CDS length would be helpful to correct for things that pS does not correct for, since pS is a rate (controlling for CDS length) and does not account for the coding footprint (hence pS is similar across gene categories).

The authors point out that it is crucial to get the control set right. This group has spent a lot of time thinking about how to define a control set of genes in several previous papers. But it is not clear if complex disease genes and infectious disease genes are specifically excluded or not. Number of virus interactions was included as a confounding factor, so VIPs were presumably not excluded. It is clear that the control set includes genes not yet associated with Mendelian disease, but the focus is primarily on the distance away from known Mendelian disease genes.

Minor comments:

On page 13, the authors say "This artifact is also very unlikely due to the fact that recombination rates are similar between disease and non-disease genes (Figure 1)." However, Figure 1 shows that "deCode recombination 50kb" is clearly higher in disease genes and comparable at 500kb. The increased recombination rate locally around disease genes seems to contradict the argument formulated in this paragraph.

1. Quintana-Murci L. Understanding rare and common diseases in the context of human evolution. Genome Biol. 2016 Nov 7;17(1):225. PMCID: PMC5098287<br /> 2. Blekhman R, Man O, Herrmann L, Boyko AR, Indap A, Kosiol C, Bustamante CD, Teshima KM, Przeworski M. Natural selection on genes that underlie human disease susceptibility. Curr Biol. Elsevier BV; 2008 Jun 24;18(12):883-889. PMCID: PMC2474766<br /> 3. Torgerson DG, Boyko AR, Hernandez RD, Indap A, Hu X, White TJ, Sninsky JJ, Cargill M, Adams MD, Bustamante CD, Clark AG. Evolutionary processes acting on candidate cis-regulatory regions in humans inferred from patterns of polymorphism and divergence. PLoS Genet. Public Library of Science (PLoS); 2009 Aug;5(8):e1000592. PMCID: PMC2714078<br /> 4. Granka JM, Henn BM, Gignoux CR, Kidd JM, Bustamante CD, Feldman MW. Limited evidence for classic selective sweeps in African populations. Genetics. Oxford University Press (OUP); 2012 Nov;192(3):1049-1064. PMCID: PMC3522151

Author Response:

Reviewer #1:

The manuscript by Bellio and colleagues is based on the experimental model of T. cruzi infection in WT, MyD88-/- and IL-18-/- mice previously described by the same group in a 2017 eLife publication. The main message of the current study is that, in addition to IFN-g+ Th1 effectors, T. cruzi infection induces an even larger population of cytotoxic CD4+ T cells.

The characterization of the cytotoxic CD4+ T cells is well documented. The data shown are convincing. However, since Burel et al. (2012) described the existence of a similar population in humans infected with P. falciparum (an intracellular pathogen), the authors should modify the statement (line 35-36) in the abstract.

First, we would like to thank Reviewer #1 for the positive comments on our work.

Please note that our statement in the abstract is: “Here, for the first time, we showed that CD4CTLs abundantly differentiate during mouse infection with an intracellular parasite” refers to mouse experimental models of parasite infection and not to human studies. We could not find any article with Burel JG as first author published in 2012; we believe that Reviewer# 1 is referring to a study published in 2016 (Burel et al. PLoS Pathog. 2016 Sep 23;12(9):e1005839), in which a population of CD4 T cells with cytotoxic properties was described in humans after primary exposure of blood-stage malaria parasites. Please note that the finding of the important role of T-cell intrinsic IL- 18R/MyD88 signaling for the development of a strong CD4CTL response is also part of the main message of our manuscript.

Similarly, the title "Cytotoxic CD4+ T cells… predominantly infiltrate Trypanosoma cruzi-infected hearts" is an overstatement. If cytotoxic CD4+ T cells outnumber 10:1 IFN-g-secreting population (in lymphoid tissue) their higher representation in hearts of infected mice is not a selective phenomenon but rather expected.

We would like to thank Reviewer #1 for this comment, giving us the opportunity to clarify this point. Of note, we were not referring to the ratio of CD4CTL to Th1 cells, but to the frequency of CD4CTL among all the CD4+CD44+ (activated/memory) T cells. In fact, as shown in Figure 7-figure supplement 2, (now added to the revised ms), we found that the frequency of GzB+ cells among all activated/memory CD4+CD44hi T cells is significantly increased in the heart compared to the frequency of GzB+ among CD4+CD44hi T cells found in the spleen. Please also note that the frequency of CD4+ T cells expressing both GzB and PRF also increases in the heart compared to the spleen (Fig. 7F, middle panel and Fig. 1D left panel). We are now including this information in the revised manuscript, clarifying this point.

My major concern is that the function of these cells remains undefined. Are they beneficial or detrimental for the host? It appears that the authors themselves could not make up their minds. The GzB+ CD4+ T cells protect but do not decrease the parasite load (Fig 6G).

Our results in the mouse model of infection with T. cruzi, employing the adoptive transfer of WT CD4+GzB+ T cells to the susceptible Il18ra-/- mouse strain, indicate a clear beneficial role of CD4CTLs in the acute phase of experimental T. cruzi infection. Significantly extended survival was observed in the group of mice receiving sorted CD4+GzB+ cells, without, however, decreasing parasite load (Figure 6G). We would like to comment here that in order to be beneficial to the host, an immune response does not always result in decreasing the pathogen load. In fact, in certain circumstances, to hinder the excessive inflammatory response (which can lead to host death), is an advantage for the host, even if this does not result in the reduction of the pathogen numbers. The advantage conferred to the host by regulating the inflammatory response was probably also explored in pathogen/host co-evolution, giving rise to chronic infections, where the host can survive for a longer period and the pathogen increases its chances of transmission (Schneider DS & Ayres JS., 2008, Nat Rev Immunol;8(11):889; Medzhitov R, et al, 2012, Science; 335(6071):936). Therefore, the results shown on Figure 6G are fully compatible with a potential regulatory role exerted by CD4CTLs, previously proposed by other authors (Mucida et al, Nat. Immunol. 2013), and point to the beneficial role of CD4CTLs for the host in the acute phase of infection with T. cruzi, probably by contributing to the decrease of immunopathology, the detrimental side of an exacerbated immune response, as discussed. Also favoring this hypothesis, the frequency of CD4CTLs expressing immunoregulatory molecules is increased when compared to other activated CD4+T cell subsets (Figure 3 and new Figure 7-figure supplements 3 and 4). Please see our complete discussion on this subject in the revised manuscript.

On the other hand, during the chronic phase of the disease, the persistence of the immune response against the parasite might involve functional changes in the CD4 T cell response. This hypothesis could explain the association found between CD4CTLs and cardiomyopathy in chronic Chagas patients. Therefore, a beneficial role for CD4CTLs in the acute phase is totally compatible with the hypothesis that, during the chronic response in a persistent infection, CD4CTLs might acquire a detrimental role, contributing to immunopathology. Of note, several studies in the literature have shown a beneficial role for Th1 cells during the acute phase of infection with T. cruzi, while the Th1 response has also been associated to a pathologic outcome during the chronic phase of Chagas disease (reviewed in Ferreira et al, 2014 World J Cardiol 2014 6(8):7820 and in Fresno & Girones, 2018, Front.Immunol. 9;351). Therefore, it is not implausible that the CD4CTL subpopulation, could also display different roles in the acute versus the chronic phases of the infection with T. cruzi. However, at present, this hypothesis remains speculative as stated in the manuscript discussion. An extensive investigation of the role of CD4CTLs, as well as of immunoregulation mechanism acting in chronic Chagas patients need to be conducted to fully answer this question, which is beyond the scope of the present work. Nevertheless, we acknowledge that the alternative possibility remains, in which the higher levels of CD4CTLs in chronic patients reflect elevated parasite burden and/or inflammation in the heart, without a direct involvement of this cell subset in the pathology. Please see our answer to Review #2 on this topic and the inclusion of discussion clarifying this point in the revised manuscript.

Are they terminally differentiated or "exhausted" effectors? GzB+ CD4+ T cells can be found in the hearts of chronically infected mice, but we do not know if they are specific for pathogen or self Ags. Do they express the markers of exhaustion on day 14 in the heart?

1) We have commented in the first version of the manuscript that one of the limitations of our work is the fact that very few CD4 epitopes of T. cruzi presented by I-Ab have been described so far, and this limits the investigation on the specificity of CD4CTLs in our model. This is a very interesting and important question, which, however, is not possible to address in the present work.

We would like to thank Reviewer#1 for the suggestion of performing a broader analysis on the expression of immunoregulatory markers associated with exhaustion and/or terminal differentiation, which adds for the comprehension of CD4CTL biology in the model of acute infection with T. cruzi. Whether GzB+CD4+ T cells are terminally differentiated or "exhausted" effectors is an interesting and debated question. It was initially hypothesized that since exhausted T cells share features with terminally differentiated T cells, this would suggest a developmental relationship between these cell states (Akbar, A.N. & Henson, S.M., 2011 Nat. Rev. Immunol.11:289; Blank, C.U. et al, 2018, Nat.Rev.Immunol,19:665). However, subsequent studies showed that exhausted T cells seem to be derived from effector cells that retain the capacity to be long-lived (Angelosanto, J.M. et al., 2012, J. Virol. 86: 8161). In the first version of our manuscript, we investigated the expression of several markers associated with exhaustion such as 2B4, Lag-3, Tim-3 and CD39, besides the downregulation of CD27 on GzB+ CD4+ T cells (Figures 1E, 3B, 3D-E and 5E). In general, cells losing the expression of CD27 have been characterized as Ag-experienced further differentiated cells (Takeuchi and Saito, 2017, Front.Immunol. 8:194). Our finding that, differently from GzB-negative cells, most GzB+CD4+ T cells had lost the expression of CD27, suggested to us that CD4CTLs present in the spleen of mice infected with T. cruzi might be further differentiated T cells (Figure 3E). The transcription factor Blimp-1 controls the terminal differentiation of cells in a variety of immunological settings and its high expression in CD4+ and CD8+ T cells is associated to the expression of immunoregulatory markers (Chihara, N. et al, 2018, Nature 558:454). The observed high expression of Blimp-1 by GzB+CD4+ T cells (Figure 5D) is also compatible with the hypothesis that CD4CTLs are terminally differentiated. Of note, most of the exhaustion studies were performed on CD8+ T cells and it is still not well established if this phenomenon is equally regulated in CD4+ T cells. We have now extended the investigation on the expression of terminal differentiation/exhaustion markers, including PD-1 staining, on GzB+PRF+ CD4+ T cells in the spleen and in the heart of infected mice. Results in Figure 7-figure supplement 3, show that CD44hiGzB+PRF+ CD4+ T cells compose the subset of activated cells among which the higher frequency of cells expressing these markers is found, both in the spleen and in the heart, at day 14 pi. The only exception was the equal ratio of cells expressing PD-1, and at equivalent levels, when comparing CD44hiGzB-PRF- and CD44hiGzB+PRF+ CD4+ T cells in the spleen. Non-significant differences in the percentages of cells expressing PD-1 among CD44hiGzB-PRF- and CD44hiGzB+PRF+ CD4+ T cells were found in the heart. However, the intensity of expression of the PD-1 marker (MFI) was significantly higher among CD44hiGzB+PRF+ compared to CD44hiGzB-PRF- CD4+ T cells infiltrating the heart. Furthermore, we also compared the frequency of CD44hiGzB+PRF+ CD4+ T cells expressing Lag-3, Tim-3, CD39 and PD-1, and their corresponding MFI values, between the spleen and the heart (Figure 7-figure supplement 4). Of note, while MFI values of Tim-3, CD39 and PD-1 expression were increased on CD4CTLs (CD44hiGzB+PRF+) in the heart compared to CD4CTLs in the spleen, Lag-3 expression levels were decreased on CD4CTLs infiltrating the cardiac tissue. Despite exhaustion being often seen as a dysfunctional state, it is important to note that the expression of these inhibitor molecules allows strongly activated T cells to persist and partially contain chronic viral infections without causing immunopathology and that highly functional effector T cells can also express such inhibitory receptors (reviewed in Wherry, E.J., 2011, Nat. Immunol.,12:492; Blank, C.U. et al, 2018, Nat. Rev. Immunol., 19:665). Interestingly, only PD-1, but not Lag-3, Tim-3 or CD39 expression is upregulated on CD8CTLs in the heart relatively to the spleen, an indication that the T. cruzi-infected cardiac tissue is a less so-called exhaustion-inducing environment compared to certain tumors (Figure 7- figure supplement 4). It is known that many immunomodulatory molecules, including Lag-3, Tim-3, PD-1 and CD39 are co-expressed as part of a module composing a larger co-inhibitory gene program, which is expressed in both CD4+ and CD8+ T cells under certain activation conditions, driven by cytokine IL-27 (Chihara, N. et al, 2018, Nature 558:454). The opposing behavior of Lag-3 expression, which is downmodulated on CD4CTLs in the heart in comparison to the spleen, indicate that CD4CTLs infiltrating the heart are not typically exhausted cells. Of note, a recent study has shown that exhausted CD8+T cells can partially reacquire phenotypic and transcriptional features of T memory cells, in a process that includes the downmodulation of Lag-3 expression (Abdel-Hakeem, M.S. et al, 2021, Nat.Immunol., 22:1008). As requested, these new data were included (Figure 7-figure supplements 3 and 4) and discussed in the revised manuscript.

The factors that control differentiation of cytotoxic CD4+ T cells are the same as for IFN-g- Th1 cells. MyD-88-/- and IL-18-/- mice significantly lack both populations and succumb to T. cruzi infection. In their 2017 eLife publication, this group reported that survival of infected MyD-88-/- and IL-18-/- mice can be rescued by adoptive transfer of purified total WT CD4+ T cells, which was attributed entirely to their ability to secrete IFN-g (at least in the case of MyD-88-/- recipients). In the current study, the authors only used infected IL-18-/- recipients and show that this time transfer of GzB+ CD4+ T cells is sufficient to confer the protection. When compared with the old data, the rescue of the infected IL-18-/- with only GzB+ CD4+ T cells looks weaker (2 surviving animals out of 10 pooled from 2 experiments), strongly suggesting that IFN-g Th1 cells do play a significant role. It is unclear when the parasite load in Fig G6 was evaluated. It would be good to show deltaCT values for individual mice.

We thank Reviewer #1 for the opportunity to clarify the point on the protective role of Th1 and CD4CTLs cells during T. cruzi infection and to better discuss our data. Please note that we do not question the beneficial role of Th1 cells in this infection model. In our paper published in 2017 in eLife, we have shown that the adoptive transfer of IFN-g- deficient CD4+ T cells do not result in the decrease of parasite loads in susceptible recipient mice. These results are totally in agreement with the known beneficial role of Th1 cells during infection with T. cruzi, through the microbicidal action of IFN-g, which was also described by other groups.

The new information that our present study brings is that the adoptive transfer of GzB+CD4+ T cells with poor (GzB-YFP+) or no (Ifng-/-) capacity of IFN-g secretion, also significantly extended survival of infected Il18r-/- mice, which have lower levels of both Th1 and CD4CTLs, compared to WT mice (Figure 6G and Figure 6-figure supplement 2). Please note that 3 (not 2) out of 10 mice that received GzB+CD4+ T cells survived. We stated in our discussion that, together, our present and past data demonstrate that both Th1 and CD4CTL are important for improving survival, although through different mechanisms, since adoptively transferred GzB+CD4+ T cells (as well as Ifng-/- CD4+ T cells) were not capable of reducing parasite load but, notwithstanding, extended survival.

Following the guidelines of the Animal Care and Use Committee, in order to prevent/alleviate animal suffering, all laboratory animals found near death must be euthanized. Therefore, parasite load in the hearts was evaluated in mice found at the moribund condition (a severely debilitated state that precedes imminent death, as defined in Toth, L.,2000; ILAR J, 41:72), presenting unambiguous signals that the experimental endpoint has been reached. We have now included 2ˆDeltaCT values for individual mice in Figure 6G, as requested.

Because donor IFN-g-/- CD4+ T cells do express IFN-gR (Supp Fig 6-2), IFN-g produced by IL-18-/- host cells could enhance the activity and/or help expand cytotoxic CD4+ T cells among the IFN-g-/- CD4+ donor population. To directly test the protective role of cytotoxic CD4+ T cells in the absence of IFN-g, the authors should treat infected IL-18-/- mice that have received IFN-g-/- CD4+ T cells with anti-IFN-gamma Ab.

It is known that IFN-g is critically important for resistance against infection with T. cruzi. Accordingly, Ifng-/- mice are extremely susceptible, dying at early time points of infection (Campos, M. et al, 2004, J.Immunol, 172:1711). Of note, IFN-g production by other cell types, and not only derived from CD4+ T cells, is relevant for resistance against infection, as demonstrated for CD8+ T cells (Martin D & Tarleton R. Immunol Rev. 2004, 201:304). In our present work, we performed experiments where Ifng-/- CD4+ T cells were adoptively transferred to susceptible Il18ra-/- mice, with the goal of testing whether the transferred cells would be able to confer some increment in the survival time of infected mice, despite of not being able to decrease parasite loads, a direct consequence of their deficiency in IFN-g production, as previously shown (Oliveira et al., 2017, eLife). In fact, this turned out to be the case and we showed that the transfer of purified Ifng-/- CD4+ T cells extended survival (Figure 6-figure supplement 2). Of note, our data demonstrate that the percentage of GzB+CD4+ T cells is not affected in the total absence of IFN-g, since Ifng-/- mice display the same frequency of this cell population as found in WT mice (Figure 4B). The increased survival of adoptively transferred mice is compatible with a regulatory function of GzB+CD4+ T cells, which additionally express several immunoregulatory molecules, as shown. Whether IFN-g produced by the host is enhancing the activity and/or expanding cytotoxic CD4+ T cells among the transferred T cell population is not an essential point here, since we were not aiming to test the protective role of cytotoxic CD4+ T cells in the total absence of IFN-g in the host mice.

The intracellular cytokine staining in this study appears to be suboptimal. Instead of stimulating with PMA/ionomycin in the presence of Golgi block, Roffe et al. (2012) stimulated lymphocytes with anti-CD3 prior to adding Brefeldin A, an important technical difference which may explain the rather low frequencies of IFN-g+ and IL-10+ cells in this study.

We respectfully disagree from Reviewer #1 on this point. The frequency of IFNg+ CD4+ and IL-10+CD4+ T cells in the spleen of mice infected with T. cruzi Y strain obtained in our experiments is in the same range to what was previously described by other research groups investigating the immune response to this parasite, including studies that have employed anti-CD3 stimulation and brefeldin A, such as Jankovic, D. et al, 2007, JEM 204:273 (Fig.S1), cited in our manuscript (page 9, lines 218-219), among others (Nihei J et al, 2021, Front. Cell. Infect. Microbiol.11:758273; Martins GA et al, 2004, Microbes Infect 6:1133 – Fig.6B; Hamano S. et al, 2003, Immunity, 19:657- Fig. 2A). In the present work, we used the combination of monensin and brefeldin A after PMA/iono treatment, and found the same frequency of IFN-g+CD4+ T cells described in a previous study of our group, where staining was performed after incubation of splenocytes with parasite-derived protein extract and brefeldin A alone (Oliveira AC et al., 2010, PLoSPath 6(4):e1000870 –Fig. 8D). On the other hand, please note that the study cited by Rev. #1 (Roffe et al., JI 2012) employed a different strain of T. cruzi, the Colombiana strain, which differs in several aspects from the Y strain used in our work. Colombiana induces a different pathology, with distinct kinetics. In that study, intracellular IFN-g and IL-10 detection was performed at a much later time point of infection (day 30 pi), and in cells infiltrating the heart, not the spleen. In summary, frequencies of IFN-g and IL-10 secreting CD4+ T cells described in our manuscript are comparable to the ones found in the spleen of mice infected with the same or similar strains of T. cruzi and reported in articles of prestigious journals by other groups, cited above.

Reviewer #2:

In this work, Professor Bellio and her colleagues provide compelling evidence to show unusually strong induction of cytotoxic CD4 T cells (CD4CTLs) in Trypanosoma cruzi-parasitized mice. Using genetic models and mixed bone marrow chimeras they dissect the signals responsible for CD4CTL induction in this infection and identify T cell-intrinsic IL-18R/MyD88 signaling as the key inducer. The CD4CTLs that clonally expand in T. cruzi infection outnumber CD4 cells with typical Th1 profile (IFN-γ secretion) and bear the hallmarks of CD4CTLs described in other model systems and in humans. Utilizing GzmbCreERT2/ROSA26EYFP reporter mice, the authors show that adoptive transfer of CD4 cells that have made GzB can increase the survival of T. cruzi parasitized l18ra-/- mice. Finally, the authors describe a clear correlation between the frequency of CD4CTLs the circulation of patients with T. cruzi-induced chronic Chagas cardiomyopathy, implying a pathogenic role for these cells in chronic disease.

The findings reported here are an important addition to the understanding of both the origin of CD4CTLs and their potential role in host protection or disease. The evidence provided in support of the main claims is very strong and the association between CD4CTLs and Chagas disease quite intriguing. There are, however, some aspects of the work that would benefit from further clarification or experimental support, so that alternative interpretations of the data can be excluded.

The defining characteristic of CD4CTLs that separates them from other CD4 subsets is the production of granzymes and perforin and, by extension, the ability to kill target cells in a granzyme/perforin-dependent manner. In contrast, all T cells can kill target cells via alternative mechanisms that are not dependent on granzyme/perforin, for example through expression of TNF family members. It would appear that much, if not most, of the killing activity of T. cruzi-induced CD4CTLs can be attributed to FasL (Fig. 1B). FasL-mediated killing is not restricted to CD4CTLs and as the title of one of the cited studies (Kotov et al., 2018) states, "many Th cell subsets have Fas ligand-dependent cytotoxic potential". It would be important to ascertain if expression of granzyme/perforin by CD4CTLs in T. cruzi infection is also associated with granzyme/perforin-dependent cytotoxicity. This affects the direct and indirect in vitro cytotoxicity assays, as well as the interpretation of in vivo protection.

Similarly, the protective effect of transferring GzmbCreERT2/ROSA26EYFP reporter-positive cells to Il18ra-/- mice may not be necessarily mediated in a granzyme/perforin-dependent manner or by CD4CTLs for that matter. The reporter will mark cells that express GzB at the time of tamoxifen administration but does not guarantee that these cells will continue to express GzB or that they will prolong survival of recipients in a granzyme/perforin-dependent manner.

While the authors provide evidence that GzB-producing cells are largely distinct from IFN-γ-producing cells, the reporter-positive cells may still contain genuine Th1 cells. Given Th1 cells have been previously found necessary for protection of Il18ra-/- mice in the T. cruzi model, can a role for Th1 cells in this transfer model be formally excluded? The authors do convincingly demonstrate that IFN-γ itself is not essential for protection, but that does not leave granzyme/perforin-dependent as the only other alternative. For example, the experiment described in Fig. 6G lacks an important control, the transfer of reporter-negative cells. What would the conclusion be if reporter-negative (but T. cruzi-specific) cells proved as protective as reporter-positive cells?

We would like to thank Reviewer #2 for the positive comments on our study and for giving us the opportunity to better discuss and clarify the relevant points raised in this review.

(i) Concerning the role of GzB/PRF in cytotoxicity: as explained in more details in our next answer to Reviewer #2, we have now shown that the cytolytic activity of the CD4 T cell subset differentiating in the murine T. cruzi-infection model is totally dependent on a GzB- and PRF-mediated mechanism.

(ii) Concerning a possible role for Th1 in the adoptive transfer experiments: please note that the parasite load is not decreased by the adoptive transfer of CD4+GzB+ T cells (Figure 6G); Additionally, we showed that the adaptive transfer of Ifng-/- CD4+ T cells also extend the survival of infected mice (Figure 6-figure supplement 2), but did not decrease parasite levels (Oliveira et al., 2017). These results exclude a role for Th1 cells, which are known to exert an important microbicidal function through the production of IFN-g, as previously demonstrated by us (Oliveira, 2017) and other groups. Together, our present and past data support the notion that both Th1 and CD4CTL are important for extending survival, although through different mechanisms. Our results are in accordance with an immunoregulatory role played by CD4CTLs, likely through the GzB/PRF/FasL-mediated killing of infected APCs in an IFN-g-independent manner, although it is not possible to attribute the beneficial role of the adoptively transferred CD4CTLs exclusively to their cytolytic function, as discussed in the revised manuscript. Of note, we also show here that most CD4+GzB+PRF+ T cells express high levels of immunomodulatory molecules, raising the possibility that the beneficial role of adoptively transferred CD4CTLs might rely on the concerted action of their cytolytic function and immunomodulatory activity. Please see the full discussion on this point in the revised version of the manuscript.

(iii) Concerning the adoptive transfer of GzB-EYFP-negative cells: unfortunately, GzB-EYFP-negative cells cannot be employed as a control, since in the GzmBCreERT2/ ROSA26EYFP mouse line age, only 1 - 3 % of total splenic CD4+ T cells express EYFP after induction by tamoxifen (Figure 2-figure supplement 3). This contrasts to 10-40% of GzB+ and PFR+ cells among CD4+ T lymphocytes, observed by intracellular staining. Consequently, the majority of the CD4+GzB+ T population is EYFP-negative in this system and thus, sorted “GzB-EYFP-negative”, based on the absence of expression of EYFP, would not be bona-fide GzB-negative cells. If it were possible to sort GzB reporter-negative cells, Th1 cells would be among the sorted cells and upon adoptive transfer they would secrete IFN-g and, consequently, decrease the parasite load in recipient mice (Oliveira, 2017). However, in the absence of the proposed immunoregulatory action of CD4CTLs, Th1 cells transferred alone might also increase pathology and, consequently, it is possible that they would not extend survival, albeit diminishing parasite load. It is expected that higher levels of extended survival would be attained when both Th1 and CD4CTLs are transferred, as discussed in the manuscript and in answer (ii) above. Importantly, please note that one current hypothesis is that CD4CTLs differentiate from Th1 and, therefore, the adoptive transfer of Th1 cells will not guarantee that Th1-derived CD4CTLs would not be developing in vivo, unless special engineered mouse strains, not available at present, would be employed for these experiments.

Reviewer #3:

By modelling trypanosoma cruzi infection in mice, the authors highlighted the presence of a subsets of CD4 T cells expressing canonical markers and transcription factors of CTLs and capable of exerting antigen specific and MHC class II restricted cytotoxic activity. Mechanistically, using KO mice, the authors have shown that myd88 expression is required for strengthening the CD4 CTLs phenotype during the infection.

Moreover, by investigating the presence of a previously published CD4 CTLs gene signature in a mixed bone marrow chimera settings they highlighted a cell intrinsic role for Myd88 in imprinting the signature. The study also identifies Il18R as a myd88 upstream receptor potentially responsible for CD4 CTLs development by showing that lack of IL18R phenocopied myd88 deficiency in failing to promote a CD4 CTLs phenotype.

Finally, by showing the direct correlation between perforin expressing CD4 T cells in Chagas infected individuals and parameters of heart disfunction the authors hinted at a possible involvement of CD4CTLs in a clinical setting.

-The core finding of the paper, providing the first evidence of CD4 CTLs development in a mouse model of intracellular parasite is well supported by the data. The expression of markers correlated to CD4 cytotoxicity in other settings and gene signatures fits well the phenotype described and suggests possible common features for CD4 CTLs development across infection with different pathogens.

This manuscript will boost the knowledge over the involvement of non canonical CD4 types in the immune responses to parasites. Moreover the finding that CD4 CTLs are the predominant phenotype in organs importants for viral replication imply an involvement of these cells in the development of the pathology that will have to be taken into accounts in future studies.

• The understanding of the parental relationship beteween CD4CTLs and Th1 remains unclear and it's complicated by the low numbers of IFNg (regarded as an hallmark of functional Th1) producing CD4 T cells detected in the model. IFN-g production by CD4 is lower than 10% even when achieved by PMA/Iono stimulation and half of Gzb+ CD4 stain positive for the cytokine. On the other hand the putative transcription factor of Th1 development, Tbet, is expressed by all Gzb positive CD4s. This discrepancy and the low number of IFNG+ should be better discussed by the authors.

First, we would like to thank Reviewer #3 for the constructive criticism on our manuscript. Regarding the apparent discrepancy on the frequencies of IFN-g+ and Tbet+ CD4+ T cells in our model, please first note that the percentage of IFN-g+ CD4+ T cells detected in the present study is comparable to the ones found in the spleen of mice infected with the same or similar strains of T. cruzi and reported by other groups (please see our complete answer to Reviewer #1 on this topic). With this remark done, we think that the apparent discrepancy between the expression of T-bet and the low fraction of GzB+CD4+ T cells producing IFN-g is a very interesting question. It is known that T-bet is a key transcription factor associated with the development of IFN-g-producing CD4+ T cells and that it also coordinates the expression of multiple other genes in CD4+ T cells and in other cell types. Also, T-bet can interact with other proteins, resulting in the induction or inhibition of key factors in T cell differentiation (reviewed in Hunter, 2019, Nat. Rev. Immunol, 19:398). Importantly, it has been shown that during the late stages of Th1 cell activation, T-bet recruits the transcriptional repressor Bcl-6 to the Ifng locus to limit IFNg transcription (Oestreich, 2011, JEM, 208:1001) Therefore, T-bet action is not limited to transactivation of the Ifng gene, but can also act as part of a negative-feedback loop to limit IFN-g production in certain cells. We do not believe that Bcl-6 is playing a role in CD4+GzB+ T cells in our model, since we found that the majority of CD4+GzB+ T lymphocytes express Blimp-1 (Figure 5D), and Blimp-1 and Bcl-6 are known to be reciprocally antagonistic transcription factors.

However, the possibility remains that another repressor factor is downregulating Ifng gene transcription in the majority of T-bet+ CD4+GzB+ T cells, with the participation of T-bet or not. Of note, Blimp-1 was shown to be a critical regulator for CD4 T cell exhaustion during infection with T. gondii, and CD4+ T cells deficient in Blimp-1 produced higher levels of IFN-g in infected mixed-bone marrow chimeric mice reconstituted with WT and Blimp-1 conditional knock-out cells (Hwang, S., 2016, JEM 213:1799). Furthermore, Blimp-1 attenuates IFN-g production in CD4 T cells activated under nonpolarizing conditions and chromatin immunoprecipitation showed that Blimp-1 binds directly to a distal regulatory region in the Ifng gene (Cimmino, L. et al. 2008, JI 181:2338). We have also shown that, like Blimp-1, Eomes is expressed by around 60% of the GzB+CD4+ T cells (Figure 2G). It is known that Eomes controls the transcription of cytotoxic genes and promotes IFN-g production in CD8+ T cells, binding to the promotor of the Ifng gene. Interestingly, Eomes was also shown to participate in the induction of immunoregulatory/exhaustion receptors, such as PD-1 and Tim-3. Furthermore, deficiency of Eomes led to increased cytokine production (Paley, M.A. et al., 2012, Science 338: 1220). More recently, evidence in favor of the participation of Eomes in the repression of IFN-g production in TCR-gamma-delta T cells was also published (Lino, C. et al.,2017, EJI 47:970). Therefore, these studies indicate the complex control of Ifng gene, in which T-bet, Eomes, Blimp-1 and possible other TFs might play concerted roles. We think it would be interesting to investigate the role of Eomes and/or Blimp-1 in the repression of the Ifng gene in GzB+CD4+ T cells. Kinetics studies on the expression of these TFs, may contribute for the better understanding of the parental relationship between CD4CTLs and Th1 cells, a fundamental question, not completely understood yet. A comment on this subject was included in the revised manuscript.

On the same note, while the confirmation of a CD4 CTLs gene signature in the model is very convincing, it must be noted that the one used as a reference was obtained by performing single cell RNA seq , taking into account only IFNg+ CD4 cells and then comparing Gzb+ and Gzb- negative in the setting. The authors are instead using bulk RNA seq and comparing populations of cells that would have none VS low levels of Th1. In this view, while the confirmation of the CD4 CTLs signature is striking, addressing the relative relationship with Th1 cells is complicated. Using Gzb YFP reporters in the setting could help improving the resolution between the 2 subsets.

Our analysis clearly demonstrated the presence of the CD4CTL signature among WT CD4+ T cells, and its absence among Myd88-/- CD4+ T cells from the same mixed-BM chimeric mice. Together with our past work (Oliveira, 2017) and results included in the present manuscript, this analysis strongly contributes to demonstrate the importance of T-cell intrinsic IL-18R/MyD88 signaling for the development of a robust CD4CTL response to infection with an intracellular parasite. Although these results argue in favor of a common origin for CD4CTLs and Th1 cells during infection, an interesting point is that Ifng-/- mice display the same percentage of GzB+CD4+ T cells as WT mice (Figure 4B), suggesting that GzB+CD4+ T cells might emerge independently of IFN-gdependent Th1 cells. Therefore, the possibility remains that not all CD4CTLs are derived from the putative terminal differentiation of Th1 cells but that, instead, a divergence between the Th1 and CTL differentiation programs might occur at an earlier step. Although addressing this fundamental question goes beyond the possibilities of the present study, we believe that our results bring an important and substantial contribution for the understanding of the biology of CD4CTLs in response to infection and highlights the importance of IL-18R/MyD88 signaling for the reinforcement and/or stabilization of CD4+ T cell commitment into the CD4CTL phenotype. Regarding the use of GzB-YFP reporters, please see our answer below.

• The dependancy on the Myd88/IL18r axis to promote CD4 CTLs is well characterized and the prolonged survival rate of IL18r-/- after the adoptive transfer of Gmb YFP+ CD4 is very convincing. However instead of using PBS as control the authors could have used YFP- or total CD4 cells for the task. While in previous publication it was already showed that protection was achieved by transferring the total CD4 population; comparing GzB + VS GzB- would have added useful insights over the amount of protection conferred by the subtypes and relative roles of CD4 CTLs and Th1 in the model. Parasitemia could also be reassessed in this view.

We have already discussed the impossibility of sorting bona-fide GzB-negative cells from the reporter mouse strain available. Please see our complete answer to Reviewer 2 on this issue (iii) in this point-by-point letter. Moreover, due to the low percentage of GzB-EYFP cells labeled in the tamoxifen-treated reporter mice, a high number of mice is necessary for performing these adoptive transfer experiments. Unfortunately, due to the COVID-19 pandemic and its consequences on our animal facility, at present it is impossible to repeat this experiment including total CD4+T cells within a reasonable time. However, we have already shown in our past study (Oliveira, 2017), that the transfer of total WT CD4+T cells to Il18ra-/- mice, increased survival and lowered parasite load. On the other hand, our current data demonstrate that the adoptive transfer of GzB+CD4+ T cells increases survival but does not change the parasite load (Figure 6G). Therefore, these data strongly support that GzB+CD4+ T cells act in an IFN-g-independent way and, hence, differ from Th1 in the effector mechanism employed for extending survival of the recipient mice. In summary, our results favor the notion that CD4CTLs and Th1 cells have complementary roles, both being able to extend survival of recipient mice, although only Th1 are effective in lowering parasite load.

Author Response

Reviewer #1 (Public Review):

The results are quite interesting and potentially have important therapeutic implications. Nevertheless, in the current form there are several weaknesses that diminish the strength of the findings.

1) As the authors note, they do not provide direct evidence for the ultimate conclusion of the study that assembly with β2a and β2e subunits are necessary for CaV2.3 channels to contribute to pacemaking in SN DA neurons. The authors state siRNA knockdown experiments in SN DA neurons are technically challenging. Nevertheless, shRNA knockdown studies in SN neurons have been previously published. Such a study is critical to provide direct evidence for what would be a very important and impactful finding.

Please refer to our detailed response to essential revision 1 above.

2) Relative contribution of CaV1.3 (L‐type) and CaV2.3 channels to pacemaking in SN DA neurons. As the authors note, a phase III clinical trial for the L‐type channel blocker, isradipine, showed no efficacy for neuroprotection, even though some mice studies suggested this might be efficacious. On the other hand, the authors' previous work with CaV2.3 knockout mice suggest inhibition of this channel would be more appropriate for a neuroprotective response. It would be useful to get a direct comparison of the impact of isradipine and SNX‐482 on pacemaking in SN DA neurons (Figs. 1 and 2). If their impacts on pacemaking (and Ca2+ oscillations) are similar it would suggest something beyond the pacemaking Ca2+ influx could be responsible for neuroprotection (e.g. changes in NCS‐1 expression as previously suggested by the authors).

The question about the relative contribution of Cav1.3 and Cav2.3 on pacemaking is complex due to the finding that different results have been obtained regarding the role of L‐type channels on pacemaking. In Cav1.3 knockout mice pacemaking frequency is normal (7, 8). Inhibition (of Cav1.2 and Cav1.3) by dihydropyridine Ca2+ channel inhibitors (e.g. isradipine, nimodipine) was found to inhibit pacemaking in some (e.g. 9‐11) but not in all (8, 12) reports. This seems to be dependent on experimental conditions, but the reasons for these discrepancies are currently unclear. Similarly, we find inhibition of pacemaking by SNX‐482 in cultured midbrain neurons (this paper) but, as previously reported, not in Cav2.3‐deficient mice (1). While this toxin is well suited to isolate Cav2.3‐mediated Ca2+ current components, effects on pacemaking in DA neurons have to be interpreted with more caution because (as clearly outlined in our original MS and our previous paper, 1), SNX‐482 is also a potent inhibitor of Kv4.3 channels. We consider this limitation even more in the discussion of SNX‐482 effects on pacemaking in cultured neurons (data now moved to Suppl Fig. 5) in the revised MS (end of page 15, top of page 16), although the SNX‐482 changes suggest an involvement of Cav2.3 for AP generation.

Although we acknowledge the relevance of the question raised by the reviewer, based on our previous findings (1) the absence of an obvious role of Cav2.3 for pacemaking in SN DA neurons (despite their role for Ca2+ transients) as an experimental read‐out prevents a straightforward approach to study the contribution of different β‐subunits and their splice variants for this process.

3) The slice recording data (Fig. 9) are confusing and raise concerns about adequacy of pharmacological isolation of CaV2.3 currents in this preparation. The accuracy of interpretation of the data in Fig. 9 rests critically on the idea that the cocktail of CaV channel blockers given successfully isolates CaV2.3 currents. Yet, the amplitudes of the exemplar currents shown for plus or minus the CaV channel blocker cocktail are almost the same. This cannot be due to CaV2.3 providing the dominant current in the slice preparation since addition of SNX‐482 only decreased Ca2+ current amplitude by 13% (Suppl Fig. 5). It is not clear to me why the steady‐state activation and inactivation curves experiments were not conducted in the cultured neuron preparation (Figs. 1 and 2) where there seems to be better control of pharmacological block of different Cav channel isoforms.

We have now performed the isolation of SNX‐482sensitive currents not only in the cultured neuron preparation as suggested but, in addition, also in SN DA neurons. The latter experiments gave essentially identical steady‐state inactivation parameters as compared to our "R‐type" current (current remaining in the presence of all other channel blockers). This now also allows a direct comparison of SNX‐482‐sensitive current properties in cultured neurons and in slices (see response above). We now also specifically discuss previous reports of SNX‐482‐sensitive Rtype components in the introduction to allow comparison of these reports with our findings. Please also note that in our legend to Fig. 9A (original MS, now Fig. 6) we have explicitly stated that recordings of "similar amplitudes were chosen" to facilitate comparison of current kinetics. We still think that this makes sense and kept this part of the figure but now strengthened this point even more in the figure legend (Fig. 6).

4) While the transcript data show that β2a and β2e are present in SN DA neurons, numerically they would still represent only a minority of the beta subunits present (<25%). I don't think sufficient thought has been given to this in the discussion of the results. Unless there is some preferential association of CaV2.3 with β2a and/or β2e, there would be a mix of channels with the majority incapable of supporting pacemaking in SN DA neurons. Given this, one would not necessarily expect that the gating characteristics of CaV2.3 would be the same as what is obtained with reconstituted channels in tsA201 cells where all the channels are assembled with β2a or β2e (see point #5 below).

We now give this important point more thought in the discussion and mention that our data would imply such a preferential association of Cav2.3 with β2a and/or β2e and provide possible explanations. In addition, as in the original MS, we also provide alternative interpretations (Discussion, pg 14, 2nd and 3rd paragraph).

5) The V0.5,inact of putative CaV2.3 channels in SN DA neurons of ‐52.4 mV was said to be 'very similar' to the value of ‐40 mV that was observed in tsA201 cells. A difference of +12 mV in voltage‐dependence gating of ion channels is substantial and should not be brushed off. A more nuanced interpretation would be that in SN DA neurons CaV2.3 likely associates with other beta subunits in addition to b2a and b2e and so one would not necessarily expect the V0.5,inact to be the same as what is observed in reconstituted channels in tsA201 cells.

The V0.5,inact of ‐52.4 mV refers to the control current. We correctly stated that the V0.5,inact of R‐type current was ‐47.5 mV (as also shown in Table 3), i.e. only about 7 mV more negative than in tsA‐cells. We now rephrased this chapter because we also included the new data with inactivation data of SNX‐482sensitive currents in cultured neurons and in SN DA neurons recorded in slices (Discussion, page 13, 2nd paragraph). We do not refer to "'very similar" (difference ~5 mV) values anymore as suggested.

Reviewer #2 (Public Review):

This reviewer is very enthusiastic about the work but notes that most of the conclusions are based on data obtained by overexpressing Cav2.3 and accessory subunits in a heterologous expression system. The authors make a good argument for cross‐correlation between data in tsA‐201 cells and dopaminergic neurons, but it is unclear that the results will translate from one system to another. More data may be needed to do so (the reviewer does understand that these are challenging experiments), which the authors acknowledge in a section about the study's limitations. Based on this, it seems that the title is misleading without additional data supporting the role of Cav2.3 in dopaminergic neurons. Along the prior line, statements linking the study results to potential pathological implications seem a big stretch not supported by current data, and therefore should be eliminated.

An issue with this manuscript is that the narrative and organization of the data are difficult to follow. The reviewer understands that the authors are weaving a complex story that involves using multiple techniques and approaches. Still, the way the data is organized and described makes the reader go back and forward to compare and contrast results constantly. This is further complicated by the fact that some experiments are done in dopaminergic neurons and others in tsA‐201 cells (the identity of the cell type used should be made clearer), the order of some figures is not appropriate (Supp Fig 1 for example) and some figure panels are not discussed (Supp Fig 5E to 5J).

The MS has been completely rewritten, based on the additional SNX‐482experiments we have now performed both in the cultured DA neurons as well as in the midbrain slices. We therefore also moved data on effects on the spontaneous activity of cultured neurons by SNX‐482 into the supplement to make the key results easier to follow. The identity of neurons is indicated in all headers of table and figure legends to identify cell types. We also changed the title to “β2‐subunit alternative splicing stabilizes Cav2.3 Ca2+ channel activity during continuous midbrain dopamine neuronlike activity” to attenuate our previous statement regarding a role in dopaminergic midbrain neurons.

Author Response

Reviewer #1 (Public Review):

As we lack empirical data of the response of most species to environmental changes, developing predictive tools based on traits that are easier to access or infer may help us developing better management tools. This is the case even for terrestrial mammals, a rather well studied group but with a large study bias towards temperate Europe and North America. This study uses maximum longevity, litter size and body mass to predict the sign and size of the relationships between annual temperature and precipitation anomalies and population growth rates, using the Living Planet database for times series of abundance and Chelsa for weather anomalies. The authors use a Bayesian framework to relate the size and absolute magnitude of the relationships between detrended population growth rates and weather anomalies, the framework accounting for the uncertainty in estimates as well as phylogenetic dependencies. They did not find any systematic effects -- on average the slopes of the relationships were close to 0 -- but the magnitude of the coefficients decreases for species with high maximum longevity and low litter size. Therefore, this study points to possible predictions of the magnitude of the response to weather variability using simple demographic indices such as longevity and litter size. The study has clear limitations that are common to similar "meta-regressions" using publicly available databases, but they are not ignored when discussing the results. One would hope that such limitations would lead to improving the quality of such databases, both in terms of taxonomic and geographic coverage as well as quality of data.

We would like to thank Reviewer 1 for their overall positive feedback and constructive comments on the method and our predictions. We have now included complementary analyses based on high-quality subsets (≥ 20-year records; using life history traits estimated from structured population models), have clarified our set of hypotheses and discussed our results accordingly. Detailed responses are given below.

I would like to challenge the authors in terms of why one would expect relationships of a given sign or magnitude. First with respect to sign of relationships, even for the same species and the same weather parameters, one could expect different signs depending on where the study is done with regards to the climatic niche. If one is close to the warm (or wet) edge, any positive temperature (or precipitation) anomalies would probably have a negative effect, but the reverse would happen when close to the cold or dry edge. There are studies showing such demographic and growth rate variability differences. I find therefore hard to interpret the sign of such weather anomalies and what it tells us about the "effect" of weather variability.

We think that this is an important point to discuss with respect to the importance of within-species variability in population dynamics. Certainly, from the results L203-206 it is clear that populations of the same species can have responses of differing signs. It is also interesting to note that this may be the result of a population’s position in the climatic niche. However, aside from exploring this for species with long-term demographic monitoring across the range, we do not feel that exploring this was in the scope of the current study across species. We agree fully however that adding this perspective to studies of how populations are responding to changing climates is critical. As well as the paper mentioned below by Gaillard et al. (2013), recent work in Plantago lancelota with extensive spatial replication has also begun to reveal these within-range dynamics as a function of latitudinal or climatic gradients (Römer et al. 2021). We have added further discussion of this to the manuscript L330-340. We believe that this point adds to the context of our results highlighting variability within-species. In addition, we have clarified in the introduction that no clear directional responses of populations to weather anomalies was expected among and within species L133-135.

Römer, G., Christiansen, D. M., de Buhr, H., Hylander, K., Jones, O. R., Merinero, S., ... & Dahlgren, J. P. (2021). Drivers of large‐scale spatial demographic variation in a perennial plant. Ecosphere, 12(1), e03356.

Second with regards to the magnitude, it is clear that the maximum growth rate is strongly linked to maximum longevity and litter size -- slow species have a much lower maximum rate of growth than fast species. So, one would expect that variability of population growth rates is larger in fast species than slow species, and therefore the magnitude of their response to environmental variability. Now the question might also be whether weather variability explains a smaller or larger proportion of the variability in population growth rates -- that is, does weather have a relatively larger influence in fast species than slow species? You might have the answer but with the multiple standardizations of the response and predictor variables it is not obvious (that is, when you standardize the response and predictor variables, coefficients are correlations, but this is across species, not for a given population).

The reviewer raises a very interesting and important point on whether the patterns we observe are simply a result of larger variability in growth rates in short-lived species. We have two responses to this point: 1) while there is indeed larger variation in the population growth rates of short-lived species, we believe that this variability is likely an evolved life-history strategy in response to the environment, and thus a key component of patterns we observe, 2) we also feel that our use of models that included annual effects, and state-space models with explicit process-noise terms, account for any confounding effect of this variation.

To address the first point in more detail, we expect that life-histories (and thus population dynamics) are evolved responses to the environment (Stearns, 1992). For ‘fast’ organisms therefore, their intrinsic life-history strategy results in boom-bust population dynamics relative to ‘slow’ species. This is clearly observable in transient or non-asymptotic dynamics, where short-lived species more often have short-term population dynamics with a greater magnitude (Stott et al. 2011). On this point, we therefore argue that this variation in population growth is part of what we are trying to capture. Anomalies in the weather are therefore expected to act more strongly in ‘fast’ species. Following this point and the comments of Reviewer #3, we have now included more explicit hypotheses in terms of life-history L133-144.

For the second point, while we may expect this variability to be the result of dynamics we are trying to capture, this does not preclude other sources of variation in population size confounding the patterns we could observe. For example, hunting pressure may influence both short-term population variability and long-term trends. As a result, we aimed to capture this residual variation using auto-regressive terms for year in our GAMs. While these terms do not explicitly model variability in population growth, they do account for a component of the trend, with variation (error around the trend, which is expected to be larger for fast species), and auto-regressive components of population change. Moreover, we did additional analyses using a state-space modelling approach. In the state-space approach, process noise, which in our case would equate to variability in population growth, is explicitly modelled and accounted for. We therefore believe that our analyses account for residual variability in population growth rates. State space models were also highly correlated with our auto-regressive GAMs, and we can therefore conclude that we do not expect that this variability influences our findings. We have now asserted this in the Methods section L531-535.

Stearns, S.C., 1992. The evolution of life histories (No. 575 S81).

Stott, I., Townley, S. and Hodgson, D.J., 2011. A framework for studying transient dynamics of population projection matrix models. Ecology Letters, 14(9), pp.959-970.

Your analyses remove trends -- that is, climate or other systematic change as opposed to weather anomalies (yearly differences) -- and trends might be the main concerns in terms of conservation. This is made clear in the discussion but perhaps not as much in the introduction where you seem to focus on climate change (the title reflects this well, however, as you mention weather, not climate). This confusion between weather and climate is often made in the literature, when reference is made to climate effects rather than weather effects.

We agree with the reviewer that climate and weather are often conflated in ecological studies. We apologise for this oversight in the introduction, and agree that the narrative and link to weather was not made explicit in the previous version. Following this point and the suggestions of Reviewer #3, we have now restructured large sections of the introduction to improve the clarity of our hypotheses. To address this point, we have now included specific introduction of different components of climate that species populations may respond to, including short-term extreme weather patterns as we explore in this study. Please find this revised section L80-97.

Finally, I would like to see a measure of how good is the prediction you can make using traits. You may have "significant effects" but not helping much in terms of prediction (see PB Adler et al. 2011 in Science, for an example with species richness and productivity).

On this point we disagree with the reviewer. The core of our analysis framework was to examine the predictive performance of models. We do not report any significant effects, and instead use Bayesian inference. Throughout the analysis framework, we used explicit tests of out-of-sample predictive performance with leave-one-out cross validation (Vehtari et al. 2017). This is asserted in the manuscript title and results section when introducing our spatial analysis L188-191. Cross validation was combined with model selection to test the predictive performance of a set of candidate models with respect to base models excluding predictors of interest. This predictive performance framework was not applied to examine the directional effects (question 1), as these models did not contain key predictors. However, model selections using predictive performance were done throughout questions 2 and 3, to explore spatial and life-history effects. We highlight this point in both the results L188-191 and methods sections L608-615. In the case of life-history, we found that relative to the base model, out-of-sample predictions were improved when including univariate life-history traits relative to the base model, and thus life-history traits aid in predicting weather responses.

We did not explore the relative predictive performance of life-history traits with respect to other traits such as dietary specialisation, which have been shown to be important in climate responses (Pacifici et al. 2017). We believe that this would have been out of scope for the purpose of the current study, where we aimed to test specific hypotheses established in life-history theory.

Pacifici, M., Visconti, P., Butchart, S.H., Watson, J.E., Cassola, F.M. and Rondinini, C., 2017. Species’ traits influenced their response to recent climate change. Nature Climate Change, 7(3), pp.205-208.

Vehtari, A., Gelman, A. and Gabry, J., 2017. Practical Bayesian model evaluation using leave-one-out cross-validation and WAIC. Statistics and computing, 27(5), pp.1413-1432.

Reviewer #2 (Public Review):

Jackson et al. present a global analysis of the effects of life history on the response of terrestrial mammal populations to weather, showing that litter size and longevity significantly alter how populations respond to anomalies in temperature and rainfall. The topic is highly interesting, as it has implications for what data we should monitor to make more reliable predictions about species' responses to climatic change, and how we should prioritise which species to conserve by identifying those which might be at greatest risk.

The authors comprehensively validate their results with substantial secondary analyses, and I believe that their assertions are supported by the results presented here. Whilst global scale analyses such as this provide useful generalities, they should be taken as that: an investigation of the general trends observed across large spatial scales, and caution should be taken extrapolating too far away from the species which have been analysed for this study.

We thank the reviewer for their positive feedback, and agree with not drawing too many generalities from our findings. In the first paragraph of the discussion L253-262, we now explicitly refer to the results in the context of mammal population-dynamics/conservation.

Reviewer #3 (Public Review):

In this study, the authors aim to investigate how mammalian species are likely to respond to climate change. To this end, they investigate the effects of weather anomalies on the growth rates of mammalian populations. They use long-term population records for 157 terrestrial mammals from the Living Planet database. They explore three different questions using a two-step modelling approach: (1) whether temperature and precipitation anomalies have significant effects on population growth rates across species; (2) whether responses differ among species and biomes; and (3) whether life-history traits explain species responses to weather anomalies.

The work undertaken in this manuscript is of broad appeal in the field and has the potential to inform conservation. Overall, the methodology is sound and the modelling framework robust; the authors took care to test the robustness of their models by fitting alternative sets of models. The two-step design of this study is interesting and the choice of the study system is relevant for the questions the authors aim to tackle. The authors also paid attention to some important points that are at times overlooked such as resolving taxonomy before running their analyses. I also appreciated the fact that the authors made their code available.

We thank the reviewer for their positive feedback on the manuscript, which highlights many of our key goals with the paper.

I nevertheless think that, in its present form, the main weakness of this manuscript is the clarity of the writing, the framing of the study and the overall flow. I found the manuscript at times a bit difficult to follow. That said, I think there is much scope for the authors to improve it. First, I think the work would benefit from better explanation of the underlying hypotheses. Second, in some places I think the authors go into a lot of details at the expense of clarity. As such, I think the authors should strive to better balance clarity with detailed information (notably in the results and methods; adding summary sentences, for example, could help clarify these sections). Third, I think there is room for improvement in the narrative and the flow of the introduction and the discussion. Finally, I think stronger justifications are sometimes required regarding specific points of the analysis.

I believe that the conclusions of this work are supported by the data and the analyses, and think they are of interest and relevant to the field. However, I think the discussion should highlight the main limitations of the study. In particular, I think the biases in the data should be discussed, and notably whether these biases are expected to affect the results (and if so, in what way).

To conclude, I think that beyond the aforementioned weaknesses of this study, the results and the methods are of interest for the field. I think the modelling framework is applicable to other study systems and relevant to the field as well.

We warmly thank the reviewer for their positive words and thorough constructive feedback. We have extensively re-worked large sections of the manuscript (particularly the discussion and introduction) based on these points, and done our best to address all of them. Generally, we have strived to improve the clarity and succinctness of the manuscript.

Author Response

Reviewer #1 (Public Review):

In this study, Guggenmos proposes a process model for predicting confidence reports following perceptual choices, via the evidence available from stimuli of various intensities. The mechanisms proposed are principled, but a number of choices are made that should be better motivated - I develop below a number of concerns by order of importance.

I’d like to thank the reviewer for their thorough and excellent review. It’s no set phrase that this review substantially improved the manuscript.

1) Lack of separability of the two metacognitive modules.

Can the author show that the proposed model can actually discriminate between the noisy readout module and the noisy report module? The two proposed modules have a different psychological meaning, but seem to similarly impact the confidence output. Are these two mutually exclusive (as Fig 1 suggests), or could both sources of noise co-exist? It will be important to show model recovery for introducing readout vs. report at the metacognitive level, e.g., show that a participant best-fitted by a nested model or a subpart of the full model, with a restricted number of modules (some of the parameters set to zero or one), is appropriately recovered? (focusing on these two modules) This raises the question of how the two types of sigma_m are recoverable/separable from each other (and should they both be called sigma_m, even if they both represent a standard deviation)? If they capture independent aspects of noise, one could imagine a model with both modules. More evidence is needed to show that these two capture separate aspects of noise.

Testing the separability of the two noise types (readout, report) is a great idea and I have now performed a corresponding recovery analysis. Specifically, I have simulated data with both noise types for different regimes of sensory and metacognitive noise. As shown in the new Figure 7—figure supplement 6, the noise type can be precisely recovered in the most typical regimes.

I now refer to this analysis in the subsection 2.4 Model recovery (Line 521ff):

“One strength of the present modeling framework is that it allows testing whether inefficiencies of metacognitive reports are better described by metacognitive noise at readout (noisy-readout model) or at report (noisy-report model). To validate this type of application, I performed an additional model recovery analysis which tested whether data simulated by either model are also best fitted by the respective model. Figure 7—figure supplement 6 shows that the recovery probability was close to 1 in most cases, thus demonstrating excellent model identifiability. With fewer trials per observer, recovery probabilities decrease expectedly, but are still at a very good level. The only edge case with poorer recovery was a scenario with low metacognitive noise and high sensory noise. Model identification is particularly hard in this regime because low metacognitive noise reduces the relevance of the metacognitive noise source, while high sensory noise increases the general randomness of responses.”

In principle, both noise modules can co-exist and model inversion should be possible (though mathematically more complicated). On the other hand, I anticipate that parameter recovery would be extremely noisy in such a scenario. For this work, I decided to not test this possibility as it would add a lot of complexity, with a high probability of ultimately being unfeasible.

2) The trade-off between the flexibility of the model (modularity of the metacognitive part, choice of the link functions) and the generalisability of the process proposed seems in favor of the former. Does the current framework really allow to disambiguate between the different models? Or at least, the process modeled is so flexible that I am not sure it allows us to draw general conclusions? Fig 7 and section 3 of the results explain that all models are similar, regardless of module of functions specified; Fig 7 supp shows that half of participants are best fitted by noisy readout, while the other half is best fitted by noisy report; plus, idiosyncrasies across participants are all captured. Does this compromise the generalisability of the modeling of the group as a whole?

This is a fair point and I understand the question has two components: a) is the model too flexible, potentially preventing generalized conclusions? b) is the flexibility of the model recoverable?

Regarding a), I should emphasize that the manuscript (and toolbox) provides a modeling framework, rather than a single specific model. In other words, researchers applying the framework/toolbox must make a number of decisions: which noise type? which metacognitive biases should be considered? which link function? To ensure interpretability / generalizability, researchers have to sufficiently constrain the model. Due to this framework character, it makes sense that the manuscript is submitted under the Tools & Resources Article format rather than the Research Article format.

On the other hand, I agree that it is the duty of the manuscript introducing the framework to provide all necessary information to help the researcher make these decisions. This is where the reviewer’s point b) is critical and I hope that with the new parameter and model recovery analyses in the present revision (see other comments) I meet this requirement to a satisfactory degree.

To clarify the scope and aim of the paper, I now put a new subsection in front of the example application to the data from Shekhar and Rahnev, 2021 (Line 534ff):

“It is important to note that the present work does not propose a single specific model of metacognition, but rather provides a flexible framework of possible models and a toolbox to engage in a metacognitive modeling project. Applying the framework to an empirical dataset thus requires a number of user decisions: which metacognitive noise type is likely more dominant? which metacognitive biases should be considered? which link function should be used? These decisions may be guided either by a priori hypotheses of the researcher or can be informed by running a set of candidate models through a statistical model comparison. As an exemplary workflow, consider a researcher who is interested in quantifying overconfidence in a confidence dataset with a single parameter to perform a brain-behavior correlation analysis. The concept of under/overconfidence already entails the first modeling decision, as only a link function that quantifies probability correct (Equation 6) allows for a meaningful interpretation of metacognitive bias parameters. Moreover, the researcher must decide for a specific metacognitive bias parameter. The researcher may not be interested in biases at the level of the confidence report, but, due to a specific hypothesis, rather at metacognitive biases at the level of readout/evidence, thus leaving a decision between the multiplicative and the additive evidence bias parameter. Also, the researcher may have no idea whether the dominant source of metacognitive noise is at the level of the readout or report. To decide between these options, the researcher computes the evidence (e.g., AIC) for all four combinations and chooses the best-fitting model (ideally, this would be in a dataset independent from the main dataset).”

In addition, the website of the toolbox now provides a lot more information about typical use cases: https://github.com/m-guggenmos/remeta

3) More extensive parameter recovery needs to be done/shown. We would like to see a proper correlation matrix between parameters, and recovery across the parameter space, not only for certain regimes (i.e. more than fig 6 supp 3), that is, the full grid exploration irrespective of how other parameters were set.

The recovery of the three metacognitive bias parameters is displayed in Fig 4, but what about the other parameters? We need to see that they each have a specific role. The point in the Discussion "the calibration curves and the relationships between type 1 performance and confidence biases are quite distinct between the three proposed metacognitive bias parameters may indicate that these are to some degree dissociable" is only very indirect evidence that this may be the case.

A comprehensive parameter recovery analysis is indeed a key analysis that was missing in the first version of the manuscript. I now performed several analyses to address this, rewrote and extended section 2.3 on parameter recovery. The new parameter recovery analysis was performed as follows (Line 455ff):

“To ensure that the model fitting procedure works as expected and that model parameters are distinguishable, I performed a parameter recovery analysis. To this end, I systematically varied each parameter of a model with metacognitive evidence biases and generated data. Specifically, each of the six parameters (σs, ϑs, δs, σm, 𝜑m, δm) was varied in 500 equidistant steps between a sensible lower and upper bound. The model was then fit to each dataset. To assess the relationship between fitted and generative parameters, I computed linear slopes between each generative parameter (as the independent variable) and each fitted parameter (as the dependent variable), resulting in a 6 x 6 slope matrix. Note that I computed (robust) linear slopes instead of correlation coefficients, as correlation coefficients are sample-sizedependent and approach 1 with increasing sample size even for tiny linear dependencies. Thus, as opposed to correlation coefficients, slopes quantify the strength of a relationship. Comparability between the slopes of different parameters is given because i) slopes are – like correlation coefficients – expected to be 1 if the fitted values precisely recover the true parameter values (i.e., the diagonal of the matrix) and ii) all parameters have a similar value range which makes a comparison of off-diagonal slopes likewise meaningful. To test whether parameter recovery was robust against different settings of the respective other parameters, I performed this analysis for a coarse parameter grid consisting of three different values for each of the six parameters except σm, for which five different values were considered. This resulted in 35·51 = 1215 slope matrices for the entire parameter grid.”

In addition, I computed additional supplementary analyses assessing a case with fewer trials, a model with confidence biases, and models with mixed evidence and confidence biases. For details about these analyses, I kindly point the reviewer to section 2.3. Together, these new analyses demonstrate that parameter recovery works extremely well across different regimes and for all model parameters, including the metacognitive bias parameters mentioned in the reviewer’s comment.

1.8: It would be important to report under what regimes of other parameters these simulations were conducted. This is because, even if dependence of Mratio onto type 1 performance is reproduced, and that is not the case for sigma_m, it would be important to know whether that holds true across different combinations of the other parameter values.

I now repeated this analysis for various settings of other parameters and include the results as new Figure 6—figure supplement 2. While the settings of other parameters affect the type 1 performance dependency of Mratio (with some interesting effects such as Mratio > 1), parameter recovery of sigma_m is largely unaffected. The same basic point thus holds: Mratio shows a nonlinear dependency with type 1 performance, but sigma_m can be recovered largely without bias under most regimes (the main exception is a combination of low sensory noise and high metacognitive noise under the noisy-readout model, which is also mentioned in the manuscript).

Is lambda_m meaningfully part of the model, and if so, could it be introduced into the Fig 1 model, and be properly part of the parameter recovery?

I now reworked the part about metacognitive biases to make it more consistent and to introduce lambda_m on equal footing with the other metacognitive bias parameters. I now distinguish between metacognitive evidence biases (the two main bias parameters of the original model, phi_m and theta_m) and metacognitive confidence biases, i.e. lambda_m and a new additive confidence bias parameter kappa_m. The schematic presentation of the model framework in Figure 1 is updated in accordance:

This change also complies with reviewer 2, who rightfully pointed out that the original model framework put much stronger emphasis on bias parameters loading on evidence than on confidence. The metacognitive confidence bias parameters are now also part of the parameter recovery analyses (Figure 7—figure supplement 2).

While it is still feasible to combine the two evidence-related bias parameters and lambda_m – as queried by the reviewer – not all mixed combinations of evidence- and confidence-related bias parameters perform well in terms of model recovery (in particular, combining all four parameters; cf. Figure 7—figure supplement 3). Hence, a decision on the side of the modeler is required. I comment on this important aspect at the end of the section 1.4 about metacognitive biases (Line 276ff):

“Finally, note that the parameter recovery shown in Figure 4 was performed with four separate models, each of which was specified with a single metacognitive bias parameter (i.e., 𝜑m, δm, λm, or Km). Parameter recovery can become unreliable when more than two of these bias parameters are specified in parallel (see section 2.3; in particular, Figure 7—figure supplement 3). In practice, the researcher thus must make an informed decision about which bias parameters to include in a specific model (in most scenarios one or two metacognitive bias parameters are a good choice). While the evidence-related bias parameters 𝜑m and δm have a more principled interpretation (e.g., as an under/overestimation of sensory noise), it is not unlikely that metacognitive biases also emerge at the level of the confidence report (λm, km). The first step thus must always be a process of model specification or a statistical comparison of candidate models to determine the final specification (see also section 3.1).”

4) An important nuance in comparing the present sigma_m to Mratio is that the present model requires that multiple difficulty levels are tested, whereas instead, the Mratio model based on signal detection theory assumes a constant signal strength. How does this impact the (unfair?) comparison of these two metrics on empirical data that varied in difficulty level across trials? Relatedly, the Discussion paragraph that explained how the present model departs from type 2 AUROC analysis similarly omits to account for the fact that studies relying on the latter typically intend to not vary stimulus intensity at the level of the experimenter.

I thank the reviewer for this comment which made me realize that I incorrectly assumed that my model requires multiple stimulus difficulty levels. The only parameter that would require multiple stimulus intensities is the sensory threshold parameter, but for this parameter I already state that it requires additional stimulus difficulties close to threshold (Line 147ff). Otherwise I now made extensive tests that the model works just fine with constant stimuli. My reasoning mistake (iirc) was related to the fact that I fit a metacognitive link function, which I thought would require variance on the x-axis; but of course there is already plenty of variance introduced through noise at the sensory level, so multiple difficulty levels are not required to fit the metacognitive level. I now removed the relevant references to this requirement from the manuscript.

Nevertheless, I agree that it is interesting to perform the comparison between Mratio and sigma_m also for a scenario with constant stimuli. See both the new Figure 6–supplement 1 with constant stimuli, and the (updated) main Figure 6 with multiple stimulus levels for comparison.

The general point still holds also for constant stimuli: Mratio is not independent of type 1 performance. Thus, the observed dependence on type 1 performance is not due to the presence of varying stimulus levels. I now reference this new supplementary figure in Result section 1.8 (Line 389).

5) 'Parameter fitting minimizes the negative log-likelihood of type 1 choices (sensory level) or type 2 confidence ratings (metacognitive level)'. Why not fitting both choices and confidence at the same time instead of one after the other? If I understood correctly, it is an assumption that these are independent, why not allow confidence reports to stem from different sources of choice and metacognitive noise? Is it because sensory level is completely determined by a logistic (but still, it produces the decision values that are taken up to the metacognitive level)?

The decision to separate the two levels during parameter inference was deliberate. I now explain this choice in the beginning of Result section 2 (Line 416ff):

“The reason for the separation of both levels is that choice-based parameter fitting for psychometric curves at the type 1 / sensory level is much more established and robust compared to the metacognitive level for which there are more unknowns (e.g., the type of link function or metacognitive noise distribution). Hence, the current model deliberately precludes the possibility that the estimates of sensory parameters are influenced by confidence ratings.”

Indeed, I would regard it as highly problematic if the estimates of sensory parameters were influenced by confidence ratings, which are shaped by a manifold of interindividual quirks and biases and for which computational models are still in a developmental stage. Yet, from a pure simulation-based parameter recovery perspective, in which the true confidence model is known, using confidence ratings would indeed make sensory parameter estimation more precise (because of the rich information contained in continuous confidence ratings which is lost in the binarization of type 1 choices).

6) Fig 4 left panels: could you clarify the reasoning that due to sensory noise, overconfidence is expected, instead of having objective and subjective probability correct aligning on the diagonal? Shouldn't the effects of sensory noise average out? In other words, why would the presence of sensory noise systematically push towards overconfidence rather than canceling out on average?

As an intuitive explanation consider the case that no signal is present in a stimulus, e.g., a line grating in a clockwise/counterclockwise orientation discrimination task with an angle of 0 degrees. Since there is no true information in the stimulus, type 1 performance will be at chance level irrespective of sensory noise.

However, sensory noise matters for the metacognitive level. Assuming no sensory noise (i.e., sigma_s = 0), the observer’s stimulus/decision variable would be zero and thus confidence would be zero. Thus, confidence would exactly match type 1 performance. Yet, assuming the presence of sensory noise, the stimulus estimate (“decision value”) will be always different from point-zero, if ever so slightly. While the average estimate of the stimulus variable across trials will indeed cancel out to zero, each individual trial will be different from zero (in either direction) and hence also the confidence will be different from zero in each trial. Since confidence is unsigned, the average confidence will be greater than zero and thus give the impression of an overconfident observer.

Note that this explanation was implicitly included in the paragraph on the 0.75 signature of confidence (“When evidence discriminability is zero, an ideal Bayesian metacognitive observer will show an average confidence of 0.75 and thus an apparent (over)confidence bias of 0.25. Intuitively this can be understood from the fact that Bayesian confidence is defined as the area under a probability density in favor of the chosen option. Even in the case of zero evidence discriminability, this area will always be at least 0.5 − otherwise the other choice option would have been selected, but often higher.”, Line 257ff).

7) The same analysis as Fig 6 but for noisy readout instead of noisy reports do not show the same results: both sigma_m and m-ratio vary as a function of type 1 performance. Does this mean that the present model with readout module does not solve the issue of dependency upon type 1 performance?

I refer to this in the Result section: “The exception is a regime with very high metacognitive noise and low sensory noise under the noisy-readout model, in which recovery becomes biased” (Line 391ff). Indeed, the type 1 performance dependency of sigma_m recovery in this edge case is not as good as in the noisyreport model. However, note that recovery is stable across a large range of d’ including the range typical aimed for in metacognition experiments (i.e., medium performance levels to ensure sufficient variance in confidence ratings).

It is also important to point out that a failure to recover true parameters under certain conditions is not a failure of the model, but a reflection of the fact that information can be lost at the level of confidence reports. For example, if sensory noise is very high, the relationship between evidence and confidence becomes essentially flat (Figure 3), producing confidence ratings close to zero irrespective of the level of stimulus evidence. It becomes increasingly impossible to recover any parameters in such a scenario. Vice versa if sensory noise is extremely low, confidence ratings approach a value of 1 irrespective of stimulus evidence, and the same issue arises. In both cases there is no meaningful variance for an inference about latent parameters. This issue is more pronounced in the noisy-readout case because it requires an inversion of precisely the relationship between evidence and confidence.

8) In Eq8, could you explain why only the decision values consistent with the empirical choice are filtered. Is this an explicit modeling of the 'decision-congruence' phenomenon reported elsewhere (eg. Peters et al 2017)? What are the implications of not keeping only the congruent decision values?

I apologize, this was a mistake in the manuscript. The integration is over all decision values, not just those consistent with the choice. I corrected it accordingly.

Reviewer #2 (Public Review):

This paper presents a novel computational model of confidence that parameterises links between sensory evidence, metacognitive sensitivity and metacognitive bias. While there have been a number of models of confidence proposed in the literature, many of these are tailored to bespoke task designs and/or not easily fit to data. The dominant model that sees practical use in deriving metacognitive parameters is the meta-d' framework, which is tailored for inference on metacognitive sensitivity rather than metacognitive biases (over- and underconfidence). This leaves a substantial gap in the literature, especially as in recent years many interesting links between metacognitive bias and mental health have started to be uncovered. In this regard, the ReMeta model and toolbox is likely to have significant impact on the field, and is an excellent example of a linked publication of both paper and code. It's possible that this paper could do for metacognitive bias what the meta-d' model did for metacognitive sensitivity, which is to say have a considerable beneficial impact on the level of sophistication and robustness of empirical work in the field.

The rationale for many of the modelling choices is clearly laid out and justified (such as the careful handling of "flips" in decision evidence). My main concern is that the limits to what can be concluded from the model fits need much clearer delineation to be of use in future empirical work on metacognition. Answering this question may require additional parameter/model recovery analysis to be convincing.

I thank the reviewer for these encouraging and constructive comments!

Specific comments:

• The parameter recovery demonstrated in Figure 4 across range of d's is impressive. But I was left wondering what happens when more than one parameter needs to be inferred, as in real data. These plots don't show what the other parameters are doing when one is being recovered (nor do the plots in the supplement to Figure 6). The key question is whether each parameter is independently identifiable, or whether there are correlations in parameter estimates that might limit the assignment of eg metacognitive bias effects to one parameter rather than another. I can think of several examples where this might be the case, for instance the slope and metacognitive noise may trade off against each other, as might the slope and delta_m. This seems important to establish as a limit of what can be inferred from a ReMeta model fit.

This is an excellent point and was also raised by reviewer #1. See major comment 3 of reviewer #1 for a detailed response. In short, I now provide comprehensive analyses that demonstrate successful parameter recovery across different regimes and both noisy types (noisy-readout, noisy-report). See Figure 7.

Regarding the anticipated trade-offs between the confidence slope (now referred to as multiplicative evidence bias) and metacognitive noise / delta_m (now additive evidence bias), there is a single scenario in which this becomes an issue. I describe this in the Results section as follows (Line 480ff):

“Here, the only marked trade-off emerges between metacognitive noise σm and the metacognitive evidence biases (𝜑m, δm) in the noisy-readout model, under conditions of low sensory noise. In this regime, the multiplicative evidence bias 𝜑m becomes increasingly underestimated and the additive evidence bias δm overestimated with increasing metacognitive noise. Closer inspection shows that this dependency emerges only when metacognitive noise is high – up to σm  0.3 no such dependency exists. It is thus a scenario in which there is little true variance in confidence ratings (due to low sensory noise many confidence ratings would be close to 1 in the absence of metacognitive noise), but a lot of measured variance due to high metacognitive noise. It is likely for this reason that parameter inference is problematic. Overall, except for this arguably rare scenario, all parameters of the model are highly identifiable and separable.” In my experience, certain trade-offs in specific edge cases are almost inescapable for more complex models. Overall, I think it is fair to say that parameter recovery works extremely well, including the ‘trinity’ of metacognitive noise / multiplicative evidence bias / additive evidence bias.

• Along similar lines, can the noisy readout and noisy report models really be distinguished? I appreciate they might return differential AICs. But qualitatively, it seems like the only thing distinguishing them is that the noise is either applied before or after the link function, and it wasn't clear whether this was sufficient to distinguish one from the other. In other words, if you created a 2x2 model confusion matrix from simulated data (see Wilson & Collins, 2019 eLife) would the correct model pathway from Figure 1 be recovered?

Great point. I introduced a new subsection 2.4 “Model recovery”, in which I demonstrate successful recovery of noisy-readout versus noisy-report models. See also my response to the first comment of Reviewer #1, which includes the new model recovery figure and the associated paragraph in the manuscript. The key new figure is Figure 7—figure supplement 6.

• Again on a similar theme: isn't the slope parameter rho_m better considered a parameter governing metacognitive sensitivity, given that it maps the decision values onto confidence? If this parameter approaches zero, the function flattens out which seems equivalent to introducing additional metacognitive noise. Are these parameters distinguishable?

Indeed, the parameter recovery analysis shows a slight negative correlation between the slope parameter (now termed multiplicative evidence bias) and metacognitive noise (Figure 7). As the reviewer mentions, this is likely caused by the fact that both parameters lead to a flattening /steepening of the evidenceconfidence relationship. For reference, in the empirical dataset by Shekhar & Rahnev, the correlation between AUROC2 and the multiplicative evidence bias is almost absent at r = −0.017. Critically, however, while an increase of the metacognitive noise parameter σm will ultimately lead to a truly flat/indifferent relationship between evidence and confidence, the multiplicative evidence parameter 𝜑m only affects the slope (i.e., asymptotically confidence will still reach 1). This is one reason why parameter recovery for both σm and 𝜑m works overall very well. The differential effects of σm and 𝜑m are now better illustrated in the updated Figure 3:

Also conceptually, the multiplicative evidence parameter 𝜑m plausibly represents a metacognitive bias, with either interpretation that I suggest in the manuscript: as a an under/overestimation of the evidence or as a an over/underestimation of one’s own sensory noise, leading to under/overconfidence, respectively. In sum, I think there are strong arguments for the present formalization and interpretation.

• The final paragraph of the discussion was interesting but potentially concerning for a model of metacognition. It explains that data on empirical trial-by-trial accuracy is not used in the model fits. I hadn't appreciated this until this point in the paper. I can see how in a process model that simulates decision and confidence data from stimulus features, accuracy should not be an input into such a model. But in terms of a model fit, it seems odd not to use trial by trial accuracy to constrain the fits at the metacognitive level, given that the hallmark of metacognitive sensitivity is a confidence-accuracy correlation. Is it not possible to create accuracy-conditional likelihood functions when fitting the confidence rating data (similar to how the meta-d' model fit is handled)? Psychologically, this also makes sense given that the observer typically knows their own response when giving a confidence rating.

While I agree of course that metacognitive sensitivity quantifies the relationship confidence-accuracy relationship, a process model is a distinct approach and requires distinct methodology. Briefly, the current model fit cannot be improved upon, as it is based on a precise inversion of the forward model. Computing accuracy-conditional likelihoods would lead to a biased parameter estimates, because it would incorrectly imply that the observer has access to the accuracy of their choice. While the observer knows their choice, as the reviewer correctly notes, they do not know the true stimulus category and hence not their accuracy.

I argue in the manuscript that both approaches (descriptive meta-d’, explanatory process model) have their advantages and disadvantages. The concept of meta-d’ / metacognitive sensitivity does not care why a particular confidence rating is the way it is, or whether an incorrect response is caused by sensory noise or by an attentional lapse. On the one hand, this implies that one cannot draw any conclusions about the causes and mechanisms of metacognitive inefficiency, which could be perceived as a major drawback. In this respect, it is a purely descriptive measure (cf. last comment of Reviewer #1). On the other hand, because it is descriptive, it can simply compare the confidence between correct and incorrect choices and thus, in a sense, capture a more thorough picture of metacognitive sensitivity; that is, being metacognitively aware not only of the consequences one’s own sensory noise (as in typical process models), but also of all other sources of error (attentional lapses, finger errors, etc.). I now added an additional paragraph in which I summarize the comparison of type 2 ROC / meta-d’ and process models along these lines (Line 800ff):

“In sum, while a type 2 ROC analysis, as a descriptive approach, does not allow any conclusions about the causes of metacognitive inefficiency, it is able to capture a more thorough picture of metacognitive sensitivity: that is, it quantifies metacognitive awareness not only about one’s own sensory noise, but also about other potential sources of error (attentional lapses, finger errors, etc.). While it cannot distinguish between these sources, it captures them all. On the other hand, only a process model approach will allow to draw specific conclusions about mechanisms – and pin down sources – of metacognitive inefficiency, which arguably is of major importance in many applications.”

• I found it concerning that all the variability in scale usage were being assumed to load onto evidencerelated parameters (eg delta_m) rather than being something about how subjects report or use an arbitrary confidence scale (eg the "implicit biases" assumed to govern the upper and lower bounds of the link function). It strikes me that you could have a similar notion of offset at the level of report - eg an equivalent parameter to delta_m but now applied to c and not z. Would these be distinguishable? They seem to have quite different interpretations psychologically: one is at the level of a bias in confidence formation, and the other at the level of a public report.

I substantially reworked the section about metacognitive biases, including an additive metacognitive bias (κm) also at the level of confidence. The previous version of the manuscript already included a multiplicative bias parameter loading onto confidence (previously referred to as ‘confidence scaling’ parameter, now multiplicative confidence bias λm), but it was considered optional and e.g. not part of the parameter recovery analyses.

My previous emphasis on biases that load onto evidence-related variables was due to a more principled interpretation (e.g. ‘underestimation of sensory noise’), but I agree that metacognitive biases must not necessarily be principled and may be driven e.g. by the idiosyncratic usage of a particular confidence scale. Updated Figure 1 sketches the new, more complete model.

Is a mix of evidence- and confidence-related metacognitive bias parameters distinguishable? I tested this in Figure 7—figure supplement 3.

The slope matrices show that e.g., the model suggested by the reviewer (two evidence-related bias parameters 𝜑m and δm + an additive confidence-based bias parameter κm) is to some degree dissociable, although slight tradeoffs start to emerge with such a complex model. By contrast, a mix of only one evidence-related and one confidence-related bias parameter is much more robust. In general, I thus recommend using at most two metacognitive bias parameters, which are selected either based on a priori hypotheses or on a model comparison. I comment on the necessity of choosing one’s bias parameters in a new paragraph in section 1.4 about metacognitive biases (Line 276ff):

“Finally, note that the parameter recovery shown in Figure 4 was performed with four separate models, each of which was specified with a single metacognitive bias parameter (i.e., 𝜑m, δm, λm, or m). Parameter recovery is more unreliable when more than two of these bias parameters are specified in parallel (see section 2.3; in particular, Figure 7—figure supplement 3). In practice, the researcher thus must make an informed decision about which bias parameters to include in a specific model (in most scenarios 1 or 2 metacognitive bias parameters is a good choice). While the evidence-related bias parameters 𝜑m and δm have a more principled interpretation (e.g., as an under/overestimation of sensory noise), it is not unlikely that metacognitive biases also emerge at the level of the confidence report (λm, km). The first step thus must always be a process of model specification or a statistical comparison of candidate models to determine the final specification (see also section 3.1).”

Author Response

Reviewer #1 (Public Review):

The paper correctly identifies two biophysical properties that may impact an OHC contribution to cochlear amplification. These are the membrane RC time constant and prestin kinetics. The RC problem was identified by Santos-Sacchi 1989 (1) based on measures of OHC membrane capacitance, electromotility (eM) and published OHC resting and receptor potential data. At issue was a 20 dB disparity between threshold BM measures and eM when the resting potential (RP, ~ -70 mV)) is displaced from the voltage at maximal eM gain or peak NLC (Vh; ~ -40 mV). If RP were actually at Vh then the problem would not have been identified, assuming that prestin's voltage-responsiveness were frequency-independent, which was not in question at that time. Over the last two decades several groups have found prestin performance to be low pass. Isolated OHCs, macro-patch and OHCs in situ cochlear explants all show this low pass behavior. To date, no manipulations of load have pushed the voltage responsiveness to frequency-independent. This manuscript tries to avoid the kinetics issue and attempts to focus on the RC problem that has been dealt with extensively since 1989, including at that time a suggestion that the RC problem points to the dominance of the stereocilia bundle (2).

The authors suggest that kinetics of prestin is not addressed in the current manuscript, but this is not the case. In ignoring the paper from Santos-Sacchi and Tan 2018 (3), reliance on Frank et al.'s (4) data explicitly utilizes their kinetic results. OHC84 (so-called short cell, 51 um long) is essentially frequency-independent after microchamber voltage roll-off correction. The authors choose 1 nm/mV gain at 50 kHz to work with in their arguments. As it turns out, the corrected eM of OHC84 is wrong since it does not fix the reported 23 kHz microchamber voltage roll-off. While OHC65 is appropriately fixed, OHC84 is over compensated. Gain at 50 kHz should be about half the chosen gain. This is not the most problematic issue for their arguments, however.

In Santos-Sacchi and Tan 2018 (3) we show that low frequency (near DC) eM gain for OHCs averaging 55.3 um long is about 15 nm/mV. This indicates, as noted in that paper, that the resting potential of OHC84 was far shifted from Vh, accounting for its wide-band frequency response. If indeed, the authors still maintain that OHC eM is frequency-independent, ala Frank et al. (and in disregard to other publications where, to the contrary, eM gain would be far less at 50 kHz - see (5, 6)), then the eM gain at 50 kHz should be closer to 15 nm/mV; large enough, I think, to make their RC problem exercise overkill. That is, even in 1989 such a gain would not have suggested an RC problem. This is assuming that the normal resting potential is at Vh. Of course, at Vh membrane capacitance would be about twice that of linear capacitance (due to peak NLC) - the cell time constant does not discriminate against source of capacitance. All in all, isolated OHC biophysics that provides the voltage dependence and the kinetics of prestin cannot be ignored to deal with the RC problem in isolation. Doing so will give a false sense of how the cochlea works, and will encourage others to neglect, without rationale, published pertinent data, as with the Sasmal and Grosh 2019 (7) model where the OHC is treated as a frequency-independent PZE device.

Finally, to scorn the significance of component characteristics comprising the whole cochlea, e.g., based on isolated OHC biophysics or prestin's cryo-EM structure, as a fallacy of composition suffers itself from hasty generalization. Of course, knowing the biophysics of single OHCs informs on the system response. Otherwise, the prestin KO would have been an unfunded goal, never allowed to pass beyond a system modeler's review. Indeed, the authors would have none of the "carefully" chosen data to present their RC counter argument. Pertinent, published biophysical characteristics must be included in any critical discussion on OHC performance. For that matter, cochlear modelers must follow the same rule.

We thank reviewer #1 for the suggestions on the kinetics of prestin and previous literature.

Although there is no data (to our best knowledge) for electromotilty (eM) in isolated basal murine OHCs, a more thorough review of the existing literature on the topic suggest that the assumed parameters are indeed a reasonably conservative estimation of eM in situ.

Additionally, the OHC parameters are pessimistic enough to account for a doubling of effective capacitance due to NLC.

Regarding the fallacy of composition, we are puzzled that the reviewer interpreted it as a “scorning” of the OHC biophysics, obviously important for cochlear function. The raised point is simple and rather obvious: a system built with low-pass filters doesn’t mean that the system is a low-pass filter. This is elucidated with the analogy, familiar to electrical engineers, that high- and band-pass filters are often built by cascading and mixing the response of low-pass filters. The “fallacy of composition” therefore lies in the conclusion that since eM is “low-pass”, it can’t possibly contribute to high frequency amplification. Strikingly, this conclusion is often based on measured vibrations near the OHCs showing transfer functions with >30 dB peak-to-tail ratio, and that are somewhat consistent with the inner working of cochlear models. That is, we are criticizing one specific interpretation of the biophysical data, not certainly suggesting that collecting and analyzing the data in the first place is unimportant.

Reviewer #2 (Public Review):

In the inner ear, the cochlea transforms sound-induced vibrations into electrical signals that are sent to the brain. Cochlear outer hair cells (OHCs) are thought to amplify these vibrations, but it is unclear how amplification works. Sound-induced vibrations modulate the current entering an OHC, which drive its receptor potential, causing the OHC to change length. The change in length owing to the receptor potential variation, known as the OHC's electromotile response, depends on the size of the receptor potential. However, the receptor potential decreases with increasing sound frequency, because of the resistance (R) and capacitance (C) of the OHC's membrane. This paper addresses the RC problem, limitations on high-frequency amplification owing to the OHC's receptor potential decreasing with frequency.

The authors use a well-known simplification of the RC problem and some back-of-the-envelope calculations to argue that OHCs can amplify sufficiently well at high frequencies to match experimental data, despite the decrease in their receptor potentials. They argue that changes to OHC properties along the cochlea allow them to amplify at high frequencies and that OHCs reduce noise and distortion. They argue against OHCs as being cochlear impedance regulators and that OHCs do not limit cochlear tuning.

Figure 1 and Equations 1-6 are useful teaching tools but are not novel. The back-of-the-envelope calculations use these equations and a limited number of data points from the literature. There are many prior models that show amplification despite the RC problem, but they are not analyzed or discussed in much detail.

How RC OHC filtering reduces noise without reducing the signal is not explained. The type of noise calculation done in Appendix 1 is well-known and the application is again a rough back-of-the-envelope calculation. Most of the statements about noise are not fleshed out or supported by calculations.

The discussion about tonotopic variations has little new data. Fig. 2 uses two data points from the literature and an unpublished data point from a colleague. The fact that BM displacement is smaller at the base than at the apex is well known. There is speculation that reduced OHC motion is "effectively counteracted" by gradients in OHC capacitance and MET current, but no evidence is presented.

The discussion about distortions is pedagogical but is again speculation without new or strong-supporting evidence. Fig. 3 argues that OHCs might reduce high-frequency distortions, but don't limit the cochlear amplifier. The plots shown are either well-known consequences of filtering or a summary of the authors' previous model data.

The arguments against OHCs as regulators and that they don't limit tuning are not well flushed out, speculative, and unsupported by new calculations or data.

This paper does not clarify OHC operation or the RC problem, because it mixes speculation, limited data, and topics that are not clearly related to the problem.

We agree with reviewer #2 that there are no new physics principles elucidated here, and that most of the discussion relies on simple calculations. But we believe that such simple calculations are the missing piece (absent in the literature) that allow one to appreciate the magnitude of the problem under exam—magnitude typically inflated by focusing on quantities whose physical significance is uncertain. In other words, we believe that the simplicity of the calculations and physical reasoning is not a bug, but a feature of the paper.

We believe that in his criticism regarding various topics of discussion presenting little or speculative new evidence, this reviewer might not have fully considered that most of the evidence provided here is fundamentally a physics-based review of the recent experimental data, incidentally the same type of data previously employed to argue that the RC problem is dramatic in the first place. Likely we didn't convey this message clearly enough in the manuscript.

While the arguments against OHCs as regulators are not all new, they are often ignored (or perhaps forgotten) and we believe there is a value in synthesizing them all in one place. The support for these arguments comes from fundamental hydrodynamic principles, previous modeling studies, and most importantly from OCT data collected over the last 6 years. Of course, the discussion on the plausibility of suggested mechanisms lacking a concrete proposal cannot be 100% “analytic”.

About noise and signal amplification, the missing piece perhaps is that distributed internal noise sources (e.g., thermal and shot noise) are independent of each other and hence spatially incoherent. While the manuscript doesn’t specifically deal with signal vs. noise amplification in cochlear models, spatially distributed amplification is known to boost signals more than internal noise—a principle universally used in telecommunications and addressed in >60-year-old literature.

Reviewer #3 (Public Review):

This paper discusses the effect of the low-pass filtering between outer hair cell transducer current and receptor voltage. The filter's cut-off frequency (where the response is down by a factor of 0.71 of its maximum) can be quantified by the resistance and capacitance of the cell hair cell's basolateral membrane. The capacitance value is determined mainly by the lipid membrane and is augmented by the charge movement of the piezoelectric prestin molecule, which endows the OHC with its electromotile properties. The OHC's capacitance (C) value is pretty well known. The resistance (R) is determined mainly by K+ channels in the basolateral membrane, a value that is also known reasonably well. The low-pass cut-off frequency is equal to (2pi*RC)^-1 and has a value of a ~1 to a few kHz - a value that has both experimental and theoretical support. The low-pass filtering of membrane voltage is important because the cell responds to membrane voltage by shortening and lengthening - this electromotility is thought to be key to the cochlea's operation and in particular to cochlear amplification, the process that enhances the magnitude and tuning of the cochlea's passive response to sound. However, the auditory system works to 80 kHz and even higher in some animals. Thus, it has been posed (let's say by team A) that the RC cut-off frequency value of a few kHz makes electromotility too slow to operate "cycle-by-cycle" up to several 10s of kHz. The article under review, representing team B, supports "cycle-by-cycle" action, arguing that the several kHz cut off frequency is not a problem and is even an advantage.

The arguments put forward in favor of cycle-by-cycle action are:

1. The size of the motions, even with the low-pass-filtered attenuation are as large or larger as those measured in the cochlea at high frequencies.

2. Noise is often increasing as frequency decreases, thus low-pass-filtering is actually good, to reduce the predominantly low frequency noise.

3. Harmonic distortion is at supra-CF frequencies, so it's good if the hair cell is low-pass-filtering to reduce harmonics.

These three points are reasonable, and the quantification relating to statement 1 is convincing. However, the quantification associated with point 2 is muddled. The hair cell voltage signal is expressed in volts, but the noise value is given in terms of the current mediated by 1-5 channels. A quantitative comparison should be made, with signal and noise expressed in the same units, preferably volts and volts/root(Hz), with a bandwidth estimated. The appendix attempts to be more quantitative and something like that short appendix should be incorporated into the paper. If a quantitative comparison in standard units is not possible with current data, that can be stated and underscores that we really don't know whether the noise is a problem for cycle-by-cycle amplification. Point 3 is reasonable and nicely illustrated in Fig. 3B. I did not get anything from Fig. 3A and the corresponding discussion on page 8 lines 320-335. Panels C and D were under-explained and could be removed, and the caption's reference to "short wave hydrodynamics" was also under-explained.

The arguments put forward to challenge gain control mechanics, which employ DC shifts to set effective operating conditions:

1. Operation based on DC and quasi-DC operating points is sensitive to noise, which as noted above is often increasing as frequency decreases.

2. Operation that employs a DC shift for operating point is likely to work in such a way to reduce stiffness, which has been shown to be inconsistent with active cochlear responses. For example, stiffness reduction would reduce traveling wave wavelength and thus alter the response phase and timing to a degree that has not been observed experimentally. This has long been known and relevant papers are cited.

Point 4 was not convincing to me because the motions related to setting operating conditions could be larger than the nanoscale cycle-by-cycle response motions - thus these operating point motions could be above the noise values that seem limiting to cycle-by-cycle amplification. Point 5 is a nice reminder of the conclusion that, based on experimental findings and physics-based basic cochlear models, the cochlear amplifier must work by means of energy injection. This point was made clearly by Kolston (well cited in this paper) and later supported by other work.

The present paper is informative in many ways and offers useful insights for further exploration. It is nicely written and illustrated. Because the signal and noise values are not quantified, the basic claim, that the cochlea amplifier can amplify a noisy signal effectively, is not convincing and that basic question is still unsettled. Overall, the paper would be improved if the claims and arguments were presented more tightly, with fewer digressions, and more modestly.

We thank reviewer #3 for the many comments and suggestions.

We agree that plotting the spectral density of a “near-threshold” OHC signal vs. inherent electric noise results in much simplification. Regarding noise and signal amplification, previous work on transmission lines points out that amplification is the way to increase SNR along the line.

We believe that part of the undergoing confusion is that the problem is not how OHC can amplify a “noisy signal” —the cochlea amplifies “noisy” sounds similarly as it amplifies pure tones— but how OHCs can amplify signals in presence of internal noise. Amplification and detection are two distinct things, and signal amplification does not rely on detection. Detection is an intrinsically nonlinear decision process (e.g., signal present/absent). Amplification in relevant frequency ranges is what allows to detect signals in the real world (e.g., radio receivers). The cochlea (as portrayed by classic theories) does not seem exceptional in this regard.

We agree that the effect of noise on DC responses is not very clear in the manuscript. Although it is difficult to make quantitative statements on a hypothesis that lacks a concrete mechanistic proposal, ~63% of (inherent) electric noise power is confined below the RC corner frequency, i.e, the frequency band of the regulatory OHC. In presence of (unavoidable) flicker and brown noise (e.g., Brownian motion of stereocilia), this percentage can only increase. Conversely, in the frequency band of OHC cycle-by-cycle amplification, the noise power is only a tiny fraction of the total.

Reviewer #1 (Public Review):

The paper correctly identifies two biophysical properties that may impact an OHC contribution to cochlear amplification. These are the membrane RC time constant and prestin kinetics. The RC problem was identified by Santos-Sacchi 1989 (1) based on measures of OHC membrane capacitance, electromotility (eM) and published OHC resting and receptor potential data. At issue was a 20 dB disparity between threshold BM measures and eM when the resting potential (RP, ~ -70 mV)) is displaced from the voltage at maximal eM gain or peak NLC (Vh; ~ -40 mV). If RP were actually at Vh then the problem would not have been identified, assuming that prestin's voltage-responsiveness were frequency-independent, which was not in question at that time. Over the last two decades several groups have found prestin performance to be low pass. Isolated OHCs, macro-patch and OHCs in situ cochlear explants all show this low pass behavior. To date, no manipulations of load have pushed the voltage responsiveness to frequency-independent. This manuscript tries to avoid the kinetics issue and attempts to focus on the RC problem that has been dealt with extensively since 1989, including at that time a suggestion that the RC problem points to the dominance of the stereocilia bundle (2).

The authors suggest that kinetics of prestin is not addressed in the current manuscript, but this is not the case. In ignoring the paper from Santos-Sacchi and Tan 2018 (3), reliance on Frank et al.'s (4) data explicitly utilizes their kinetic results. OHC84 (so-called short cell, 51 um long) is essentially frequency-independent after microchamber voltage roll-off correction. The authors choose 1 nm/mV gain at 50 kHz to work with in their arguments. As it turns out, the corrected eM of OHC84 is wrong since it does not fix the reported 23 kHz microchamber voltage roll-off. While OHC65 is appropriately fixed, OHC84 is over compensated. Gain at 50 kHz should be about half the chosen gain. This is not the most problematic issue for their arguments, however.

In Santos-Sacchi and Tan 2018 (3) we show that low frequency (near DC) eM gain for OHCs averaging 55.3 um long is about 15 nm/mV. This indicates, as noted in that paper, that the resting potential of OHC84 was far shifted from Vh, accounting for its wide-band frequency response. If indeed, the authors still maintain that OHC eM is frequency-independent, ala Frank et al. (and in disregard to other publications where, to the contrary, eM gain would be far less at 50 kHz - see (5, 6)), then the eM gain at 50 kHz should be closer to 15 nm/mV; large enough, I think, to make their RC problem exercise overkill. That is, even in 1989 such a gain would not have suggested an RC problem. This is assuming that the normal resting potential is at Vh. Of course, at Vh membrane capacitance would be about twice that of linear capacitance (due to peak NLC) - the cell time constant does not discriminate against source of capacitance. All in all, isolated OHC biophysics that provides the voltage dependence and the kinetics of prestin cannot be ignored to deal with the RC problem in isolation. Doing so will give a false sense of how the cochlea works, and will encourage others to neglect, without rationale, published pertinent data, as with the Sasmal and Grosh 2019 (7) model where the OHC is treated as a frequency-independent PZE device.

Finally, to scorn the significance of component characteristics comprising the whole cochlea, e.g., based on isolated OHC biophysics or prestin's cryo-EM structure, as a fallacy of composition suffers itself from hasty generalization. Of course, knowing the biophysics of single OHCs informs on the system response. Otherwise, the prestin KO would have been an unfunded goal, never allowed to pass beyond a system modeler's review. Indeed, the authors would have none of the "carefully" chosen data to present their RC counter argument. Pertinent, published biophysical characteristics must be included in any critical discussion on OHC performance. For that matter, cochlear modelers must follow the same rule.

1. J. Santos-Sacchi, Asymmetry in voltage-dependent movements of isolated outer hair cells from the organ of Corti. J. Neurosci. 9, 2954-2962 (1989).<br /> 2. A. J. Hudspeth, How the ear's works work. Nature 341, 397-404 (1989).<br /> 3. J. Santos-Sacchi, W. Tan, The Frequency Response of Outer Hair Cell Voltage-Dependent Motility Is Limited by Kinetics of Prestin. J. Neurosci. 38, 5495-5506 (2018).<br /> 4. G. Frank, W. Hemmert, A. W. Gummer, Limiting dynamics of high-frequency electromechanical transduction of outer hair cells. Proc. Natl. Acad. Sci. U. S. A. 96, 4420-4425 (1999).<br /> 5. J. Santos-Sacchi, D. Navaratnam, W. J. T. Tan, State dependent effects on the frequency response of prestin's real and imaginary components of nonlinear capacitance. Sci. Rep. 11, 16149 (2021).<br /> 6. J. Santos-Sacchi, W. Tan, Complex nonlinear capacitance in outer hair cell macro-patches: effects of membrane tension. Sci. Rep. 10, 6222 (2020).<br /> 7. A. Sasmal, K. Grosh, Unified cochlear model for low- and high-frequency mammalian hearing. Proc Natl Acad Sci U S A 116, 13983-13988 (2019).

Author Response

Reviewer #1 (Public Review):

In this manuscript, Abdellatef et al. describe the reconstitution of axonemal bending using polymerized microtubules (MTs), purified outer-arm dyneins, and synthesized DNA origami. Specifically, the authors purified axonemal dyneins from Chlamydomonas flagella and combined the purified motors with MTs polymerized from purified brain tubulin. Using electron microscopy, the authors demonstrate that patches of dynein motors of the same orientation at both MT ends (i.e., with their tails bound to the same MT) result in pairs of MTs of parallel alignment, while groups of dynein motors of opposite orientation at both MT ends (i.e., with the tails of the dynein motors of both groups bound to different MTs) result in pairs of MTs with anti-parallel alignment. The authors then show that the dynein motors can slide MTs apart following photolysis of caged ATP, and using optical tweezers, demonstrate active force generation of up to ~30 pN. Finally, the authors show that pairs of anti-parallel MTs exhibit bidirectional motion on the scale of ~50-100 nm when both MTs are cross-linked using DNA origami. The findings should be of interest for the cytoskeletal cell and biophysics communities.

We thank the reviewer for these comments.

We might be misunderstanding this reviewer’s comment, but the complexes with both parallel and anti-parallel MTs had dynein molecules with their tails bound to two different MTs in most cases, as illustrated in Fig.2 – suppl.1. The two groups of dyneins produce opposing forces in a complex with parallel MTs, and majority of our complexes had parallel arrangement of the MTs. To clarify the point, we have modified the Abstract:

“Electron microscopy (EM) showed pairs of parallel MTs crossbridged by patches of regularly arranged dynein molecules bound in two different orientations depending on which of the MTs their tails bind to. The oppositely oriented dyneins are expected to produce opposing forces when the pair of MTs have the same polarity.”

Reviewer #2 (Public Review):

Motile cilia generate rhythmic beating or rotational motion to drive cells or produce extracellular fluid flow. Cilia is made of nine microtubule doublets forming a spoke-like structure and it is known that dynein motor proteins, which connects adjacent microtubule doublet, are the driving force of ciliary motion. However the molecular mechanism to generate motion is still unclear. The authors proved that a pair of microtubules stably linked by DNA-origami and driven by outer dynein arms (ODA) causes beating motion. They employed in vitro motility assay and negative stain TEM to characterize this complex. They demonstrated stable linking of microtubules and ODAs anchored on the both microtubules are essential for oscillatory motion and bending of the microtubules.

Strength

This is an interesting work, addressing an important question in the motile cilia community: what is the minimum system to generate a beating motion? It is an established fact that dynein power stroke on the microtubule doublet is the driving force of the beating motion. It was also known that the radial spoke and the central pair are essential for ciliary motion under the physiological condition, but cilia without radial spokes and the central pair can beat under some special conditions (Yagi and Kamiya, 2000). Therefore in the mechanistic point of view, they are not prerequisite. It is generally thought that fixed connection between adjacent microtubules by nexin converts sliding motion of dyneins to bending, but it was never experimentally investigated. Here the authors successfully enabled a simple system of nexin-like inter-microtubule linkage using DNA origami technique to generate oscillatory and beating motions. This enables an interesting system where ODAs form groups, anchored on two microtubules, orienting oppositely and therefore cause tag-of-war type force generation. The authors demonstrated this system under constraints by DNA origami generates oscillatory and beating motions.

The authors carefully coordinated the experiments to demonstrate oscillations using optical tweezers and sophisticated data analysis (Fourier analysis and a step-finding algorithm). They also proved, using negative stain EM, that this system contains two groups of ODAs forming arrays with opposite polarity on the parallel microtubules. The manuscript is carefully organized with impressive movies. Geometrical and motility analyses of individual ODAs used for statistics are provided in the supplementary source files. They appropriately cited similar past works from Kamiya and Shingyoji groups (they employed systems closer to the physiological axoneme to reproduce beating) and clarify the differences from this study.

We thank the reviewer for these comments.

Weakness

The authors claim this system mimics two pairs of doublets at the opposite sites from 9+2 cilia structure by having two groups of ODAs between two microtubules facing opposite directions within the pair. It is not exactly the case. In the real axoneme, ODA makes continuous array along the entire length of doublets, which means at any point there are ODAs facing opposite directions. In their system, opposite ODAs cannot exist at the same point (therefore the scheme of Dynein-MT complex of Fig.1B is slightly misleading).

Actually, opposite ODAs can exist at the same point in our system as well, and previous work using much higher concentration of dyneins (e.g, Oda et al., J. Cell biol., 2007) showed two continuous arrays of dynein molecules between a pair of microtubules. To observe the structures of individual dynein molecules we used low concentrations of dynein and searched for the areas where dynein could be observed without superposition, but there were some areas where opposite dyneins existed at the same point.

We realize that we did not clearly explain this issue, so we have revised the text accordingly.

In the 1st paragraph of Results: “In the dynein-MT complexes prepared with high concentrations of dynein, a pair of MTs in bundles are crossbridged by two continuous arrays of dynein, so that superposition of two rows of dynein molecules is observed in EM images (Haimo et al., 1979; Oda et al., 2007). On the other hand, when a low concentration of the dynein preparation (6.25–12.5 µg/ml (corresponding to ~3-6 nM outer-arm dynein)) was mixed with 20-25 µg/ml MTs (200-250 nM tubulin dimers), the MTs were only partially decorated with dynein, so that we were able to observe single layers of crossbridges without superposition in many regions.” Legend of Fig. 1(C): “Note that the geometry of dyneins in the dynein-MT complex shown in (B) mimics that of a combination of the dyneins on two opposite sides of the axoneme (cyan boxes), although the dynein arrays in (B) are not continuous.”

If they want to project their result to the ciliary beating model, more insight/explanation would be necessary. For example, arrays of dyneins at certain positions within the long array along one doublet are activated and generate force, while dyneins at different positions are activated on another doublet at the opposite site of the axoneme. This makes the distribution of dyneins and their orientations similar to the system described in this work. Such a localized activation, shown in physiological cilia by Ishikawa and Nicastro groups, may require other regulatory proteins.

We agree that the distributions of activated dyneins in 3D are extremely important in understanding ciliary beating, and that other regulatory proteins would be required to coordinate activation in different places in an axoneme. However, the main goal of this manuscript is to show the minimal components for oscillatory movements, and we feel that discussing the distributions of activated dyneins along the length of the MTs would be too complicated and beyond the scope of this study.

They attempted to reveal conformational change of ODAs induced by power stroke using negative stain EM images, which is less convincing compared to the past cryo-ET works (Ishikawa, Nicastro, Pigino groups) and negative stain EM of sea urchin outer dyneins (Hirose group), where the tail and head parts were clearly defined from the 3D map or 2D averages of two-dynein ODAs. Probably three heavy chains and associated proteins hinder detailed visualization of the tail structure. Because of this, Fig.2C is not clear enough to prove conformational change of ODA. This reviewer imagines refined subaverage (probably with larger datasets) is necessary.

As the reviewer suggests, one of the reasons for less clear averaged images compared to the past images of sea urchin ODA is the three-headed structure of Chlamydomonas ODA. Another and perhaps the bigger reason is the difficulty of obtaining clear images of dynein molecules bound between 2 MTs by negative stain EM: the stain accumulates between MTs that are ~25 nm in diameter and obscures the features of smaller structures. We used cryo-EM with uranyl acetate staining instead of negative staining for the images of sea urchin ODA-MT complexes we previously published (Ueno et al., 2008) in order to visualize dynein stalks. We agree with the reviewer that future work with larger datasets and by cryo-ET is necessary for revealing structural differences.

That having been said, we did not mean to prove structural changes, but rather intended to show that our observation suggests structural changes and thus this system is useful for analyzing structural changes in future. In the revised manuscript, we have extensively modified the parts of the paper discussing structural changes (Please see our response to the next comment).

It is not clear, from the inset of Fig.2 supplement3, how to define the end of the tail for the length measurement, which is the basis for the authors to claim conformational change (Line263-265). The appearance of the tail would be altered, seen from even slightly different view angles. Comparison with 2D projection from apo- and nucleotide-bound 3-headed ODA structures from EM databank will help.

We agree with the reviewer that difference in the viewing angle affects the apparent length of a dynein molecule, although the 2 MTs crossbridged by dyneins lie on the carbon membrane and thus the variation in the viewing angle is expected to be relatively small. To examine how much the apparent length is affected by the view angle, we calculated 2D-projected images of the cryo-ET structures of Chlamydomonas axoneme (emd_1696 and emd_1697; Movassagh et al., 2010) with different view angles, and measured the apparent length of the dynein molecule using the same method we used for our negative-stain images (Author response image 1). As shown in the plot, the effect of view angles on the apparent lengths is smaller than the difference between the two nucleotide states in the range of 40 degrees measured here. Thus, we think that the length difference shown in Fig.2-suppl.4 reflects a real structural difference between no-ATP and ATP states. In addition, it would be reasonable to think that distributions of the view angles in the negative stain images are similar for both absence and presence of ATP, again supporting the conclusion.

Nevertheless, since we agree with the reviewer that we cannot measure the precise length of the molecule using these 2D images, we have revised the corresponding parts of the manuscript, adding description about the effect of view angles on the measured length in the manuscript.

Author response image 1. Effects of viewing angles on apparent length. (A) and (B) 2D-projected images of cryo-electron tomograms of Chlamydomonas outer arm dynein in an axoneme (Movassagh et al., 2010) viewed from different angles. (C) apparent length of the dynein molecule measured in 2D-projected images.

In this manuscript, we discuss two structural changes: 1) a difference in the dynein length between no-nucleotide and +ATP states (Fig.2-suppl.4), and 2) possible structural differences in the arrangement of the dynein heads (Fig.2-suppl.3). Although we realize that extensive analysis using cryo-ET is necessary for revealing the second structural change, we attempted to compare the structures of oppositely oriented dyneins, hoping that it would lead to future research. In the revised manuscript, we have added 2D projection images of emd_1696 and emd_1697 in Fig.2-suppl.3, so that the readers can compare them with our negative stain images. We had an impression that some of our 2D images in the presence of ATP resembled the cryo-ET structure with ADP.Vi, whereas some others appeared to be closer to the no-nucleotide cryo-ET structure. We have also attempted to calculate cross-correlations, but difficulties in removing the effect of MTs sometimes overlapped with a part of dynein, adjusting the magnifications and contrast of different images prevented us from obtaining reliable results.

To address this and the previous comments, we have extensively modified the section titled ‘Structures of dynein in the dynein-MT-DNA-origami complex’.

In Fig.5B (where the oscillation occurs), the microtubule was once driven >150nm unidirectionally and went back to the original position, before oscillation starts. Is it always the case that relatively long unidirectional motion and return precede oscillation? In Fig.7B, where the authors claim no oscillation happened, only one unidirectional motion was shown. Did oscillation not happen after MT returned to the original position?

Long unidirectional movement of ~150 nm was sometimes observed, but not necessarily before the start of oscillation. For example, in Figure 5 – figure supplement 1A, oscillation started soon after the UV flash, and then unidirectional movement occurred.

With the dynein-MT complex in which dyneins are unidirectionally aligned (Fig.7B, Fig.7-suppl.2), the MTs kept moving and escaped from the trap or just stopped moving probably due to depletion of ATP, so we did not see a MT returning to the original position.

Line284-290: More characterization of bending motion will be necessary (and should be possible). How high frequency is it? Do they confirm that other systems (either without DNA-origami or without ODAs arraying oppositely) cannot generate repetitive beating?

The frequencies of the bending motions measured from the movies in Fig.8 and Fig.8-suppl.1 were 0.6 – 1 Hz, and the motions were rather irregular. Even if there were complexes bending at high frequencies, it would not have been possible to detect them due to the low time resolution of these fluorescence microscopy experiments (~0.1 s). Future studies at a higher time resolution will be necessary for further characterization of bending motions.

To observe bending motions, the dynein-MT complex should be fixed to the glass or a bead at one part of the complex while the other end is free in solution. With the dynein-MT-DNA-origami complexes, we looked for such complexes and found some showing bending motions as in Fig. 8. To answer the reviewer’s question asking if we saw repetitive bending in other systems, we checked the movies of the complexes without DNA-origami or without ODAs arraying oppositely but did not notice any repetitive bending motions. However, future studies using the system with a higher temporal resolution and perhaps with an improved method for attaching the complex would be necessary in these cases as well.

Author Response

Reviewer #2 (Public Review):

Schrecker, Castaneda and colleagues present cryo-EM structures of RFC-PCNA bound to 3'ss/dsDNA junction or nicked DNA stabilized by slowly hydrolyzable ATP analogue, ATPyS. They discover that PCNA can adopt an open form that is planar, different from previous models for the loading a sliding clamp. The authors also report a structure with closed PCNA, supporting the notion that closure of the sliding clamp does not require ATP hydrolysis. The structures explain how DNA can be threaded laterally through a gap in the PCNA trimer, as this process is supported by partial melting of the DNA prior to insertion. The authors also visualise and assign a function to the N-terminal domain in the Rfc1 subunit of the clamp loader, which they find modulates PCNA loading at the replication forks, in turn required for processive synthesis and ligation of Okazaki fragments.

This work is extremely well done, with several structures with resolutions better than 3Å, which a significant achievement given the dynamic nature of the PCNA ring loading process. To investigate the role of the N-terminal domain of Rfc1 in PCNA loading, the authors use in vitro reconstitution of the entire DNA replication reaction, which is a powerful method to identify specific defects in Okazaki fragment synthesis and ligation.

Important issues

1. Figure 3B,D,F. I would find them much more informative if the authors showed the overlay between atomic model and cryo-EM density in the main figure. If the figure becomes too busy, the authors could decide to just add additional panels with the overlay as well as the atomic models alone. I do not think that showing segmented density for the DNA alone, as done is Figure 6C is sufficient. Also including the density for e.g. residues Trp638 and Phe582 seems important.

We thank the reviewer for the suggestion. However, we have been unable to establish a way to show the density for both the protein and DNA in a meaningful manner due to the large number of atoms in the fields of view. For an example, please see Figure 1, which corresponds to Figure 3H. To aid the reader, we have revised several of the Figures and Figure Supplements to include density for the DNA.

Consistent with our structures, recent work from the Kelch group has identified Trp638 and Phe582 as facilitating DNA base flipping (Gaubitz et al., 2022a). Despite the role in base flipping, no growth defects were observed in cells in which either of these residues were mutated and thus their functional role and the role of DNA base-flipping remains unclear.

1. Cryo-EM samples preparation included substoichiometric RPA, which has been shown to promote DNA loading of PCNA by RFC. Would the authors expect a subset of PCNA-RFC-DNA particles to contain RPA as well? The glycerol gradient gel indicates that, at least in fraction 5, a complex might exist. If the authors think that the particles analyzed cannot contain RPA, it would be useful to mention this.

We have no evidence to suggest that RPA cannot be present in the imaged particles. We have revised the text (lines 150 - 152) clarify that while RPA was present in the sample, we did not observe any density that could not be assigned to either DNA, RFC or PCNA. We therefore suggest that RPA does not interact with the complex in a stable manner.

1. Published kinetic data indicate that ATP hydrolysis occurs before clamp closure. To incorporate this notion in their model, the authors suggest that ATP hydrolysis might promote PCNA closure by disrupting the planar RFC:PCNA interaction surface and hence the dynamic interaction of PCNA with Rfc2 and -5 in the open state. In addition, ATP hydrolysis promotes RFC disengagement from PCNA-DNA by reverting from a planar to an out-of-plane state. This model appears reasonable and nicely combines published data with the new findings reported by the authors. However, the model is oversimplified in Figure 6, where the only depicted effect of ATP hydrolysis is RFC release. Perhaps the authors could use the figure caption to acknowledge that ATP hydrolysis likely still has a role in facilitating PCNA closure.

We have revised Figure 6 to show that DNA hydrolysis may occur either before or after ring closure.

1. Can the authors explain what steps should be taken to describe PCNA loading by RFC in conditions where ATP hydrolysis is permitted? How would such experiments further inform the molecular mechanism for the loading of the PCNA clamp?

As highlighted in point 3 above and by the other reviewers, ATP and ATPgS may alter the behavior and energetic landscape of RFC. In our studies, ATPgS was added trap the complex in a pre-hydrolysis state in which all components are assembled. We have added a section to the discussion noting the potential differences and highlighting the need for future studies to better elucidate the role of nucleotide hydrolysis. To achieve a hydrolysis competent complex, one could apply time-resolved cryo-EM approaches where the complex is formed on the grids and quickly vitrified. Such an approach, particularly if coupled with stopped-flow kinetic analyses, may provide additional insights in the kinetics of loading of PCNA onto DNA by RFC.

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Reply to the reviewers

Response to Reviewers

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

This is a well-executed and interesting study addressing a still controversial issue in clathrin-mediated endocytosis, namely the nature of curvature generation during formation of endocytic clathrin coated vesicles. The authors have applied new techniques to this old question, including state-of-the-art high resolution 3D single-molecule localization microscopy (SMLM, i.e. Super-resolution microscopy), a new maximum-likelihood based fitting framework to fit complex geometric models into localized point clouds (Wu et al., 2020, BioRxix) and mathematical modeling leading to a new cooperative curvature model of clathrin coat remodeling and temporal reconstruction of CCP structural dynamics based on the distribution of static super-resolution images. This is an important contribution, but will it resolve the controversy of constant curvature vs constant area for CCP invagination? I doubt it. In some ways the controversy is somewhat contrived and, as this paper shows the answer is unlikely to be either or. Below are some specific comments, in somewhat random order, from someone (a curmudgeon?) who has reviewed and/or carefully read these papers since 1980. Points that the authors should address are in bold. All can be addressed with modifications to the text, as the one experiment I asked for (quantification of clathrin recruitment) is impossible with this approach).

• I wonder how many people who cite Heuser's 1980 paper have ever read it carefully. Indeed, many of the observations made here were also made by Heuser. Below, for example, is a summary I wrote, but then removed from a review as it was too lengthy "While Heuser favored the model that CCPs assemble first as flat structures and then rearrange during invagination, he was also careful to note several caveats. First, he observed that the edges of CCPs were 'ragged', likely reflecting sites of assembly of new polygons and that pentagons were more abundant at the edges. Thus, he argued that 'if even a few of these edge pentagons were destined to become completely surrounded with hexagons, it would be necessary to conclude that some degree of curvature can be built into coats as soon as they form". Second, by examining tilted sections he observed that "even the flattest baskets have a small degree of inward curvature, and many were complete hemispheres". Finally, he cautioned that his images were snap-shots and a precursor-product relationship could not, therefore, be unambiguously established and that the very large flat lattices he observed might well be 'prove to be some sort of dead end'. We now know that fibroblasts, in particular, have large numbers of static flat clathrin plagues."

Thus, many of the author's conclusions, i.e. that 'completely flat clathrin coats are rare (pg 12, although they're not numbered), and that curved structures can be seen to emerge from the edges of flat lattices (see Supplemental Figure 1a, 3 examples on the right) are indeed consistent with Heuser's observations. In many ways, Heuser's 1980 paper is used as a straw man argument for the constant area model. The authors should more accurately cite and acknowledge this seminal paper.

Response: __We thank the reviewer for this insightful and constructive input on the interpretation of the constant area model (CAM). We have revised the discussion (Page 14, Lines 397-402), citing Heuser’s observations more carefully and in similarity of what was already suggested eloquently by the reviewer. We agree that the strict interpretation of the CAM is misleading, and early evidence already suggests its flawed approximation of the endocytic mechanism (further mentioned now on __Page 15, Lines 429-431).

• As Heuser did in his 1980 classic, the authors here would do well to note several caveats related to their analyses. These include:

+

Like Heuser they have assembled static imaged to create a pseudotemporal model, albeit using a much more quantitative approach. Nonetheless, it seems that this assumes only a single, stereotypic pathway for CCV formation. How good is this assumption? We know from dynamic imaging that there exists significant heterogeneity in both the kinetics and the molecular composition of CCPs. The authors should acknowledge this limitation.

__Response: __We agree with the reviewer that the lack of direct temporal information is a clear limitation of our approach.

We now introduce this limitation on Page 16, Lines 474-484, where we discuss the disadvantage of reconstructing an average trajectory based on static images. Here, the assumption of a single, stereotypic pathway of endocytosis is addressed. We cannot exclude the possibility of slight mechanistic variations being averaged out using our approach. However, we want to highlight the fact that our approach seems sensitive enough to distinguish between structures that originate via endocytosis, and structures that derived from a different pathway, potentially from the Golgi.

We further address the kinetic variability in terms of abortive events on Page 14, Lines 405-411, __and discuss their effect on the mechanistic interpretation of our results. Generally speaking, abortive events are characterized as dim and short-lived structures in live-cell acquisitions. As the earliest structures in our data set already contain half the final coat area, we are most likely not capturing these abortive events in the first place (potential technical reasons for not capturing earlier structures are discussed on __Page 14, Lines 385-395).

• The method, which required that they 'optimized the sample preparation to densely label clathrin at endocytic sites' involves labeling cells to near saturation with rabbit polyclonal antibodies to both clathrin light chains and clathrin heavy chains followed by detection with a second polyclonal donkey anti-rabbit. This gives 20 nm of additional and presumably flexible linker on the label. How might this effect the measurements and modeling? The Wu et al paper, which BTW has not been peer-reviewed, shows high precision fitting of the nuclear pore structure, but using endogenously tagged NUP-95, not two-layers of antibodies. The authors will need to discuss this limitation, it is my biggest concern regarding the analysis shown.

Response: __We acknowledge the limitations imposed by indirect immunolabelling and formulated a hypothesis on how this could affect our model fit (mentioned on __Page 13, Line 363, illustrated in Supplementary Figure 6). A larger linkage error between label and target molecule would increase the distribution of localizations around the true underlying structure. As LocMoFit fits our spherical model directly to the localization coordinates, it is able to take this distribution into account, and will weigh the fit results based on the uncertainty of the localization estimation. A uniform distribution of labels around the true underlying structure should therefore be fitted accurately also at larger linkage error. A non-uniform labeling could occur should e.g. the densely crowded space between the coat and the plasma membrane not allow for the diffusion of the antibody to the clathrin epitopes. In that case, labeling would be one-sided, and instead of the true underlying structure, LocMoFit would optimize the spherical model to the highest probability density of label around + 10 nm from the true clathrin coat. This would result in an overestimation of the radius by the model, which we could correct by substracting 10 nm from the experimentally determined radius. This was done in Supplementary Figure 6 for the hypotheses of (1) uniform displacement by the antibodies; (2) biased displacement of the antibodies towards the cytosol; and (3) biased displacement of the antibodies towards the plasma membrane. Whilst we see that the fitting parameters scale with the corrected radii, the mechanistic interpretation of partial flat pre-assembly on the membrane, and subsequent bending and surface area growth still holds true.

• One reason for continued controversy in this field is the lack of rany attempt to resolve findings obtained using different methods. Can a parsimonious explanation be found, or are their artifacts or misinterpretations of previous findings that can explain the discrepancies? Any valid model should fit all of the valid data. For example, the authors fail to cite a recent paper by Willy et al in Dev Cell (PMID 34774130), which has been on BioRxiv since 2019 (doi: https://doi.org/10.1101/715219). Here, similar to this present study, the authors used high resolution SIM-TIR to analyze ~1000 CCPs in 3 different cells lines (sadly non-overlapping with the cells used herein) and in Drosophila embryos to quantitatively test the two models. They conclude that their findings unambiguously support a constant curvature model. The authors would do the field a favor if they carefully read this paper and identified areas of commonality (i.e. that curvature is detected at early stages in both cases) and possible explanations for the discrepancies. Certainly, they should not ignore it.

Response: __We agree with the reviewer on the importance of consolidating findings from different studies to converge to a generally accepted mechanism of clathrin coat formation. We had indeed cited Willy et al in the introduction, but agree that further discussion of their findings should be included. We therefore discuss their findings in more detail, also in comparison to our work, on __Page 17, Lines 502-511. We agree that we reach contradictory conclusions, which we think lies at least in part with the way that Willy et al. analyze their data. Willy et al. acquire 2D projections of the endocytic clathrin structures, whose size is just at the limit of their image resolution. They then compare their projected sizes to a purist constant area model, which assumes that a coat has to grow to its entire surface as an entirely flat structure and then instantaneously snaps to an increased curvature, resulting in a sudden drop of the projected area (footprint). As we and others (e.g. Bucher et al 2011, Heuser, 1980) have observed, completely flat lattices are rare, and curvature is initiated before final surface area is acquired. We do not agree that the absence of a purist constant area model implies that clathrin mediated endocytosis follows a constant curvature trajectory. Instead, we imagine that our cooperative curvature model is likely to fit well with the observations of Willy and colleagues.

• An important body of evidence that is not considered in their model or discussion is that derived from live cell imaging. In addition to the heterogeneity mentioned above, studies have shown that the clathrin addition to CCPs is complete (i.e. the growth phase) occurs within the first ~20-30s, followed by a variable length (0->100s) plateau phase (Loerke et al, PMID 21447041). Both the current study and the Willy et al study admit that they may not be able to detect the earliest intermediates in CCP assembly. Indeed, in this study the smallest surface area CCPs are only 2-fold smaller than the largest CCPs, suggesting that over half of the triskelions have been recruited before a CCP can be distinguished from the background of clustered, nonspecifically-bound antibodies. Could the authors be monitoring events during the plateau phase and not the earliest events? Regardless, the findings are important as they address the nature of curvature generation during this plateau phase. While monitoring curvature generation during early events in CME, a recent study (Wang et al., eLife, PMID 32352376) showed that the acquisition of curvature within the first 20s of CCP assembly was a distinguishing feature between abortive and productive events. The authors might discuss how these studies on CCP dynamics might (or might not) inform their models.

__Response: __We thank the reviewer for this very insightful comment and discuss this hypothesis on __Page 16-17, Lines 485-511. __We suggest that part of the initiating/growth phase observed in live-cell dynamics falls into the fast, flat assembly that we are unable to capture with our approach. It is challenging to clearly identify at which point in real-time we are detecting our earliest sites. We would however argue that the plateau phase in real-time could coincide with curvature generation and final addition of triskelia at the lattice rim. The variability in the duration of this plateau phase could therefore result from variable recruitment speed of triskelia and other factors during the finalizing of the vesicle neck.

• The authors advertise 'quantitative' description of clathrin coated structure and indeed their measurements and models are quantitative; but there is no measure of intensity/numbers of triskelions and CCP growth: an important piece of quantitative data. I expect this is impossible with indirect immunofluorescence but should be considered as a limitation of the approach. Indeed, to my knowledge no one has yet quantitatively measured curvature generation in parallel to clathrin addition at CCPs (closest is Saffarian and Kirchhausen, PMID 17993495), but they don't discuss the relationship.

Response: __We agree with the reviewer that quantifying the number of triskelia would be an essential piece of information to correlate area growth and curvature generation with dynamic information retrieved from fluorescence intensity in live-cell studies. Unfortunately, the indirect immunolabelling approach used in this work complicated this quantification, and direct comparison between number of localizations and fluorescence intensity cannot be made. However, we do observe a correlation between coat surface area and number of localizations in our data and show this in the newly added __Supplementary Figure 7. This allows us to formulate the hypothesis on Page 16-17, Lines 485-511, which suggests that the plateauing of fluorescence intensity coincides with curvature generation and final triskelia addition to the coat rim. We further highlight the necessity of capturing both high spatial and temporal resolution simultaneously, to ultimately overcome this limitation.

• On page 7 equation 1, you assume a constant growth rate for addition of triskelia, but later describe that the rate might be cooperative (as the number of edges increases). How would this affect your modeling?

Response: __We formulate the __surface area growth rate of the clathrin coat to be proportional to the rim length with a constant____ rate. The cooperativity between clathrin molecules we consider to affect the rate of curvature generation. The more molecules are present, the more the entire coat is inclined to bent. We rephrased that section to emphasize this distinction (Page 8, Line 217).

Minor points:

• Can you indicate in the first paragraph of the results that you are using indirect immunofluorescence with rabbit anti-CLCA, anti-CHC and detection with donkey anti-rabbit for labeling, to augment the rather vague statement 'we optimized the sample preparation to densely label clathrin at endocytic sites'.

Response: __We added a clear indication on the labelling strategy used in this work on __Page 4, Lines 109-110.

• I'm not comfortable with the conclusioin on page 5 that your data 'indicates that at the time point of scission, the clathrin coat of nascent vesicles is still incomplete'. Other explanations might be the relative kinetics of scission vs CCP growth (i.e. these structures are too transient to detect), or that deeply invaginated pits are sheered-off the membrane during sample preparation (there is evidence that most biochemically isolated CCVs are derived from sheered CCPs).

Response: __We extended the explanation for the absence of fully closed vesicles with the hypotheses mentioned by the reviewer on __Page 5, Lines 159-161.

• Bottom of page 5, can you briefly mention what data is shown in Supplemental Figure 2 (ie. Figure 2D and examples of likely non-endocytic CCPs shown in Supplemental Figure 2). When I read this, I questioned your speculation.

Response: __We clarified the cross reference to (now) Supplementary Figure 3 accordingly on __Page 6, Lines 184-185.

• Can you indicate N CCPs from N cells in the data in Tables 2-3 for fibroblasts and U2OS cells? Do you observe and have to ignore a larger number of flat/clustered CCPs in the fibroblasts?

Response: __We indicated the number of cells and sites per data set in the Table captions on __Page 36, Lines 51; 959; and 967. We did not quantify the number of flat/clustered, plaque like structures in our data sets. During data acquisition, we would specifically select cells with minimal number of these structures present, and even within this cell chose an area in the periphery exhibiting low number of plaques. Our data is therefore not ideal to reliably quantify plaque density between different cell lines. Qualitative observations showed that whilst we had to disregard a few cells from the U2OS and SK-MEL-2 cell-lines due to high plaque formation, the 3T3 fibroblasts were relatively straight forward to image, as few cells showed high plaque density. A recent study by Hakanpää et al., 2022 (bioRxiv) showed the decreased formation of plaques when cells were seeded on fibronectin. The fact that fibroblasts excrete their own fibronectin agrees well with our observations of relatively few 3T3 cells exhibiting extensive plaque formation.

• The last 3 paragraphs of the Introduction are results. The Introduction might best be used to review literature in more detail, discuss the reasons why uncertainty still exists and perhaps indicate how the methods applied here will help.

Response: __We re-wrote the last 3 paragraphs of the introduction, now clearly stating the knowledge gap in the field, and what methods would be required to bridge it (Page 3, Lines 80-102).__

Reviewer #1 (Significance (Required)):

This is another excellent addition to a growing list of papers seeking to define the process of curvature generation at endocytic clathrin coated pits. In my opinion, its impact would be increased by better integrating the results presented here with other studies and methods, including the recent paper by Willy et al and the large body of literature on coated pit dynamics, some of which might be relevant in interpreting results, or at least placing them in a real vs pseudo-temporal perspective. The methods introduced and the quality of imaging, modeling and quantification further increase the study's significance. The finds will be of interest to those in the CME field, those studying membrane curvature generation in other contexts, those modeling CME, vesicle formation and curvature generation and those using SMLM to discern the structure of macromolecular assemblies.

Reviewer expertise: Clathrin-mediated endocytosis (Sandra Schmid)

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

Summary In this article, the authors aimed to investigate the dynamic of clathrin lattice during clathrin-mediated endocytosis (CME). Overall, they successfully achieved the goal by observing a large number of clathrin spots from several cell lines with 3D single-molecule localization microscopy (SMLM). With the help of this high-resolution imaging technique, they were able to describe the physical properties of each spot and reconstruct the assembly and remodeling of the clathrin coat. Moreover, by comparing the constant area/curvature model with their own data, the authors highlighted that neither of the prevailing models perfectly explained what they observed and proposed 'cooperative curvature model'. With the novel model, the authors were able to reconstruct the clathrin coat remodeling in different cell lines and concluded that the simultaneously bending and assembly of the clathrin coat is a homogenous property of endocytosis.

The experiments and analytical procedures are well-designed and performed, and the manuscript is well-organized. The conclusion 'cooperative curvature model' was deduced from a large amount of data analysis and clearly stated in the text. I would like to recommend its publication if the following issues will be clarified.

Major comments:

1. The authors compared the morphological dynamics of clathrin-coated pit among three different cell lines (SK-MEL-2, U2OS, and 3T3) and found slight differences. As U2OS cells was derived from bone tissues, it has different mechanical properties (membrane tension, elasticity of cortical layer, etc..). It would be interesting to consider those mechanical properties in understanding the morphology (Figure 2) and progress (Figure 4) of the CME. Considering the fact that the bending energy of the plasma membrane is dependent on the membrane tension, they may be able to find some relationships between mechanical properties of the cell cortex and CME.

__Response: __We thank the reviewer for this comment and very much agree that the relationship between mechanical properties structural adaptation of the endocytic machinery is a highly interesting question. We came to the same conclusion and are therefore exploring this relationship at the moment. This is however not a straightforward task, and the complex nature of plasma membrane mechanics necessitates careful experimental design. It is therefore outside the scope of this publication. We do think this point further highlights the potential of the method presented here, as it allows the investigation of additional principles in clathrin-mediated endocytosis mechanics. We do hope to share our insights on this topic soon.

In Figure 4, the authors estimated the progression of the CME using the frequency distribution of theta. However, I wonder how they handled the events which were aborted in the middle of the CME. It had been suggested that some CME are aborted during the initial step of the CME. The authors should consider (at least discuss) those abortive events, which can disturb the analysis.

Response: __Generally speaking, abortive events (now discussed on __Page 14, Lines 405-411) are characterized as dim and short-lived structures in live-cell acquisitions. As the earliest structures in our data set already contain half the final coat area, we are most likely not capturing these abortive events in the first place (potential technical reasons for not capturing earlier structures are discussed on Page 14, Lines 385-395).

Abortive events throughout the later process of endocytosis would, according to our data, still follow the same mechanistic trajectory as other sites. They could potentially slightly skew our pseudotime analysis, as they would result in an overestimation of specific endocytic stages. The overall mechanistic insight of our work would not be greatly affected, as curvature generation would still occur according to the same trajectory. Due to the low impact on our overall results we do not discuss these late abortive events further.

Minor comments:

1. Page5, result section 2. The author should further explain why vesicles from trans Golgi could responsible for the small disconnected set of data points corresponding to the vesicles with larger curvatures.

Response: __We extended our explanation for the presence of non-endocytically derived structures in our data set on __Page 6, Lines 184-189. We further extended the supplementary information with an additional experiment (Supplementary Figure 4), highlighting the absence of AP2-positive structures within the disconnected population. As AP2 is a specific marker for CME, these results further solidify our hypothesis. Further experiments would be required to determine their exact origin, and are outside of the scope of this publication.

Page7, line 6. The author assumed that the clathrin coat starts growing on a flat membrane. However, as is mentioned in the discussion, clathrin has been proved to have curvature sensing ability which could be further amplified by adapter proteins by several times (Zeno et al., 2021). So, it seems that clathrin preferred a highly curved membrane instead of a flat one. Is it still reasonable to make this assumption?

Response: __Whilst our assumption states the growing of clathrin coat on flat membranes, we do not restrict our model to an intercept through 0, and it would therefore still hold true even in the case of growth starting on slightly bent membranes. The impact of the preference of clathrin for curvature is considered as a potential mechanistic explanation for the positive feedback in curvature generation described by our model. We therefore already cite the reference mentioned by the reviewer on __Page 8, Line 224.

As we do observe flat structures in our data set (discussed more in detail now on Page 14, Lines 396-404), we still think the assumption of early flat growth holds true.

Page 9, result section 4. In the sentence: "we effectively generated the average trajectories of how curvature, surface area, projected area and lattice edge change during endocytosis in SK-MEL-2 cells (Figure 4B-E)." Here I think the authors are describing Figure 4C-F.

__Response: __That is correct, an oversight on our part. We changed the cross-reference.

Page 11, discussion. In the sentence: "A deviation of the cross-sectional profile from a circle is nevertheless preserved in the averaging (Supplementary Figure 5)." I didn't see supplementary figure 5 in the article.

Response: __We changed the cross-reference. We were addressing a subsection of __Supplementary Figure 8.

Reviewer #2 (Significance (Required)):

From a vast amount of microscopic images and data analysis, the manuscript gives a clear model on the progress of the CME, which integrates two opposing models; constant area and constant curvature models. This is a big progress in our understanding of the molecular mechanism of CME, and will attract many researchers in the field of cell biology. From a viewpoint of my expertise (molecular imaging of plasma membrane and endocytic processes), this manuscript has significant impact on the related research fields.

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

Summary: The authors used single-molecule localization microscopy of clathrin in fixed cells (2 human cell lines, one mouse) to capture snapshots of a clathrin-mediated endocytosis (CME), fitted these localizations to a geometric model of a forming vesicle, and used these fitted measurements to test existing models of clathrin-mediated vesicle formation before refining their own. Specifically, the closing angle, a measure of vesicle completeness, was used as a proxy for growth-stage of the vesicle such that the many captured snapshots could reconstruct a pseudo-timeline with an unknown parameterization of time on closing angle. Two standard models of CME vesicle formation, where the surface area is kept constant or where the curvature is kept constant, were examined and determined to be incommensurate with the pseudo timelines of curvatures and surface area. The authors then describe their own model for CME vesicle formation, in which neither surface area nor curvature are constant in evolution of the vesicle, and cooperative forces are hypothesized to non-linearly modulate the curvature-growth as a function of closing angle. Additionally, by binning snapshots and then aligning, scaling, and azimuthally smoothing each bin, they reconstruct representations of distinct endocytic stages.

Major comments:

Most results are quite convincing, and the authors do a nice job of displaying examples of SMLM data, both with fit results as well as example clathrin assemblies that are too far removed from their budding-vesicle model to be included for analysis, for example. It is also worth noting that the clathrin images themselves appear to be very high-quality - clearly, as detailed in the methods, attention was given to each step of the imaging and reconstruction process.

While the presented cooperative curvature model seems reasonable and surely fits the curvature-, surface area-, and rim length-vs. closing angle data better than the simplistic constant surface-area and constant curvature models, it also has more parameters, namely: gamma (the initial rate of curvature change with closing angle) and H_0 (the final preferred curvature). It would be appropriate to calculate an information criterion (e.g. Bayesian), using an assumption of Gaussian-distributed errors (presumably the data fitting in R was least squares, so this would match) to justify the additional parameters.

Response: __This is an important observation by the reviewer. Indeed, our model uses one more parameter compared to the models we compare it with. To justify this, we performed the calculation as suggested by the reviewer, and found that the cooperative curvature model (CoopCM) indeed results in the lowest BIC (__Supplementary Notes). We therefore are confident that out of the three models tested in this work, our CoopCM fits best to the underlying experimental data (Page 8, Lines 232-235).

A related issue relates to the error in the extracted value of the closing angle from a single 3D reconstruction - the error distribution should be quantified for this very important parameter. The errors in the other parameters extracted from the fits are less important, but would enhance the paper.

Response: __We thank the reviewer for pointing out the importance of the estimation error of the key parameter closing angle. To address this point, based on the geometrical model, we simulated clathrin-coated structures with closing angles evenly distributed across the entire range (0-180°). This realistic simulation represents the data quality (e.g., localization precision and labeling efficiency) of the experimental data (corresponding methods are included in __Pages 22- 23, Lines 679-706). The result of fitting these structures using LocMoFit shows an unbiased estimation with small spread of the error (overall STD = 2.82°; see the newly included Supplementary Figure 2a).

Pseudo-temporal sorting on closing angle makes sense and I appreciate the authors mentioning potential caveats to the monotonicity, etc. However, a comment about the impact of closing angle errors on the pseudo-time determinations would be helpful. The agreement of theta-rank plots with the hypothesized sqrt(t) scaling is reassuring.

I additionally appreciate the robustness of fitting a geometric structure from localizations rather than relying on pseudo-temporal sorting on clathrin count extracted from localization-merging of multi-blinking emitters.

Response: __The pseudo-temporal sorting is based on the precisely estimated closing angle, and therefore is also precise, as the distribution of the fitted closing angle has no significant distortion compared to the expectation (__Supplementary Figure 2b).

The authors did a nice job of qualifying their more speculative claims, in particular I appreciated their mentioning the possibility that smaller clathrin coats could be below their detection limit.

The authors state a set of data points in suppl. figure 2D (and suppl. Fig 3A-C) are "likely" small clathrin-coated vesicles from the trans Golgi. I appreciate the examples rendered in that figure so a reader can appraise, but if they have my background they might not know how reasonable exclusion of this data is from model testing. This claim could be rephrased or the rationale expanded upon to justify the Golgi hypothesis.

Response: __We agree with the reviewer and further expanded on our hypothesis on the origin of the structures within the disconnected cloud of data points (Page 6, Lines 184-189). We further performed an additional experiment (Supplementary Figure 4)__, where we simultaneously imaged the clathrin coat at high resolution, and the CME specific AP2 complex tagged with GFP at diffraction limited resolution. We observed that there were no AP2-GFP positive structures present in the disconnected cloud of our data set, and conclude that these structures indeed must originate via a different pathway.

The data and methods are presented such that they could be reproduced, and replicating their experiment in multiple cell lines, across multiple species, would seem to be adequate replication. As mentioned above, the statistical analysis of whether the model complexity is justified by improved goodness of fit is currently missing but can readily be checked and added.

Minor comments:

Last paragraph of the introduction, positive feedback is mentioned but not the slowing down as preferred curvature is realized (inclusion of which might help foster a clearer understanding of the model early on).

Response: __We now mention the slowing down towards a preferred curvature in our introduction on __Page 3, Lines 100-102.

In Fig. 1, please state in the figure caption what is being displayed in the two large panels and what is the color map. Is this the 3D data from the overlapping elliptical Gaussians projected on the plane in a "hot" map? Further, in the top right small panels, are the x-y images projections of all z, or measured at a specific z?

Response: __We adjusted Figure 1 and the figure caption to clearly explain what is mentioned in each superresolution panel. The exact details for image rendering, including the color map and gaussian blurring of the localization coordinates are now described in the methods on __Page 21, Lines 625-627. Ultimately, the x-y images represent an enlarged view of the projections as visible in the previous two panels. We hope that rephrasing of Figure 1 legend clarifies this accordingly.

In Eqn. (1), epsilon is not defined.

Response: __The definition is mentioned on __Page 8, Line 210, right before the equation, same as for kon.

For the theta-rank plots (Fig4 B, SFig D-F ii) moving the theta(t)=sqrt(t) red curves behind sorted theta data would make the data easier to see.

__Response: __We adjusted the Figures according to the reviewer's suggestion.

"Laser" in sentence about the speckle reducer should probably be plural.

Response: __We corrected this grammar mistake, and changed “laser” to “lasers” on __Page 20, Line 586.

I would like to see the "custom" algorithm based on redundant cross-correlation for drift correction briefly described.

Response: __We added an explanation on the algorithm used for the drift correction on __Pages 20-21, Lines 611-617.

A legend for supplemental figure 3 A-C would be nice.

Response: __We added a legend for the various models in (now) __Supplementary Figure 5, and further made some clarifications in the figure caption.

If the definition of the abbreviation flat-to-curved-transition as FTC was explicit I missed it.

Response: __As we do not use this abbreviation anywhere else in the manuscript, we removed it from the __Supplementary Note to avoid confusion.

Resolution of 20 and 30 nm (laterally and axially, respectively) was quoted once towards the beginning of the manuscript as being an improvement resulting from the localization method described in Li et al., 2018. Resolution can be difficult to speak about precisely, but the methods section would seem to indicate that localizations are filtered at 20 nm lateral localization precision (potentially 30 nm axially?), and I think the authors could consider rephrasing to depict this unless I am missing elsewhere a description of the resolution metric being used.

Response: __The original 20 and 30 nm resolution (laterally and axially) was calculated based on the median localization precision values in x-y and z for a representative image, using the FWHM approach (described in Methods __Page 21, Lines 621-624). After consideration of the reviewer's question, we found the modal value to be a better quantity to calculate the resolution, and changed this in the text accordingly (Page 4, Lines 113-115, and Methods Page 21, Lines 621-624).

Reviewer #3 (Significance (Required)):

Proteins involved with inducing curvature in membranes are in general very exciting targets for localization microscopy, yet still for many systems questions remain unanswered. The authors tackle one such question in this manuscript. In other, unresolved, discussions, the posed hypotheses are quite similar to the simplistic models surpassed in this work (e.g. that curvature scales linearly with local protein copy number, or that surface area scales linearly with local protein copy number). The idea of cooperativity may be useful for others to consider, and the authors additionally demonstrate a seemingly smooth workflow using their separately described tools (primarily LoMoFit; Wu et al. 2021).

I myself am not an expert on CME or vesicle trafficking. My background is primarily in SMLM method development and SMLM / fluorescence image analysis. From my perspective, the novelty of the biological conclusions appears to be the authors' specific cooperative model and the presence of two structural states which are enriched (closing angle 70{degree sign} and 130{degree sign}). As referenced, and authors F. Frey and U. S. Schwarz nicely present in Bucher et al. 2018, the constant curvature and constant surface area models are known to be inaccurate descriptions of CME evolution, and further it is also known that clathrin first assembles small flat structures before beginning to curve the membrane. However, the 3D super-resolution imaging and direct evaluation of a 3D model geometry in this work is a nice extension of the 2D super-resolution imaging and projection evaluation in the authors' previous work studying endocytosis through ensemble averaging in yeast (Mund et al. 2018) as well as the analysis on projections in Bucher et al. 2018. Fully 3D treatment of the clathrin structures allows the authors to orient asymmetric assemblies such that they are averaged out in their ensemble reconstruction, and as they point out the molecular specificity afforded by a fluorescence-based technique ensures unbiased segmentation of clathrin-involved endocytic sites. In other words, while this work does not describe a technical advance not already described elsewhere, it sets a nice example for those researching protein-membrane interactions of how to leverage the right tools to clearly and directly answer their questions. With their additional work to make these tools extensible to other geometries, multiple color channels, etc., I expect their work to inspire quality studies in other systems. That significance is complementary to their proposal of a reasonable model for the geometric evolution of CME.

References:

Maximum-likelihood model fitting for quantitative analysis of SMLM data, Yu-Le Wu, Philipp Hoess, Aline Tschanz, Ulf Matti, Markus Mund, Jonas Ries, bioRxiv 2021.08.30.456756; doi: https://doi.org/10.1101/2021.08.30.456756

Bucher, D., Frey, F., Sochacki, K.A. et al. Clathrin-adaptor ratio and membrane tension regulate the flat-to-curved transition of the clathrin coat during endocytosis. Nat Commun 9, 1109 (2018). https://doi.org/10.1038/s41467-018-03533-0

Markus Mund, Johannes Albertus van der Beek, Joran Deschamps, Serge Dmitrieff, Philipp Hoess, Jooske Louise Monster, Andrea Picco, François Nédélec, Marko Kaksonen, Jonas Ries, Systematic Nanoscale Analysis of Endocytosis Links Efficient Vesicle Formation to Patterned Actin Nucleation, Cell, 174, 4, (2018). https://doi.org/10.1016/j.cell.2018.06.032.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this article, the authors aimed to investigate the dynamic of clathrin lattice during clathrin-mediated endocytosis (CME). Overall, they successfully achieved the goal by observing a large number of clathrin spots from several cell lines with 3D single-molecule localization microscopy (SMLM). With the help of this high-resolution imaging technique, they were able to describe the physical properties of each spot and reconstruct the assembly and remodeling of the clathrin coat. Moreover, by comparing the constant area/curvature model with their own data, the authors highlighted that neither of the prevailing models perfectly explained what they observed and proposed 'cooperative curvature model'. With the novel model, the authors were able to reconstruct the clathrin coat remodeling in different cell lines and concluded that the simultaneously bending and assembly of the clathrin coat is a homogenous property of endocytosis. The experiments and analytical procedures are well-designed and performed, and the manuscript is well-organized. The conclusion 'cooperative curvature model' was deduced from a large amount of data analysis and clearly stated in the text. I would like to recommend its publication if the following issues will be clarified.

Major comments:

1. The authors compared the morphological dynamics of clathrin-coated pit among three different cell lines (SK-MEL-2, U2OS, and 3T3) and found slight differences. As U2OS cells was derived from bone tissues, it has different mechanical properties (membrane tension, elasticity of cortical layer, etc..). It would be interesting to consider those mechanical properties in understanding the morphology (Figure 2) and progress (Figure 4) of the CME. Considering the fact that the bending energy of the plasma membrane is dependent on the membrane tension, they may be able to find some relationships between mechanical properties of the cell cortex and CME.
2. In Figure 4, the authors estimated the progression of the CME using the frequency distribution of theta. However, I wonder how they handled the events which were aborted in the middle of the CME. It had been suggested that some CME are aborted during the initial step of the CME. The authors should consider (at least discuss) those abortive events, which can disturb the analysis.

Minor comments:

1. Page5, result section 2. The author should further explain why vesicles from trans Golgi could responsible for the small disconnected set of data points corresponding to the vesicles with larger curvatures.
2. Page7, line 6. The author assumed that the clathrin coat starts growing on a flat membrane. However, as is mentioned in the discussion, clathrin has been proved to have curvature sensing ability which could be further amplified by adapter proteins by several times (Zeno et al., 2021). So, it seems that clathrin preferred a highly curved membrane instead of a flat one. Is it still reasonable to make this assumption?
3. Page 9, result section 4. In the sentence: "we effectively generated the average trajectories of how curvature, surface area, projected area and lattice edge change during endocytosis in SK-MEL-2 cells (Figure 4B-E)." Here I think the authors are describing Figure 4C-F.
4. Page 11, discussion. In the sentence: "A deviation of the cross-sectional profile from a circle is nevertheless preserved in the averaging (Supplementary Figure 5)." I didn't see supplementary figure 5 in the article.

Significance

From a vast amount of microscopic images and data analysis, the manuscript gives a clear model on the progress of the CME, which integrates two opposing models; constant area and constant curvature models. This is a big progress in our understanding of the molecular mechanism of CME, and will attract many researchers in the field of cell biology. From a viewpoint of my expertise (molecular imaging of plasma membrane and endocytic processes), this manuscript has significant impact on the related research fields.

Author Response

Reviewer #1 (Public Review):

The authors attempt to optimize the FluoroSpot assay to allow for the assessment of cross-reactive antibodies targeting conserved epitopes shared by multi-allelic antigens and those specific to unique antigen variant at the B cells level. This is a critical aspect to consider when identifying targets of a broad range of cross-reactive antibody for vaccine development and the antigen VAR2CSA used in this work is one that will benefit from the method described in the manuscript.

Overall, this is a method manuscript with extensive detail of the assay validation process. The description of the assay performance steps using, first monoclonal antibodies and later hybridoma/immortalized B cells was important to understand conditions that can influence the antigen-antibody interactions in the assay. This multiplex approach can assess the cross-reactivity of antibody to up four allelic variants of an antigen with the possibility to explore the affinity of antibody to a particular variant using the RSV measurements. The validation of the assay with PBMC from malaria exposed donors both men and women (that naturally acquired high titer of antibodies to VAR2CSA during pregnancy) is a strength of this work as this is in the context of polyclonal antibodies with more heterogenous antibody binding specificities.

The ability of the assay to detect cross-reactive antibodies using all four tags appear highly variable even in the context of monoclonal antibody targeting the homologous antigen labelled with all 4 tags.

We understand the concern for variability, but we think that in general the assay was very consistent. Regardless of the configuration used, we detected strikingly comparable number of spots/well, especially when the homologous antigen labelled with four tags was used (Figure 2A). Similar consistency has been previously reported when a similar assay was used to study cross-reactivity in dengue-specific antibodies.

Overall, it appears that the assessed antibody reactivity with TWIN tagged antigens was relatively low and this needs to be explained and discussed as the current multiplex method, as it is, might just be optimized for study of cross-reactive antibodies to 3 antigens.

The LED380 (used to detect and visualize the TWIN tag) indeed gave more background than the other three detection channels. We normally observed a ring of fluorescence at the edge and the middle of the wells, accompanied by lower intensity of the spots. These two characteristics are apparent in the figures and RSV plots presented in the manuscript. In an attempt to reduce these issues, we attempted to substitute the TWIN tag for a BAM tag detected with a peptide-specific antibody (data not presented). However, that approach did not improve the readout and we therefore decided to keep the TWIN-StrepTactin pair for all the experiments. Importantly, even with these issues, routine manual inspection of the wells confirmed the Apex software automatically and efficiently counted “real” spots giving us confidence on the performance of the assay. We acknowledge that exclusion of the LED380 data would lead to higher assay accuracy. However, it would result in reduced ability to assess broad antibody cross-reactivity, which was the primary objective of our study. We have added text briefly discussing this to the revised manuscript (lines 154-160).

As acknowledged by the authors, the validation of this assay on PBMC from only 10 donors (7 women and 3 men) is a caveat to the conclusion and increasing this number of donors (the authors have previously excelled in B cells analyses of PfEMP1 proteins and would have PBMC readily available) will strengthen the validity of this assay.

We thank the reviewer for this comment and agree the number of donors tested is far from sufficient to provide any conclusive evidence regarding frequencies of VAR2CSA-specific and cross-reactive B cells in the context of placental malaria. However, we firmly believe that the validation of the assay – which was the objective of the study – is sufficient, especially because we included human B-cell lines isolated from donors naturally exposed to VAR2CSA-expressing parasites. Futures studies including more donors and full-length VAR2CSA antigens are certainly warranted. As the performance of assay has now been validated (this manuscript) to our satisfaction, we are indeed planning such studies.

Reviewer #2 (Public Review):

The manuscript describes the development of a laboratory-based assay as a tool designed to identify individuals who have developed broadly cross-reactive antibodies with specificity for regions that are common to multiple variants of a given protein (VAR2CSA) of Plasmodium falciparum, the parasite that causes malaria. The assay has potential application in other diseases for which the question ofacquisition of antibody-mediated immunity, either through natural exposure or through vaccination, remains unresolved.

From a purely technical/methodological viewpoint, the work described is of high quality, relying primarily on the availability of custom-designed, in-house-derived protein and antibody reagents that had, for the most part, been validated through use in earlier studies. The authors demonstrate a high degree of rigour in the assay development steps, culminating in a convincing demonstration of the ability to accurately and reproducibly quantify cross-reactive antibody types under controlled conditions using well-characterized monoclonal antibodies.

In a final step, the authors used the assay to assess the content of broadly cross-reactive antibodies in samples from a small number of malaria-exposed African men and women. Given that VAR2CSA is a parasite-derived protein that is exclusively and intimately involved in the manifestation of malaria during pregnancy, with specific localisation to the maternal placental space, the premise is that antibodies -including those with cross-reactive specificities - should be almost exclusively detectable in samples from women, either pregnant at the time of sampling or having been pregnant at least once. The assay functioned technically as expected, identifying antibodies predominantly in women rather than men, but it failed to identify broadly cross-reactive antibodies in the women's samples used, only revealing antibodies with specificity for just one of the different variants used. The latter result could have two mutually non-exclusive explanations. On the one hand, the small number of women's samples (7) screened in the assay could simply be insufficient, demanding the use of a much larger panel. On the other hand, for technical reasons the assay involves the use of only relatively restricted parts of the VAR2CSA protein, and this particular aspect may represent its primary limitation. In earlier work, the authors did identify broadly cross-reactive antibodies in samples from African women, but that work relied on the use of the whole VAR2CSA protein present in its natural state embedded in the membrane of the infected red cell, or as a complete protein produced in the laboratory. The important point being that the whole protein likely interacts with antibodies that recognize protein structures that the isolated smaller parts of the whole protein used in the assay fail to reproduce, and that the cross-reactive antibodies identified recognize these structures that are conserved across different VAR2CSAvariants. The authors recognize these potential weaknesses in their discussion of the results. It is also possible that VAR2CSA variants expressed by parasites from geographically-distinct regions (Africa, Asia, South America) are themselves distinct, and this aspect could also have affected the outcome, since the variant protein sequences used in the assay were derived from parasites originating in these different regions.

The assay could find application in the malaria research field in the specific context of assessments of antibody responses to a range of different parasite proteins that are, or have been, considered candidates for vaccine development but for which their extensive inherent allelic polymorphism has effectively negated such efforts.

We thank the reviewer for the kind evaluation. We fully acknowledge the need for more comprehensive studies to assess the robustness of the pilot data regarding antibody cross-reactivity after natural exposure in the present study, which was aimed to document the performance of the complicated multiplexed assay rather than to provide such evidence. As mentioned above, we are currently planning such a study. We also acknowledge the need to assess the degree of cross-reactivity to full-length antigens rather than domain-specific components of them. This is obviously particularly true for large, multi-domain antigens such as PfEMP1 (including VAR2CSA). Such an exercise is complicated by the need for appropriately tagged antigens. We are intrigued by the apparent discrepancy between the degree of antibody cross-reactivity in depletion experiments using individual DBL domains of VAR2CSA (low cross-reactivity) versus full-length VAR2CSA antigens (very substantial cross-reactivity) reported by Doritchamou et al., and are keen to apply our approach to explore that finding. Therefore, as also mentioned above, we are currently planning a study employing tagged full-length VAR2CSA allelic variants as well.

Reviewer #1 (Public Review):

The authors test whether neurons in V1 show "multiplexing", which means that when two stimuli A and B are presented inside their receptive fields (RFs), the neuronal response fluctuates across trials between coding one of the two, leading to a bimodal spike count histogram. They find evidence for this "mixture" model response in a subset of V1 neurons. They next test whether the spike count noise correlations (Rsc) vary between pairs of neurons that prefer the same versus different stimuli, and show that Rsc is positive for neurons that prefer the same stimulus but negative for neurons that prefer different stimuli.

While this paper shows some intriguing results, I feel that there are a lot of open questions that need to be addressed before convincing evidence of multiplexing can be established. These points are discussed below:

1. The best spike count model shown in Figure 2C is confusing. It seems that the number of "conditions" is a small fraction of the total number of conditions (and neurons?) that were tested. Supplementary Figure 1 provides more details (for example, the "mixture" corresponds to only 14% of total cases), but it is still confusing (for example, what does WinProb>Min mean?). From what I understood, the total number of neurons recorded for the Adjacent case in V1 is 1604, out of which 935 are Poisson-like with substantially separated means. Each one has 2 conditions (for the two directions), leading to 1870 conditions (perhaps a few less in case both conditions were not available). I think the authors should show 5 bar plots - the first one showing the fraction for which none of the models won by 2/3 probability, and then the remaining 4 ones. That way it is clear how many of the total cases show the "multiplexing" effect. I also think that it would be good to only consider neurons/conditions for which at least some minimum number of trials are available (a cutoff of say ~15) since the whole point is about finding a bimodal distribution for which enough trials are needed.

2. More RF details need to be provided. What was the size of the V1 RFs? What was the eccentricity? Typically, the RF diameter in V1 at an eccentricity of ~3 degrees is no more than 1 degree. It is not enough to put 2 Gabors of size 1 degree each to fit inside the RF. How close were the Gabors? I am confused about the statement in the second paragraph of page 9 "typically only one of the two adjacent gratings was located within the RF" - I thought the whole point of multiplexing is that when both stimuli (A and B) are within the RF, the neuron nonetheless fires like A or B? The analysis should only be conducted for neurons for which both stimuli are inside the RF. When studying noise correlations, only pairs that have overlapping RFs such as both A and B and within the RFs of both neurons should be considered. The cortical magnification factor at ~3-degree eccentricity is 2-2.5mm/degree, so we expect the RF center to shift by at least 2 degrees from one end of the array to the other.

3. Eye data analysis: I am afraid this could be a big confound. Removing trials that had microsaccades is not enough. Typically, in these tasks the fixation window is 1.5-2 degrees, so that if the monkey fixates on one corner in some trials and another corner in other trials (without making any microsaccades in either), the stimuli may nonetheless fall inside or away from the RFs, leading to differences in responses. This needs to be ruled out. I do not find the argument presented on pages 18 or 23 completely convincing, since the eye positions could be different for a single stimulus versus when both stimuli are presented. It is important to show that the eye positions are similar in "AB" trials for which the responses are "A" like versus "B" like, and these, in turn, are similar to when "A" and "B" are presented alone.

4. Figures 5 and 6 show that the difference in noise correlations between the same preference and different preference neurons remains even for non-mixture type neurons. So, although the reason for the particular type of noise correlation was given for multiplexing neurons (Figure 3 and 4), it seems that the same pattern holds even for non-multiplexers. Although the absolute values are somewhat different across categories, one confound that still remains is that the noise correlations are typically dependent on signal correlation, but here the signal correlation is not computed (only responses to 2 stimuli are available). If there is any tuning data available for these recordings, it would be great to look at the noise correlations as a function of signal correlations for these different pairs. Another analysis of interest would be to check whether the difference in the noise correlation for simply "A"/"B" versus "AB" varies according to neuron pair category. Finally, since the authors mention in the Discussion that "correlations did not depend on whether the two units preferred the same stimulus or different", it would be nice to explicitly show that in figure 5C by showing the orange trace ("A" alone or "B" alone) for both same (green) and different (brown) pairs separately.

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Reply to the reviewers

We thank the reviewers for their constructive comments and are pleased that all reviewers share our opinion, that the present study “makes an important contribution to the molecular architecture of mitochondria”, is in addition “an important advancement in our understanding of the mechanism by which Cqd1 regulates CoQ distribution” and will “thereby appealing to the broad readership of the journals”. We are convinced that addressing the important points raised by the reviewers will further strengthen the manuscript and result in additional significant insights in the molecular function of Cqd1.

Reviewer #1:

The major concerns affecting the conclusions are: 1) Experimental evidence is lacking on the contribution of contact site formation by Cqd1 to the effects on mitochondrial architecture and respiration-dependent growth. Determining the effects of the overexpression of the kinase-dead mutant on mitochondrial morphology and contact site formation with Por1-Om14 can address that.

We thank reviewer #1 for raising these important points. Indeed, the various functions of Cqd1 might be independent from each other and so far we cannot distinguish between them. As suggested by the reviewer we will analyze the effect of overexpression of CQD1 in the Dups1 deletion mutant and make use of the point mutant in the conserved ATP binding domain which cannot complement the phenotype of the Dups1 Dcqd1 double deletion mutant. We generated a yeast mutant strain expressing Om14-3xHA in the absence of wild type Cqd1. Expression of the cqd1(E330A) mutant in the Om14-3xHA background and subsequent immunoprecipitation will allow us to test whether ATP binding is also essential for contact site formation. Preliminary experiments showed that the overexpression of cqd1(E330A) in the Dcqd1 deletion background results in a growth defect comparable to that caused by overexpression of CQD1 WT. Therefore, we think it might be more promising to analyze the interaction of Om14 and Cqd1 E330A at wild type level in order to avoid pleiotropic effects.

In addition, we will further characterize the cqd1(E330A) mutant by analyzing the effect of its overexpression on mitochondrial morphology, cell growth and assembly of MICOS and F1FO ATP synthase in the Dcqd1 deletion background.

2) Related to point #1, Cqd1 overexpression in deltaUsp1 cells could have addressed whether the role of Cqd1 in contact sites and mitochondrial architecture is independent of its role on CoQ distribution and phospholipid metabolism. Further characterization of the kinase-dead Cqd1 mutant on CoQ distribution, contact sites, mitochondrial archictecture and phsophsolipid metabolism might help discerning how these activities can be separated.

We agree that the related points 1) and 2) raised by reviewer #1 are important and addressed our plans in the response on point 1).

3) It is unclear how both Cqd1 overexpression and deletion induce mitochondrial fragmentation. Performing live cell imaging with a mitochondrial-phoactivatable GFP to measure mitochondrial fusion rates could help discerning the causes for fragmentation. It is a possibility that overexpression induced fragmentation by activating fission without changing fusion, while deletion induced fragmentation by blocking fusion.

We thank reviewer #1 for bringing up this point. Perhaps our explanation in this respect was too short. Fig. 4E shows that deletion of CQD1 does not result in altered mitochondrial morphology, however, deletion of CQD1 in the Dups1 background leads to virtual complete fragmentation of the mitochondrial network. This is likely due to inhibition of mitochondrial fusion through disturbed processing of the fusion protein Mgm1 (see Fig. 4D). In contrast, overexpression of CQD1 does NOT result in formation of small mitochondrial fragments, but in formation of huge mitochondrial clusters which in addition contain a large proportion of ER membranes. So, we don’t think that this phenotype is related to either enhanced fission or reduced fusion. We will clarify this point in text of the revised manuscript.

Minor comment:

1) Figure 4 claims that mitochondrial function is impaired by ups1 deletion, which Cqd1 deletion exacerbates. However, no respiration data is shown in figure 1, only measurements of mitochondrial architecture are shown. Thus, oxygen consumption measurements are needed to claim effects on mitochondrial function.

We did not want to claim that mitochondria lose respiratory competence upon simultaneous deletion of CQD1 and UPS1. Actually, our results indicate that the Dups1 Dcqd1 double deletion mutant grows like wild type on complete medium containing glycerol. Therefore, respiration is not impaired in this mutant. However, mitochondrial function is not restricted to ATP production by oxidative phosphorylation. The reviewer probably refers to Figure 4 where we show that mitochondrial biogenesis and dynamics are impaired in the Dups1 Dcqd1 double deletion mutant – the heading of the legend summarizes this as "mitochondrial function". We will be more precise in the revised version on this point and add a panel showing growth of the mutant strain on non-fermentable carbon source to avoid any further confusion.

2) Some Western blots lack quantifications and statistical analyses of independent experiments.

It is correct that some quantification and the respective statistics were missing in the initially submitted manuscript. We will add the requested information in the revised version of the manuscript.

Reviewer #2:

I have the following concerns for the authors to consider. (1) Although biochemical evidence shows that Cqd1 is likely a factor that forms CS structures in mitochondria, it would make the manuscript stronger if the authors can observe uneven distribution of Cqd1 in the mitochondrial membranes (assessed by fluorescent microscopy or ideally high-resolution microscopy) and the presence of Cqd1 in the region of close apposition of the OM and IM by immunogold labeling for electron microscopy.

Two independent lines of evidence show that Cqd1 is a novel contact site protein: (i) it is found in the contact site fraction in density gradients (Fig. 6A), and (ii) it can be co-immunoprecipitated with outer membrane proteins (Fig. 6G, H, I). Furthermore, the co-IP is supported by cross-links of expected size (Fig. 6F). In sum, we feel that this is solid evidence to support our claim that Cqd1 is present in mitochondrial contact sites. However, it still might be interesting to check an uneven distribution of Cqd1 in mitochondria, as suggested by the reviewer. We will do this by 3D deconvolution fluorescence microscopy.

(2) Since the structural characterization of Cqd1 is important to understand its interactions with the OM proteins and other UbiB protein kinase-like family proteins, Coq8 and Cqd2, take different orientations, the membrane topology of Cqd1 should be experimentally analyzed. The authors state, "two hydrophobic stretches can be identified in the Cqd1 sequence, of which the first one (amino acids 125-142) might be a bona fide transmembrane segment" (lines 97-100); then is Cqd1 a single membrane spanning protein or two-membrane spanning protein?　　

Unfortunately, it was not possible to test the location of the N terminus experimentally because an N-terminally tagged variant of Cqd1 (tag inserted between presequence and mature part) turned out to be unstable. We consider it very unlikely that the second hydrophobic stretch is a transmembrane domain as it is rather short (only 11 amino acids). Furthermore, several Cqd1 homologs in other fungi, including Yarrowia lipolytica, Aspergillus niger and Schizosaccharomyces pombe, are lacking the second hydrophobic stretch. Therefore, we propose that the major part of Cqd1 including the protein kinase-like domain is exposed to the intermembrane space. We will point out this more clearly in the revised manuscript.

(3) The authors state, "conserved GxxxG dimerization motif (amino acids 504‐508)" (Fig. 1A caption), but this description needs a reference. The GxxxG motif was proposed to mediate transmembrane helix-helix association (https://doi.org/10.1006/jmbi.1999.3489), which is not consistent with the membrane topology proposed by the authors.

We thank reviewer #2 for this comment. It is correct that GxxxG motifs are usually present in transmembrane a-helices. However, there is information available indicating that these motifs may also be present in soluble proteins and are stabilizing dimeric interactions for instance in the homodimeric Holliday-junction protein resolvase (Kleiger et al., 2002; doi: 10.1021/bi0200763.). However, as this point is not critical for our conclusions we will remove the discussion of the GxxxG motif from the revised manuscript.

(4) What is the role of the kinase activity of Cqd1 in the CS formation? The effects of overexpression of Cqd1 (Fig. 7) should be tested for its E330A mutant.

We also thank reviewer #2 for raising this important point similar to reviewer #1. Please see our response to point 1) of reviewer #1.

(5) Is there stoichiometric as well as quantitative information on the 400 kD complex consisting of Cqd1, Por1 and Om14? Does the stoichiometry and amount of the complex depend on the growth condition? Does the complex contain other Por1 interacting IM proteins like Mdm31?

We appreciate that reviewer #2 points out this important aspect. It might well be that the amount of the Cqd1 containing complex depends on growth conditions since its presence might be important for phospholipid homeostasis, CoQ distribution and mitochondrial architecture and morphology which for sure strongly depend on growth conditions. Therefore, we will try to analyze the amount of the Cqd1 complex present in mitochondria isolated from yeast cells grown on different media by BN-PAGE. So far we do not have any information on the stoichiometry of this complex and we feel that an analysis would go beyond the scope of this study. We agree with reviewer #2 that Mdm31 is an obvious candidate for an interaction partner of Cqd1. We actually tested this by co-immunoprecipitation using Cqd1-3xHA or Mdm31-3xHA. However, none of these approaches resulted in successful co-isolation of the potential interaction partner. We will mention this result in the revised manuscript.

(6) For Fig. 7E, the authors state, "consistently, we observed dramatically increased mitochondria‐ER interactions Cqd1 overexpression", but this observation could be due to secondary effects because overexpression of Cqd1 itself already caused abnormal morphology of mitochondria.

We thank reviewer #2 for bringing up this important point. To check whether the increased mitochondria‐ER interactions are a secondary effect due to altered mitochondrial morphology we will analyze the mitochondria‐ER interactions in other mitochondrial morphology mutants by fluorescence microscopy. This will reveal whether abnormal mitochondrial morphology generally leads to disturbed ER structure.

(7) Since the antagonistic role of Cqd2 to Cqd1 was proposed, the results of the experiments for Cqd1 can be compared with those for Cqd2. For example, what will become of overexpression of Cqd2 instead of Cqd1 for Fig. 7? What is the lipid composition of the cqd1Dcqd2D double deletion mutant cells (the decreased PA level is recovered?)? Lines 424-425: In summary, overexpression of Cqd1 causes severe phenotypes on growth, formation of mitochondrial structural elements, and mitochondrial architecture and morphology. Is this phenotype affected by overexpression of Cqd2?

This point raised by reviewer #2 is very interesting. Our preliminary experiments and previously published data (Tan et al., 2013) indicate that overexpression of Cqd2 is also toxic and results in the formation of huge mitochondrial clusters. Therefore, we will extend our study and analyze the effect of overexpression of CQD2, either alone or in combination with overexpression of CQD1.

Reviewer #3:

1) The central point of the paper is that Cqd1 is part of a novel contact site between the inner and the outer membrane. Om14 and Por1 were identified as outer membrane components of this contact site by immunoprecipitation. The data look convincing but they were generated from targeted experiments to test the involvement of suspected proteins. Ideally, one would like to see a cross-linking mass spectrometry (XL-MS) experiment that identifies the physical interactions of Cqd1 without bias.

We thank reviewer #3 for acknowledging the presented data as convincing. Considering the significant amount of experiments planned for the revised version of the manuscript, we hope that reviewer #3 agrees that this point is not essential.

2) Could an analogous blot of the MICOS complex be added to Figure 6D?

Of course, we are happy to include BN-PAGE analysis showing the running behavior of MICOS next to the Cqd1 containing complex in Fig. 6D.

3) In the Introduction, a host of contact sites is mentioned, which are partly from older papers. I'm not sure whether this is the accepted view of the field. Also, newer data suggest that the permeability transition pore is derived from complex V rather than ANT, CK, and VDAC. The authors should double check in order to represent the current state of the art

We thank reviewer #3 for this comment. We will update this part according to the more recent literature.

Author Response

Reviewer #2 (Public Review):

First, I want to congratulate the author team on this manuscript, which I read with great pleasure. I think this will be a fine addition to the literature!

The present MS by Clement et al. provides a comprehensive overview of the brain shapes of lungfishes. Besides previously known/described brain endocasts, the work includes models and descriptions of previously undescribed taxa. Notably, all CT data are deposited online following best practices when working with digital anatomy. The specimen sample is impressive, especially as the sampled material is housed in museum all over the world. Although the sample size may seem numerically low (12 taxa), this actually is a comprehensive sample of fossil (and extant) lungfishes in terms of what's preserved in the first place.

The study at hand has several goals: (1) The description of lungfish brains for taxa that were previously undescribed; (2) the quantification of aspects of brain shape using morphometric measurements; (3) the characterization of brain shape evolution of lungfishes using exploratory methods that ordinate morphometric measurements into a morphospace.

The provided 3D data and descriptions will serve as valuable comparisons in future lungfish work. This type of data is imperial for palaeontological studies in general, and the anatomical information will be extremely valuable in the future. For example, anatomical characters related to brain architecture have been shown to be informative about phylogeny in the past, and the presented data may inform future phylogenetic studies. The quantification of brain shape via (largely linear) measurements is relatively simplistic, and can thus only detect gross trends in brain shape evolution among lungfishes. The authors describe several such trends - such as high variation in the olfactory brain region in comparison to other parts of the brain. The results and interpretations drawn from the authors are supported by their data, and the approach taken is valid, even if more sophisticated shape quantification methods (e.g. 3D landmarking) and analytical methods (e.g. explicit phylogenetic comparative methods) are available, which could provide additional insights in the future.

We agree with Reviewer #2 that 3D geometric morphometrics could have provided more sophisticated analytical methods. However, geometric morphometrics has some limitations with regard to the type of data that we analysed: (1) low sample size and (2) missing/incomplete data. In order to have a comprehensive coverage of the brain shape, it would have required to have numerous landmarks (and semilandmarks) to represent the complexity of brain shape.

First, our sample size (12 taxa) is low (although it is an impressive sample size when considering the type of data). Although there are no universal rule concerning the ratio “number of specimens / number of landmarks” (Zelditch et al., 2012), ideally the sample size must be from two to three times the number of landmarks. Thus, with a sample size of 12 we could have used ca. 4-6 landmarks which is very limited to describe complex shapes. In addition, in order to use geometric morphometrics (2D or 3D), the landmarks should be present on all the specimens. Because of the partial completeness of the studied fossils, the brain endocasts are not uniformly known for each species. Incomplete and deformed specimens prompt the removal of potential landmarks for analyses. Even using right-left reflexion of the endocasts, most specimens do not share all neurocranial information.

We agree with Reviewer #2 that a phylogenetic PCA could have provided interesting analytical perspectives. Phylogenetic PCA are available on standard PCA, it is uncertain that it can be used on Bayesian PCA and InDaPCA (this method has been published very recently, and we haven’t found much literature about it). However, we did not find an adaptation of phylogenetic PCA to the BPCA nor the InDaPCA; we even contacted Liam Revell, who created the phylogenetic PCA, about this issue.

The presented results and interpretations in this regard must be seen as a preliminary assessment of lungfish brain evolution, but it is clearly written and generally well performed.

A potential shortcoming of the paper is the lack of explicit hypothesis testing, which is not problematic per se, but puts limits on the conclusions the authors can draw from their data.

We decided to address the issues using exploratory methods rather than testing hypotheses. It is a more conservative approach, since it is the first quantitative analysis of dipnoan endocasts. Future analyses, will be able to formulate hypotheses based on our interpretation of our exploratory approach. We hope to stimulate such hypotheses testing, when in the future further dipnoans will be added; however, one has to remember that ossified neurocrania are known in Devonian dipnoans and one partially ossified neurocranium in a Carboniferous, the remaining dipnoans have cartilaginous neurocrania which limit the sample size from which endocast data could be gathered.

For example, the authors state that different anatomical parts of the labyrinth (particularly, the utricle with respect to the semicircular canals or saccule) may show modular dissociation from other labyrinth modules, based on the polarity of eigenvalue signs of the PCA analysis. I think this is fine as a first approximation, but of course there are explicit statistical tools available to test for modularity/integration, such as two-block partial least squares regression analysis (Rohlf & Corti 2000, Syst. Biol.). I don't see the lack of usage of such methods as problematic, because you cannot do everything in one paper, and the authors remain careful in their interpretation.

We agree with Reviewer #2 that different geometric morphometrics methods have been developed to look at variational modularity; one of the co-authors (RC) has been publishing a few papers on patterns of morphological integration and modularity in fishes (see Larouche, Cloutier & Zelditch, 2015, Evol. Biol.; Lehoux & Cloutier, 2015, J. Exp. Zool. Mol. Dev. Evol.; Larouche, Zelditch & Cloutier, 2018, Sci. Rep.). Interesting a priori hypotheses of brain modules could have been formulated and tested for modularity using for example Covariance Ratio (CR) and distance matrix approach. But still the low sample size and the incompleteness of the data are major constrains to test modularity. We would however endeavour to use such methods in future work as more complete material becomes available.

It may be advisable, however, to add the odd sentence or statement about how some findings are preliminary or hypothesized, and that these should receive further treatment and testing using other methods in the future. I think this approach is actually very rewarding, because then you can inspire future work by outlining outstanding research problems that arise from the new data presented herein.

We have now included an additional sentence early in the Discussion section stating: “We acknowledge that our investigation of lungfish brain evolution as elucidated from morphometric analysis of cranial endocasts is still preliminary in several respects. We hope that our study can inspire future work on the neural evolution of both fossil and extant lungfish.”

In the following, I comment on a few aspects of the manuscripts. These represent instances where I had additional thoughts or ideas on how to slightly improve various aspects of the manuscript.

1) Presentation of PCA results

The authors provide several PCA analyses (preliminary analyses on partial matrices, BPCA, InDaPCA), and are very explicit about the procedures in general. For instance, I appreciate they explicitely state using correlation matrices for PCA analyses due to the usage of different measurement units among their data.

Visually, the BPCA and InDaPCA are presented in figures 2 and 3, whereas the preliminary partial matrix PCAs are only reported as supplementary figures. While I don't object to any of this, I find the sequence of information given in the results section suboptimal.

The figures have now been substantially reorganised to include more within the main body text and not as Supplementary Information, and we hope that this improves the sequence of information within the manuscript.

The authors start by discussing the partial matrix analyses, although none of these analyses are visually/graphically depicted in the main text figures, and although their results do not seem to be of real importance for the narrative of the discussion. The other two PCA analyses actually are presented afterwards and separately, but they convey some common signals, particularly that the major source of variation seems to be a decreasing olfactory angle with increasing olfactory length, and a scaling relationship between all linear measurements (which all have the same eigenvector signs on the first PC axis). I wonder if an alternative way of presenting the PCA results would be better for this particular MS. For example, the authors could give "first level observations" first ("PCA analyses agree in X,Y,Y"), and then move to second order observations ("Morphospace of BPCA has some interesting taxon distribution with regard to chirodipterids"; "InDaPCA axis projections continuously retrieve clustering of specific variables"). I suspect this would shorten the text somewhat and could serve as a clearer articulation of the take home messages?

Accordingly with Reviewer #2, we have now provided “first level” observations based on the standard PCA. We added some further comments on the species distribution in the morphospaces.

2) Selection of PC axes for interpretation

You describe how you use the broken-stick method to decide how many PC axes are retained for the interpretation of results, which I agree is a good procedure. However, I have a few questions regarding this. First, in line 331 (description of InDaPCA) you state that the first three axes are non-trivial "based on the screeplot" - which got me confused because it sounds a bit like eyeballing off the screeplot. Have you used the broken stick method for all your PCA analyses?

Originally, we used both screeplot and broken-stick method, however, we are now solely using the broken stick method to determine the number of non-trivial axes. We agree with Reviewer #2 that this method is more rigorous than the scree plot. Our choice is greatly inspired by the studies of Jackson (1993, Ecology) and PeresNeto et al. (2005, Computational Statistics & Data Analysis). We have now edited the text so that our methods are clearer (and removed the text relating to the screeplot such as “based on the screeplot…”).

The second question relates to the results of the broken stick method, which I did not find reported. Unless I am mistaken, for the xth axis, the method sums the fractions of 1/i (whereby i = x..n; n = number of axes), and divides this number by n to get a value of expected variation per axis. This number is then compared with the actual value of variance explained by the axis. So for the 1st of 17 axes, the broken-stick expectation is = (1 + 1/2 + .. + 1/17) / 17. If you apply this to your BPCA, the third axis' value (i.e., (1/3 + ... + 1/17)/17) is 0.114, which is smaller than the reported 0.120 that PC3 explains. Thus, following the broken stick method, PC3 does explain more variation that expected (and should thus be retained, contra your comment in line 311 which refers to two non-trivial axes)?

We thank Reviewer #2 for the insightful evaluation of our paper who took the time to validate each step of our analyses. Effectively, we agree with Reviewer #2 that based on the broken stick method the third axis in nontrivial. The value for the third axis is 1,0531310. Thus, we are presenting these results as well as discussing the three PCA projections (axis 1 versus axis 2, axis 2 versus axis 3, axis 1 versus axis 3).

Related to this potential issue is the presentation of the BPCA results in Fig. 2: You present loadings of three PC axes, although only the first two are considered in morphospace bi-plots and although the text also mentions only two non-trival axes. If the third axis is indeed non-trivial, then the loading-presentation could be retained in the figure, but then the authors should consider showing a PC1 vs. PC3 plot in addition to the currently presented biplot showing the first and second axis only. If the third axis indeed is trivial, as currently suggested by the text, then showing the loadings is unnecessary.

We consider showing a biplot of PC1 vs PC3 unnecessary as those shown (PC1 vs PC2) already account for 83.4% of the variation captured. We have edited these figures so that the loadings related to PC3 have also now been omitted.

It would be great if you clarify the usage/application of the broken stick method for all your PCAs. An easy way to report the results may be the add a row to each of your PCA loading tables in the supplements, in which you divide the actual value of variation explained by the value expected under the broken stick method - this way, all axes which explain more variation than expected by the stick method have values larger than 1, and axes which explain less have values lower than 1.

We have taken this suggestion from Reviewer #2 on board and have now recalculated all values for the brokenstick method for each analysis; we also provide broken-stick values in their respective loading tables in the SI.

3) Missing commentary on allometry

In basically all PCA analyses, the first PC axis seems to be dominated by allometric size effects, given that all linear measurements have the same eigenvalue signs. The authors do acknowledge this (lines 314-316; 335-336), but offer no further comment on size effects/allometry.

We agree that normally the first axis represents variation related mainly to size changes and shape changes related to size (allometry). However, we are reluctant to assume that our first axis corresponds to evolutionary allometry. Among others, Klingenberg & Zimmermann (1992) and Klingenberg (1996) used standard PCA (or multi-group PCA) to disentangle evolutionary and ontogenetic allometry (as well as static allometry) mainly by analysing multiple specimens for each group (or species) in order to have a better repartition of the covariance. Since our sample is limited to 12 species, and that they are all represented by a single specimen (except for Dipterus), it would be difficult to clearly discriminate variation associated to allometry. Even in a case of ontogenetic allometry, a sample size of 12 would have been limited to unambiguously conclude any variation.

For example, it would be interesting to see how the linear measurements scale with overall head size. Similarly, the authors note that the semicircular canal measurements covary strongly, as do the utricle and saccule height/length measurements (paragraph line 346). Basically, it seems that the semicircular canal measurements scale with one another: as one gets bigger, so gets the other. It is interesting that the utricle does not seem to follow the same scaling pattern as the saccule and semicircular canals, and it would be good to hear if the authors think that there is a functional implication for this. Increases in utricular/saccular/semicircular canal sizes are usually explained by increased sensitivity - so is an increased utricular size a compensatory development to decreased semicircular canal+saccule size to retain an overall level of sensitivity, or does it maybe related to a relative change of importance of the specific functions, e.g. increased importance of linear accelerations in the horizontal plane with simultaneous decrease of importance of angular and vertical accelerations?

We thank Reviewer 2 for this suggestion about overall head size scaling - endocast measurements. Our original study design also included measurements of dermal skulls, but we omitted this from the final version as the material available was far too incomplete to be able to conduct meaningful analyses. It is a topic of future study that some of us (AC, RC) have already discussed as a potential future project to be investigated.<br /> With respect to the functional implications of the modular dissociation of the labyrinths, we have expanded the final paragraph of the “implications for sensory abilities” within the Discussion, and similarly added the sentence “However, we acknowledge that it is difficult to determine if increased relative utricular size results from greater reliance of sensitivity in the horizontal plane alone, or if it expands to compensate for e.g. relative stagnation of the sacculus + semicircular canals in some way. Further studies, such as investigation of neuronal densities in extant lungfish labyrinths, may potentially in part clarify this uncertainty in future.”

4) Labyrinth size

With the above mentioned utricular exception, labyrinth size measurements particularly on the semicircular canals seem to imply that there is a relative consistent scaling relationship between the canals. When one canal gets larger, so do the others, perhaps thereby retaining canal symmetry across different absolute labyrinth sizes. Labyrinth size in tetrapods is often interpreted in relation to body size/mass or head size (e.g. Melville Jones & Spells 1963, Proc. R. Soc. Lond. Biol. Sci.; Spoor & Zonneveldt 1998, Yearb. Phys. Anthr.; Spoor et al. 2002, Nature; Spoor et al. 2007, PNAS; Bronzati et al. 2021, Curr. Biol.), as deviations from the expected labyrinth size per head size indicate increased or decreased relative labyrinth sensitivities. Large relative head sizes of birds and (within) mammals have generally been interpreted as indicative of "active" or "agile" behaviour, although doubt has been casted on these relationships recently (e.g., Bronzati et al. 2021). Increased sampling of relative labyrinth size from various vertebrate groups would be important to better understand labyrinth sizefunction relationships. Melville Jones & Spells (1963) have shown that fishes have large labyrinth sizes compared to most tetrapods, but they don't have lungfish data and the large labyrinth sizes of fishes have often remained uncommented on in tetrapod works. I think this study offers a fantastic opportunity to provide comparative labyrinth size data for lungfishes. In this regard, it would be really interesting to quantify labyrinth size relative to head size, and show a respective (phylogenetic) regression analysis. Ideally, the size of the labyrinth could be quantified along the arc lengths of the semicircular canals, but other ways are also thinkable (for example a box volume of labyrinth size by the existing measurements, contrasted with a box volume of the skull, i.e. heightwidthlength).

Firstly, many thanks for the suggested reading of Bronzati et al. (2021) And while we consider a labyrinth skull size regression analysis to be a worthwhile suggestion, we have chosen not to include one in this study, partly as there is no phylogenetic regression based on the new methods that we are using, and secondly that it forms the basis of another study currently underway by some of the authors.

Reviewer #1 (Public Review):

In this study, the authors aimed to address the important question of the mechanism of deep brain stimulation (DBS) in treating Parkinson's disease, based on a mouse model that the authors established previously.

The strength of the study lies on 1) avoiding the interference of stimulation artefacts of using electrophysiological recording technique, and 2) examining effects on cell-type or projection-specific targets.

However, there are several critical problems in this study. First, the low temporal resolution and the averaged population signal (rather than from individual neurons) of the fibre photometry data prevents in-depth enough analysis of the effects of DBS on the target areas to draw useful conclusion. Thus, all interpretations were based on an average rise in GCaMP-reported calcium signals with pretty low temporal resolution. As a result, important readouts that were analysed in many previous studies such as the firing patterns (e.g. rhythmic) or synchrony among neurons were missed by this approach. Take one example. The conclusion that antidromic activation is excluded as a possible mechanism is based partly on the lack of good correlation of the averaged calcium signal with the behavioral improvement. However, such a lack of correlation is also evident in the averaged calcium signal and the improvement in movement behavior under 60Hz and 100 Hz stimulation (Figure 2). While a higher average in calcium signal is observed under 60Hz DBS than 100Hz, the improvement in motor behavior is lower than that induced by 100 Hz DBS. This highlights the severe limitation of the fibre photometry data in revealing the therapeutic mechanism of DBS.

Second, there is no clear elucidation of the pathological changes revealed by the fibre photometry in PD mice to illustrate what is normal and what is abnormal, and how the DBS rectifies the abnormal changes. For example, when we need to interpret the effect of the DBS on calcium activities in the subthalamic nucleus (STN), the substantia nigra pars reticulala (SNr) and the primary motor cortex (M1), what abnormal GCaMP signal did the authors find, compared with healthy control mice? Without such information, it is difficult to get a sense of what an increase in GCaMP signal in STN, SNr and M1 mean with respect to motor control, and therefore what it means with respect to the effect of DBS. With the specific context of a peak (actually a biphasic waveform) of the calcium activity in the PD anima, it is puzzling that a surge of STN is correlated with movement onset, while in principle it should result in movement termination. Therefore, it is critical to know if there is there such a correlation in healthy animals. If yes, this may not indicate a pathological change that needs to rectified by DBS. If no, how the pathological appearance of such change leads to parkinsonian motor symptoms (akinesia, bradykinesia etc) must be established.

Third, it is well-known that clinical DBS employed at least 120 Hz stimulation. In fact, the authors had also demonstrated in their previous report that the optimal stimulation frequency in the mouse model is around 180Hz. But the present study utilised clearly suboptimal frequencies (60 and 100Hz only) to address the mechanism. It is possible that different mechanisms or combinations of mechanism may take place under different stimulation frequencies. As such, any conclusion drawn from this study may not represent the whole picture.

Given the above consideration, I do not think that the authors have achieved the aim of their study, as the results cannot convincingly support their conclusions.

Reviewer #3 (Public Review):

Zadbood and colleagues investigated the way key information used to update interpretations of events alter patterns of activity in the brain. This was cleverly done by the use of "The Sixth Sense," a film featuring a famous "twist ending," which fundamentally alters the way the events in the film are understood. Participants were assigned to three groups: (1) a Spoiled group, in which the twist was revealed at the outset, (2) a Twist group, who experienced the film as normal, and (3) a No-Twist group, in which the twist was removed. Participants were scanned while watching the movie and while performing cued recall of specific scenes. Verbal recall was scored based on recall success, and evidence for descriptive bias toward two ways of understanding the events (specifically, whether a particular character was or was not a ghost). Importantly, this allowed the authors to show that the Twist group updated their interpretation. The authors focused on regions of the Default Mode Network (DMN) based on prior studies showing responsiveness to naturalistic memory paradigms in these areas and analyzed the fMRI data using intersubject pattern similarity analysis. Regions of the DMN carried patterns indicative of story interpretation. That is, encoding similarity was greater between the Twist and No-Twist groups than in the Spoiled group, and retrieval similarity was greater between the Twist and Spoiled groups than in the No-Twist group. The Spoiled group also showed greater pattern similarity with the Twist group's recall than the No-Twist group's recall. The authors also report a weaker effect of greater pattern similarity between the Spoiled group's encoding and the Twist group's recall than between the Twist group's own encoding and recall. Together, the data all converge on the point that one's interpretation of an event is an important determinant of the way it is represented in the brain.

This is a really nice experiment, with straightforward predictions and analyses that support the claims being made. The results build directly on a prior study by this research group showing how interpretational differences in a narrative drive distinct neural representations (Yeshurun et al., 2017), but extend an understanding of how these interpretational differences might work retrospectively. I do not have any serious concerns or problems with the manuscript, the data, or the analyses. However I have a few points to raise that, if addressed, would make for a stronger paper in my opinion.

1) My most substantive comment is that I did not find the interpretive framework to be very clear with respect to the brain regions involved. The basic effects the authors report strongly support their claims, but the particular contributions to the field might be stronger if the interpretations could be made more strongly or more specifically. In other words: the DMN is involved in updating interpretations, but how should we now think about the role of the DMN and its constituent regions as a result of this study? There are a number of ideas briefly presented about what the DMN might be doing, but it just did not feel very coherent at times. I will break this down into a few more specific points:

While many of us would agree that the DMN is likely to be involved in the phenomena at hand, I did not find that the paper communicated the logic for singularly focusing on this subset of regions very compellingly. The authors note a few studies whose main results are found in DMN regions, but I think that this could stand to be unpacked in a more theoretically interesting way in the Introduction.

Relatedly, I found the summary/description of regional effects in the Discussion to be a bit unsatisfying. The various pattern similarity comparisons yielded results that were actually quite nonoverlapping among DMN regions, which was not really unpacked. To be clear, it is not a 'problem' that the regional effects varied from comparison to comparison, but I do think that a more theoretical exploration of what this could mean would strengthen the paper. To the authors' credit, they describe mPFC effects through the lens of schemas, but this stands in contrast to many other regions which do not receive much consideration.

Finally, although there is evidence that regions of the DMN act in a coordinated way under some circumstances, there is also ample evidence for distinct regional contributions to cognitive processes, memory being just one of them (e.g., Cooper & Ritchey, 2020; Robin & Moscovitch, 2017; Ranganath & Ritchey, 2012). The authors themselves introduce the idea of temporal receptive windows in a cortical hierarchy, and while DMN regions do appear to show slower temporal drift than sensory areas, those studies show regional differences in pattern stability across time even within DMN regions. Simply put, it is worth considering whether it is ideal to treat the DMN as a singular unit.

2) I think that some direct comparison to regions outside the DMN would speak to whether the DMN is truly unique in carrying the key representations being discussed here. I was reluctant to suggest this because I think that the authors are justified in expecting that DMN regions would show the effects in question. However, there really is no "null" comparison here wherein a set of regions not expected to show these effects (e.g., a somatosensory network, or the frontoparietal network) in fact do not show them. There are not really controls or key differences being hypothesized across different conditions or regions. Rather, we have a set of regions that may or may not show pattern similarity differences to varying degrees, which feels very exploratory. The inclusion of some principled control comparisons, etc. would bolster these findings. The authors do include a whole-brain analysis in Supplementary Figure 1, which indeed produced many DMN regions. However, notably, regions outside the DMN such as the primary visual cortex and mid-cingulate cortex appear to show significant effects (which, based on the color bar, might actually be stronger than effects seen in the DMN). Given the specificity of the language in the paper in terms of the DMN, I think that some direct regional or network-level comparison is needed.

3) If I understand correctly, the main analyses of the fMRI data were limited to across-group comparisons of "critical scenes" that were maximally affected by the twist at the end of the movie. In other words, the analyses focused on the scenes whose interpretation hinged on the "doctor" versus "ghost" interpretation. I would be interested in seeing a comparison of "critical" scenes directly against scenes where the interpretation did not change with the twist. This "critical" versus "non-critical" contrast would be a strong confirmatory analysis that could further bolster the authors' claims, but on the other hand, it would be interesting to know whether the overall story interpretation led to any differences in neural patterns assigned to scenes that would not be expected to depend on differences in interpretation. (As a final note, such a comparison might provide additional analytical leverage for exploring the effect described in Figure 3B, which did not survive correction for multiple comparisons.)

4) I appreciate the code being made available and that the neuroimaging data will be made available soon. I would also appreciate it if the authors made the movie stimulus and behavioral data available. The movie stimulus itself is of interest because it was edited down, and it would be nice for readers to be able to see which scenes were included.

To sum up, I think that this is a great experiment with a lot of strengths. The design is fairly clean (especially for a movie stimulus), the analyses are well reasoned, and the data are clear. The only weaknesses I would suggest addressing are with regards to how the DMN is being described and evaluated, and the communication of how this work informs the field on a theoretical level.

Congruence is the antidote to collective illusion.

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Reply to the reviewers

We thank all reviewers for their very helpful comments. We feel that the comments pointed to a few main issues that we could remedy. First, we found that many comments and concerns could be addressed with work from our previous paper (doi.org/10.1101/2020.11.24.396002). To fix this, we added additional descriptions of experiments done previously and additional citations. We discussed more in depth an experiment that shows that ciliary membrane and membrane proteins can indeed come from the cell body plasma membrane, we talked more about how we determined that the actin puncta are representative of membrane remodeling functions like endocytosis, and we discussed some of the mechanistic insights provided by our previous work that are applicable here. We hope that this helps to answer several of the reviewer questions. Second, there were a few experiments we thought would be useful to add. These are represented in bold in our responses below. Briefly, we added a measure of internalization or endocytosis in the drp3 mutant, we added some images of cilia to the phalloidin figure to orient readers’ views of the cell, we added some additional mechanistic insight (supplemental figure 3), and we added an axoneme stain to confirm that the axoneme was extending (supplemental figure 4). Finally, we fixed some of our wording in the paper to represent our findings more accurately. Together, we hope that these revisions will address the reviewer concerns.

Additionally, we added some data that we collected while waiting on reviews. We investigated the requirement for myosin in this pathway and include this data in the supplement.

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

The current manuscript by Bigge et al. demonstrated that the chemical inhibition of GSk3 causes ciliary elongation in Chlamydomonas reinhardtii. They show that lithium induced ciliary lengthening is majorly due to GSK3 inhibition. Consistent with earlier reports, they show that new protein synthesis is not required for lithium induced ciliary elongation. The authors report that targeting endocytosis either by using chemical inhibitors (dynasore and CK-666) or genetic mutants (dpr3 and Arpc4) does not cause lithium induced ciliary elongation. They further reveal enhanced actin dynamics in lithium treated cells and such activity is lost in Arpc4 mutants. Based on these results, the authors concluded that endocytic pathways may be involved in lithium induced ciliary lengthening. The results are interesting, and this work is important in understanding more about ciliary length regulation. However, more experimental evidence addressing the current interpretation that endocytic pathways may be involved in lithium induced ciliary lengthening is required.

Major comments: 1 The authors use chemical inhibitors as major tools for their study. However, the specificity of these inhibitors is a concern. How specific are these GSK3 inhibitors such as LiCl? Can authors show that LiCl mediated ciliary lengthening is due to inhibition of GSK3? Authors used BFA and Dynasore to show that not the Golgi, but the endocytosis derived membrane is required for ciliary lengthening. Again, here the specificity of these inhibitors is a concern. Especially as Dynasore has been shown to have non-specific effects.

We agree that the specificity of chemical inhibitors can be a concern. This is why we used 4 separate inhibitors of GSK3, each showing elongation of cilia and an increase in actin puncta (suggesting an increase in actin dynamics at the membrane). While these different inhibitors may have different off-target effects. Their intended target, GSK3, is the same, suggesting that the shared phenotype from each inhibitor is conserved. The ability of LiCl to affect GSK3 activity in Chlamydomonas was also investigated in depth with a kinase assay and a western blot in Wilson, 2004 (doi: 10.1128/EC.3.5.1307-1319.2004). To address the off-target effects of Dynasore, we employed the drp3 mutant to confirm genetically what we saw from the chemical inhibition. We also show in our previous paper that Dynasore and PitStop2 have similar effects in Chlamydomonas, both of them inhibiting the internalization of a dye-labelled membrane, suggesting that they both function to block endocytosis (doi.org/10.1101/2020.11.24.396002). While no mutant or alternative inhibitor is available to look at the effects of BFA, this inhibitor and its effects on cilia have been well-characterized in Dentler, 2013 (doi.org/10.1371/journal.pone.0053366).

Does inducing/enhancing endocytosis independent of GSK3 by other means has any effect on ciliary length regulation?

Our concern with the proposed experiment is that even if elongation requires endocytosis, all endocytosis might not lead to ciliary elongation when endocytosis is for other purposes. For example, endocytosis could occur for other purposes, like nutrient uptake, that will have no effect on cilia. The plasma membrane to cilium pathway may be a targeted pathway triggered by specific disruptions. Therefore, we don’t feel that the proposed experiments will add to our model.

The major claim of this paper is that LiCl mediated ciliary lengthening is due to enhanced endocytosis. Although authors showed that inhibition of endocytosis results in reduced ciliary length, it is important to show if GSK3 inhibition by LiCl (or any other inhibitor) causes any increased cellular endocytosis? Similarly, what is the effect of GSK3 mutants on endocytosis?

*We show an increase in actin dynamics at the membrane and actin puncta following treatment with LiCl and the other GSK3 inhibitors. We show here and in our previous paper (doi.org/10.1101/2020.11.24.396002), that these puncta are likely endocytic based on the timing of their appearance and the proteins required for puncta formation (including the Arp2/3 complex and Clathrin) (Figure 7, previous paper). We updated our latest version to reflect the data we have already collected and presented as follows: *

“Further, they rely on proteins typically thought to be involved in endocytosis including the Arp2/3 complex and clathrin, and they form at times when it makes sense for endocytosis to be occurring, like immediately following deciliation when membrane and protein must be recruited to cilia in a timeframe too short for new protein and membrane synthesis, sorting, and trafficking (Bigge et al. 2020). Thus, we stained cells with phalloidin to visualize filamentous actin and these endocytosis-like punctate structures when cells are treated with GSK3 inhibitors.”

A phenotypic mutant of GSK3 does not currently exist in Chlamydomonas, and methods of reliably introducing mutants in Chlamydomonas do not currently exist. Thus, we used the array of GSK3 inhibitors.

Are these endocytic processes enhanced specifically at/or around the cilium during the ciliary lengthening process?

*Based on our phalloidin staining data, these processes are primarily enhanced near the cilium, but puncta also exist throughout the cell. To more clearly show this and in response to a comment from reviewer 2, we added a set of images with brightfield to demonstrate where the dots are in relation to cilia. We also added arrows to the images in the figure to point out the apex of the cell as determined by the filamentous actin structures in the cells. *

Authors claim that drp3 is a target of GSK3 and, similar to the canonical dynamin, functions in endocytosis. While, it is an important observation, experiments are required to show the role of drp3 in endocytosis and also to show that it is indeed a target of GSK3.

To address this comment, we are employing an experiment that was designed in our previous paper (doi.org/10.1101/2020.11.24.396002, Figure 5B-E). This experiment uses a lipophilic membrane dye, FM4-46FX. The dye binds to the membrane but is unable to enter the cell alone. It is quickly endocytosed and results in vesicular-like structures within the cell. We added a panel to Figure 3 where we do this experiment in wild-type and ____drp3 mutant cells. This shows that endocytosis is affected by the mutation in DRP3. The discussion of this new data is summarized in the text as follows:

“Additionally, we showed that this DRP is required for internalization of a lipophilic membrane dye, FM4-46FX through endocytosis. This dye binds to the membrane but is unable to enter the cells on its own and must be endocytosed. In wild-type cells it is quickly endocytosed and visible as puncta within the cell (Figure 3F, H) (Bigge et al. 2020). However, in drp3 mutants the amount of dye endocytosed is significantly lower (Figure 3G-H), suggesting that DRP3 is required for optimal endocytosis in these cells.”

Mechanistic insights into how endocytosis/actin dynamics regulate ciliary lengthening would be interesting to see. Further, it is interesting to see if the ciliary signaling defects caused by abnormal ciliary length can be rescued by inhibition of endocytosis.

*In our previous paper (doi.org/10.1101/2020.11.24.396002), we dive into the mechanisms tying together actin dynamics, endocytosis, and cilia. We find that Arp2/3 complex-nucleated actin networks are required for endocytosis to reclaim ciliary membrane and membrane proteins from a pool in the plasma membrane for the rapid early stages of ciliary assembly. We believe that this is a similar mechanism to what is occurring when cells elongate following lithium treatment. This is because there are several parallels in phenotypes: *

-The Arp2/3 complex is required for both ciliary assembly (Figure 1, previous paper) and ciliary elongation resulting from lithium treatment. In the case of ciliary assembly, treating with cycloheximide to block the synthesis of new protein fully eliminates regrowth in the absence of the Arp2/3 complex, suggesting this Arp2/3 complex dependent mechanism in early ciliary assembly does not involve new protein synthesis (Figure 2, previous paper). Similarly, the process of ciliary elongation in response to lithium does not require new protein synthesis.

*-A burst in actin dynamics/actin puncta occurs immediately following deciliation during early regrowth and during growth initiated by lithium treatment. We know these puncta are Arp2/3 complex and clathrin dependent (Figures 4 and 7, previous paper). *

*-Both initial ciliary assembly or ciliary maintenance and elongation of cilia due to lithium treatment require endocytosis (Figures 5, 7-8, previous paper) but not require Golgi-derived membrane (Figure 3, previous paper). *

*-Also in the previous paper, we find that this mechanism is required for the internalization and relocalization of a ciliary membrane protein for mating (Figure 6, previous paper). We also find that ciliary membrane proteins move from the plasma membrane to the cilia during ciliary assembly (Figure 7-8, previous paper). *

*This is summarized in the text as follows: *

*In the introduction we added: *

“Previous data from our lab suggest that the Arp2/3 complex and actin are involved in reclaiming material from the cell body plasma membrane that is required for normal ciliary assembly (Bigge et al. 2020). We show that the Arp2/3 complex is required for the normal assembly of cilia and for endocytosis of both plasma membrane and plasma membrane proteins in various contexts. Further, we find that deciliation triggers Arp2/3 complex-dependent endocytosis by observing an increase in actin puncta immediately following deciliation (Bigge et al. 2020).”

And in the discussion we added:

“Previous work has shown that while the Golgi is required for ciliary maintenance and assembly (Dentler 2013), it is not the only source of membrane. Instead, we found that membrane reclaimed through actin and Arp2/3-complex dependent endocytosis is required for ciliary assembly or growth from zero length (Bigge et al. 2020). More specifically, we found that the Arp2/3 complex is required for normal ciliary maintenance and ciliary assembly, especially in the early stages when membrane and protein are needed quickly. The Arp2/3 complex is also required for the internalization of membrane and a specific ciliary membrane protein required for mating. Further, we show that endocytosis-like actin puncta form immediately following deciliation in an Arp2/3 complex and clathrin-dependent manner, and that membrane from the cell body plasma membrane can be reclaimed and incorporated into cilia (Bigge et al. 2020). This led us to question whether that same mechanism might be required for ciliary elongation from steady state length induced by lithium treatment.”

Minor comments: 1. The paper needs a thorough proof reading as it harbors many spelling mistakes, grammatical errors, and poor sentence formation in multiple instances.

*The paper was thoroughly read, and spelling mistakes and grammar were fixed. *

Supplemental Figure S2A and S2B should be quoted separately from S2C and S2D.

*This was updated in the latest version of the paper. *

In Page 6 paragraph 2 - "authors wrote "To determine if GSK3 could be a potential kinase for this protein, we employed ScanSite4.0, which confirmed that of the 9 DRPs of Chlamydomonas, the only one with a traditional GSK3 target sequence was DRPs (Supplemental Figure 2)." No data is shown in S2 with regard to this. Either data needs to be shown or change the text in a way to avoid confusion.

*The text was changed in a way to avoid confusion. *

It would be nice to see if GSK3 can actually phosphorylate DRP3.

*This would be interesting, however there is not currently a simple way to test this. There is not an antibody for DRP3 that shares enough of its immunogen sequence with the Chlamydomonas DRP3 sequence to use for a western blot. *

The authors observe that arpc4 mutants do not form actin puncta upon LiCl treatment. Could this phenotype be rescued by complementing with WT ARPC4.

*We showed in our previous paper (doi.org/10.1101/2020.11.24.396002) that the actin puncta could be rescued by re-expression of wild-type ARPC4 (Figure 4). *

The concentration of inhibitors is described differently in the text and figure legends (for example Fig. 4A)

*In the figure legend of figure 4, the concentration of 6-BIO was accidentally reported as 100 µM instead of the correct value (100 nM) as it was throughout the rest of the paper. This was addressed in the latest version. *

The p values are not significant in some of the figures. (Fig. 4D &Fig. 5C)

P values were provided for all comparisons in an effort to be transparent and so that readers could draw their own conclusions about the data.

Reviewer #1 (Significance (Required)):

The current manuscript by Bigge et al. demonstrates that endocytosis is required for GSK3 inhibition mediated ciliary lengthening. Maintenance of proper length of cilia is crucial and its dysregulation results in pathogenesis. This work takes the field forward and helps in our understanding of how ciliary length is regulated. This work is of interest to researchers working in the field of ciliary biology as well as to those working on endocytosis.

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

Summary: The authors show in this study that Lithium and other GSK3-beta inhibitors induce cilia elongation in Chlamydomonas. They further demonstrate that inhibition of endocytosis by Dynasore prevents the induced elongation of cilia. They speculate that a Dynamin-related protein might be involved in this process, and determine 9 Dynamin related proteins (DRPs) in Chlamydomonas of which DRP3 shows the highest sequence similarity. Lithium-induced ciliary elongation is prevented in DRP3 mutants supporting the author's hypothesis and indicating that DRP3 might be a GSK3-beta target, similar to some animal Dynamins. Since Dynamins interact with the F-actin regulator ARP3/3-complex, and because F-actin reorganization is observed in cells after GSK3-beta inhibition, they test the induction of ciliary elongation in arpc4 mutants and after blocking the ARP-complex by CK-666. Indeed, F-actin remodeling and cilia elongation were prevented after loss of ARP-complex function. The induction of ciliary elongation and F-actin remodeling also correlates with the emergence of strong F-actin punctae in cells, and the authors interpret that as induction of Dynamin-dependent endocytosis (also addressed in a current preprint from the group). From that, the conclude that endocytosis is required for delivering membrane to the growing cilium and that this is required for the observed effects. While this claim is somewhat supported by a lack of cilia elongation inhibition after treatment to prevent protein synthesis or Golgi function, direct evidence for membrane delivery to the cilium, the need for membrane delivery for ciliary elongation, and presence of bona fide endocytotic vesicles is sadly missing. Therefore, this study sheds new light on an important process in ciliary functional regulation and also furthers our understanding on why GSK3-beta inhibition induces elongated cilia in many cell systems, but I am not convinced that the conclusions are actually supported by the data, as the two key points in question were not experimentally addressed at this point.

Main points: 1. The authors need to demonstrate that new membrane is delivered in the process to the growing cilium. E.g. this could be done by membrane stains (pulse) and static or live-cell imaging analysis in untreated, GSK3-beta inhibitor treated and in mutants.

*In our previous paper (doi.org/10.1101/2020.11.24.396002), we do an experiment similar to the one described here (Figure 8, previous paper). We biotinylated all surface proteins, then removed the cilia (and therefore all labelled ciliary surface proteins) and allowed them to regrow. We then isolated the new cilia and probed for biotinylated proteins because any biotinylated proteins must have come from the surface of the cell. We found that the cilia did contain membrane proteins from the surface of the cell. This experiment shows that membrane and membrane proteins derived from the plasma membrane are entering growing cilia during regeneration. We added a description of this experiment to the text as follows: *

“Conversely, when treated with Dynasore to inhibit endocytosis, cilia could not elongate to the same degree as untreated cells (Figure 3A-B), implying endocytosis is required for lithium-induced elongation and that endocytosis requires dynamin. This is consistent with results from our previous studies which show that ciliary membrane and membrane proteins are delivered from the cell body plasma membrane to the cilia. In an experiment first performed in Dentler 2013 and then later in Bigge et al. 2020, we biotinylated all cell surface proteins. Then, deciliated cells and allowed cilia to regrow. We then isolated cilia and probed for biotinylated proteins. Any biotinylated proteins present must have come from the cell body plasma membrane, and we found that indeed biotinylated proteins exist in the newly grown cilia, suggesting that ciliary membrane and membrane proteins can be recruited from the cell body plasma membrane (Dentler 2013; Bigge et al. 2020).”

However, this experiment cannot be done in the case of lithium because cilia are not removed meaning they already will contain labelled surface proteins. Additionally, cells do not regrow cilia in the presence of lithium, meaning that we cannot add a regeneration. Regardless, work from our previous paper described above does establish that ciliary membrane and membrane proteins are able to come from the cell body plasma membrane as the reviewer requested.

Along the same line, the authors need to demonstrate that the punctae are truly endocytotic vesicles. For that uptake assays/stains could be used and additional markers. Furthermore, there are multiple modes of endocytosis (e.g. Clathrin) besides Dynamin. The authors should determine if blocking other modes of endocytosis has similar or divergent effects on cilia elongation.

*In our previous paper (doi.org/10.1101/2020.11.24.396002) we supplement the actin puncta data with membrane labelling to show that the puncta are likely endocytic pits (doi.org/10.1101/2020.11.24.396002, Figure 5). We also show that the puncta require both the Arp2/3 complex and active clathrin to form, further suggesting that they are endocytic (Figure 7, previous paper). We added this to the paper as follows: *

“Further, they rely on proteins typically thought to be involved in endocytosis including the Arp2/3 complex and clathrin, and they form at times when it makes sense for endocytosis to be occurring, like immediately following deciliation when membrane and protein must be recruited to cilia in a timeframe too short for new protein and membrane synthesis, sorting, and trafficking (Bigge et al. 2020). To provide additional evidence that these are endocytic puncta, we also showed that a corresponding increase in membrane internalization occurs during this same timeframe using a fluorescent membrane dye that is endocytosed in wild-type cells (Bigge et al. 2020).”

Additionally, Dynamin is required for most forms of endocytosis, including clathrin mediated endocytosis. In the previous paper (doi.org/10.1101/2020.11.24.396002), which we cite here, we do a deep dive into which endocytic proteins are present in Chlamydomonas. We found that clathrin mediated endocytosis is the most highly conserved on the endocytic processes we looked at (Figure 5, previous paper).

We did add a new figure to this paper (Figure 4) using a dye that labels membrane in lithium treated cells. This dye binds to the plasma membrane but is unable to enter cells by itself and must be endocytosed. We found that during the first 30 minutes of lithium treatment there is increased membrane dye internalization.

No cilia are actually shown in the study. I personally, would like to see how these cilia look like, especially in relation to the sites of F-actin remodeling and punctae formation. What comes first? Please also provide a axoneme staining to confirm elongation of the ciliary core and what happens to the tubulin pool when cilia cannot elongate any more? Is it accumulating at the ciliary base?

We added a panel demonstrating where the puncta are in relation to cilia in Figure 4 with a brightfield overlay.* We also look at the appearance and timing of these puncta more in depth in our previous paper (doi.org/10.1101/2020.11.24.396002, Figure 7). We find that puncta form immediately following deciliation and start to return to normal following about 10 minutes of regrowth. We think that this mechanism of ciliary elongation in lithium is similar to what occurs during those early steps of ciliary assembly suggesting that the dots likely form very early on. *

We also included axoneme staining in Supplemental figure 4*. We show that the axoneme does continue to elongate with the cilia. After about 90 minutes, the cilia actually stop growing and detach from the cells (doi: 10.1128/EC.3.5.1307-1319.2004, doi: doi.org/10.1247/csf.12.369). However, we are interested in the more acute mechanisms that result in ciliary elongation. *

The authors also claim that the method of GSK3 inhibition is not important. It would be more correct to say that the mode/drug of GSK3 inhibition is not important, but discuss how some of the minor variance between treatments could be explained (incl. the timeline and temporal dynamics of the diverging effects; and the dose-dependency as low concentrations of BIO seem to induce shortening but high doses induce elongation of cilia).

*We further discussed this in the text as follows: *

“The minor variances between the drugs could be explained by the timeline in which we tested cilia (90 minutes) or the exact dosages we used. An example of this is 6-BIO where treatment with a low dose of 100 nM caused ciliary lengthening, but treatment with a higher concentration of 2 µM reportedly caused ciliary shortening (Kong et al. 2015). Together, the data suggest that the mode of inhibition by chemical targets of GSK3 is not important for ciliary lengthening. Whether GSK3 was inhibited via competition for ATP binding or phosphorylation, cilia were able to elongate.”

They propose here a positive effect of F-actin build up in cilia length regulation, while most studies to date report ciliary shortening to correlate with increased F-actin at the ciliary base. I believe that this is not highlighted and discussed enough, which I find reduces the overall quality of the paper (but is easy to improve). It might be also interesting to test if other F-actin inducers/stabiliziers have the same effect?

*This is addressed in the discussion in the latest version in depth as follows: *

“One important detail to point out is that Chlamydomonas differ from mammalian cells in that they have a cell wall. The stability awarded by the cell wall means that Chlamydomonas does not require a cortical actin network as mammalian cells do. Thus, in Chlamydomonas, we are able to investigate actin dynamics and functions without the interference of the cortical actin network. This also means that some of the effects we see might be masked in mammalian cells by the presence of the cortical actin network and the effect that it has on ciliary assembly and maintenance.”

*We also added a section to the introduction to address this concern early on so that readers will have this difference in mind as they read the paper: *

“Additionally, unlike mammalian cells, Chlamydomonas lacks a cortical actin network which simplifies the relationship between cilia and actin and makes this an ideal model to study such interactions.”

Also, F-actin inducers/stabilizers do not typically have the same effect because the filamentous actin needed for these processes must be dynamic, or able to undergo rapid depolymerization and repolymerization as needed during this fairly quick timeframe. This is demonstrated in Avasthi, 2014 (*doi.org/10.1016/j.cub.2014.07.038). Cells were treated with several actin targeting inhibitors including LatB which results in depolymerization of filaments and Jasplakinolide which results in stabilization of filaments. In both cases, ciliary regeneration is impaired suggesting that actin must be dynamic for its functions related to cilia. *

Minor points: 1. In many Figures, the x-axis is labeled "Number of values", but I think that maybe number of observations might be more appropriate.

We discussed this point and decided to change the axis titles to “Number of cilia”.

The author often use the word "normally" elongating, but in all cases the elongation is induced = abnormal situation. Maybe the authors could use a different term.

We originally used “normally” because there are times when we get defective elongation but not no elongation. In the latest version we changed this to “elongation consistent with untreated wild-type cells” or something along those lines.

It is puzzling as to why DRP3 was chosen, while DRP2 actually is most similar in terms of domain composition. Maybe they could discuss that. They also could explain a bit better how the mutants were generated in which a "cassette was inserted early in the gene". What kind of disruption is expected?

DRP3 was chosen because it has the highest sequence identity (and similarity). DRP2 while containing all domains, has low overall sequence conservation. DRP3 is also the only DRP that showed a potential GSK3 target site when investigated with ScanSite4.0. This was all made clearer in the text as follows:

“Chlamydomonas contains 9 DRPs with similarity to a canonical dynamin (DRP1-9). Despite lacking 2 of the canonical dynamin domains, the DRP with the highest sequence similarity and identity to canonical dynamin is DRP3 (Supplemental Figure 2C-D). To determine if GSK3 could be a potential kinase for this protein, we employed ScanSite4.0, which confirmed that of the 9 DRPs of Chlamydomonas, the only one with a traditional GSK3 target sequence was DRP3.”

The representative images in Figure 4A do not really seem to match the quantifications.

*The quantitative data suggest that these different treatments have increased dots, which we believe the representative images do show. LiCl and CHIR99021 have the most dots, while 6-BIO and Tideglusib have more dots, but less than LiCl and CHIR99021. *

line 109: "of-targets" should be off-targets

Fixed in the latest version, thanks for pointing this out.

line 141: "delivery form the Golgi" should be FROM the Golgi

Fixed in the latest version, thanks for pointing this out.

line 160: "was DRPs" should be was DRP3

Fixed in the latest version, thanks for pointing this out.

line 204/205: the sentence starting "Thus, we phalloidin..." should be rephrased. It sounds not quite correct

Fixed in the latest version, thanks for pointing this out.

line 209: Figure 4A should refer to Figure 4B

Fixed in the latest version, thanks for pointing this out.

line 211: "times or rapid ciliary" should be of rapid ciliary...

Fixed in the latest version, thanks for pointing this out.

line 257: "in lithium." Should be in lithium treated cells Fixed in the latest version, thanks for pointing this out.

Reviewer #2 (Significance (Required)):

This study sheds new light on an important process in ciliary functional regulation and also furthers our understanding on why GSK3-beta inhibition induces elongated cilia in many cell systems, but I am not convinced that the conclusions are actually supported by the data, as the two key points in question were not experimentally addressed at this point.

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

Chlamydomonas maintains relatively regular length of cilia (flagella). However, when the cell is exposed to high concentration of lithium ions, it elongates cilia further. In this work, Bigge and Avasthi made experiments to build a potential hypothesis of molecular mechanism of this unusual cilia elongation. Their hypothesis is (1) cilia elongation is triggered, depending on supply of extra membrane (not proteins), (2) membrane is supplied from plasma membrane by clathrin-dependent endocytosis (not from Golgi), (3) this endocytosis contains Arp2/3 complex, (4) GSK3 downregulates Arp2/3 dependent endocytosis and (5) GSK3 is suppressed by lithium. They conducted well-organized experiments to prove each step. While some of them are indirect, their hypotheses were supported experimentally in outline.

(1) is undoubted, since the authors demonstrated that inhibition of protein production by cycloheximide did not influence cilia elongation.

(2) The authors clearly demonstrated that source of ciliary membrane for elongation is plasma membrane and not Golgi by examining specific inhibitors' effect. They also showed protein transfer from plasma membrane to cilia, by biotinylaing surface proteins in the cell, deciliating and growing cilia and detecting biotinylated proteins in cilia. This part rather characterizes initial growth of cilia, not elongation. Therefore this result must be properly described in the context of this work (which is elongation of cilia).

This comment was particularly helpful as it also helps us address some of the comments from the other reviewers. We updated the description of this experiment in the context of this work in the latest version as follows:

“Further, they rely on proteins typically thought to be involved in endocytosis including the Arp2/3 complex and clathrin, and they form at times when it makes sense for endocytosis to be occurring, like immediately following deciliation when membrane and protein must be recruited to cilia in a timeframe too short for new protein and membrane synthesis, sorting, and trafficking (Bigge et al. 2020). To provide additional evidence that these are endocytic puncta, we also showed that a corresponding increase in membrane internalization occurs during this same timeframe using a fluorescent membrane dye that is endocytosed in wild-type cells (Bigge et al. 2020).”

For (3)-(4), they visualized Arp2/3 localization, showing highly condensed Arp2/3. They interpreted these particles as sign of clathrin endocytosis. Since so far such an endocytosis particle has not been reported in Chlamydomonas, the authors confirmed that DRPs are target of GSK3 to indirectly show GSK3 influences formation of endocytosis. This reviewer thinks the author should be able to directly confirm endocytosis for example by electron microscopy (of traditional epon-embedded and stained cells).

We visualized Arp2/3 complex-dependent filamentous actin localization. We provide DRP3 as a potential target of GSK3, but do not report that it is the target that results in increased endocytosis or increased ciliary length. We agree that electron microscopy would be ideal to visualize endocytosis in these cells. However, we feel this is outside the scope of this current work. But, we do have plans to look at endocytosis in Chlamydomonas *using electron microscopy in the future and hope that the increased context from the previous data are sufficient at this time. *

(5) was elegantly proved by multiple drugs (all known as inhibitor of GSK3), including lithium.

After fixing these points, this manuscript will be ready for publication.

Minor points: Line188-191: not clear. What are *** and ****?

Fixed in the latest version, thanks for pointing this out.

Line262-264: It would be helpful how the initial cilia growth of the arpc4 cell.

We agree that this would be helpful information, and included more of a description of how ciliary growth is affected by loss of Arp2/3 complex function in the latest version: “Specifically, we found that the Arp2/3 complex is required for reclamation of membrane from a pool in the plasma membrane during the rapid growth that occurs during early ciliary assembly”.

Line321: it should read as follows. Cang 2014; carlsson and Bayly 2014). While we...

Fixed in the latest version, thanks for pointing this out.

Line329: were -> where

Fixed in the latest version, thanks for pointing this out.

Line365-366: Lithium-treated cells are not motile. Any thought why? Maybe protein production is not necessary for apparent cilia elongation, but necessary for elongation of functional cilia.

*This is an interesting idea. However, even when protein production is allowed to proceed, Lithium-treated cells are not motile. This is a ciliary dysfunction, and in fact, after about 90 minutes incubation with lithium, the cilia of these cells start to crash out or fall off, demonstrating that these are not healthy cells or healthy cilia. *

Reviewer #3 (Significance (Required)):

This work is an important step toward the understanding of cilia elongation and thus growth mechanism. It will attract wide audience who have interest in cell biology and motility. My expertise is about motile cilia and their 3D structure.

Author Response

Joint Public Review:

Strengths: The study represents a step forward in relating immune responses to infection outcomes that of urgent interest to public health, especially the timing of shedding and frequency of supershedding events. Nguyen et al.'s model provides a useful framework for understanding the links between immune effectors and infection outcomes, and it can be expanded to encompass further biological complexity. The study system is a good choice, given the ubiquity of both helminth and bacterial infections, and experimental infections of rabbits provide a useful point of comparison for past work in mice.

We appreciated these general comments.

Limitations: The present study does not explicitly account for differences in helminth infection dynamics across the two species represented in the data nor does it include feedbacks between the bacterial and helminth infections. Nguyen et a. therefore show the limits of what can be learned from focusing on the bacterial and immune dynamics alone, and this study should serve to motivate further work that can build on this modeling approach to produce a more comprehensive view of the interactions among species infecting the same host. Future studies examining the impact of helminth infection intensity would be tremendously useful for assessing the potential of anthelminthics to reduce the prevalence of bacterial respiratory diseases. Finally, subsequent studies may need to look beyond the factors examined here to understand why shedding varies so much through time for individual hosts.

We agree that focusing only on the bacterial infection is a limitation in this study. We followed a parsimonious approach and decided to concentrate on B. bronchiseptica shedding in the four types of infection. While we do have data on the dynamics of infection of the two helminth species, adding these data would have been an enormous amount of work and too much to present in a single paper. Yet, we have already investigated some of these bi-directional effects using the BT group (Thakar et al. 2012 Plos Comp. Biol.) and plan to keep working on these rich datasets in the future.

We also agree that it is important to understand the rapid variation in Bordetella shedding observed, which appears to be a common feature in many other host-pathogen systems. This requires a completely new set of experiments on infection and shedding at the local tissue level.

Specific comments

Definition of supershedding: A major stated goal of the MS is to investigate the effect of coinfection by helminths on supershedding. In order to compare animals with different coinfections, it is therefore necessary to have a common definition of supershedding. At present, the authors use a definition that depends on which arm of the experiment the animals belong to. This complicates the analysis and clouds its interpretation.

We value this comment and see the implication of using different datasets to quantify supershedding. To overcome this problem, we now propose a slightly different approach where we pull the four infections together and calculate a common 99th or 95th percentile threshold. This common threshold is then used to calculate the number of hosts with at least one supershedding event above this cut-off, for every type of infection. Therefore, while the threshold is the same the percentage of hosts with supershedding events varies among infection groups.

Inconsistent approach: Within each experimental treatment, the data display variability on at least three levels: (i) within animals, day-to-day shedding displays variability on a fast timescale; (ii) within animals, infection status varies more slowly over the course of infection; (iii) between animals, there is variation in both (i) and (ii). The authors' model seems well-designed to handle this variability, but the authors are strangely inconsistent in their use of it. To be specific, to account for level (i), the authors very sensibly adopt a zero-inflated model for the shedding data, whereby the rate of shedding (colony-forming units per second, CFU/s) is assumed to arise from a mixture of a quantitative process (which we might think of as intensity of potential shedding) and an all-or-nothing process (which might arise, for example, if some discrete behavior of the animal is necessary for shedding to occur at all). The inclusion of the all-or-nothing process necessitates an additional parameter, but it allows the non-zero shedding data to inform the model. To account for level (ii), the authors use a four-dimensional deterministic dynamical system. Three of the four variables are related to the measured components of the immune response. The fourth is related to the aforementioned potential shedding. Level (iii) is accounted for using a hierarchical Bayesian approach, whereby the individual animals have parameters drawn from a common prior distribution. This approach seems very well designed to address the authors' questions using the data at hand. However, they fail to exploit this, in at least three ways. First, even though the model appears designed specifically to allow for non-shedding animals, the authors exclude animals on an ad hoc basis. Second, rather than display the shedding data in the form recommended by the model, they display log(1+CFU/sec), which is arbitrary and problematic. Its arbitrariness stems from the fact that this quantity is sensitive to the units used for shedding rate. Third, despite the fact that the model appears specifically designed to account for variability at each of the three levels, they do not give enough information to allow the reader to judge whether the model does in fact do a good job of partitioning this variability.

Please see comments to each specific matter below.

Exclusion of animals: In view of the fact that the model the authors describe can account for variability on all three levels, it is strange that they exclude animals that shed too little or not at all. It would be preferable were the authors to base their conclusions on all the data they collected rather than on a subset chosen a posteriori. It is true that the non-shedders will have no information about the time-course of shedding; on the other hand, including them does not complicate the analysis, and it does allow for estimation of the all-or-nothing probability in a coherent fashion. In particular, the fact that coinfection appears to have an impact on whether animals shed at all is itself directly related to the authors' central questions. More generally, ad hoc exclusion of data raises concerns about the repeatability of the experiments that, in this case, appear entirely avoidable.

Rabbits that were infected but never shed were excluded from all our original analysis and continue to be excluded in our updated version. Our focus is on the dynamics of shedding and including animals that do not shed is not informative to our objective. Moreover, these animals do not provide meaningful information on rabbits that are infected but do not shed, since this is a very small number (n=7) to draw meaningful conclusions across four types of infection. Rabbits with three or less shedding events larger than zero (i.e. CFU/s>0) were originally excluded from the modeling and continue to be excluded. This decision was motivated by technical reasons of model convergence and our commitment to generate meaningful results; in other words, it is difficult to fit a model, and provide robust results, on a time series with only three points larger than zero, irrespective of the number of zero points in the time series.<br /> In summary our subset of animals was not chosen a posteriori but based on clear objectives (i.e. pattern of shedding between and within types of infections), a rigorous approach and reliable results. We have further clarified our approach in the Results and Material and Methods.

Incomplete description of the analysis: The description of the statistical analysis will not be complete until sufficient information is provided to allow the interested reader to decide for him- or herself whether the conclusions are warranted and for the motivated reader to reproduce the analysis. In particular, it is necessary to specify all priors fully. At present, these are not described at all, except in vague, and even incoherent, ways. Also, it is necessary to provide details of the MCMC performed. Specifically, the authors should describe the MCMC sampler and show their MCMC convergence diagnostics. Finally, it is good practice to display both the priors and the posteriors: it is impossible to assess the posteriors without an understanding of the priors.

We have carefully revised our approach and results and now provide a complete description of our analysis with additional/new details on Parameter calibration, Model fitting, Model validation and Model selection in Material and Methods, and Appendix (Appendix-3 and 4). Specifically, we have included all priors, along with all posteriors, for the four types of infection in Table 2. We have also explained how the MCMC simulations were performed and how model convergence diagnosis was assessed (section ‘Parameter calibration and Model fitting’). In Appendix-3 we also show the parameter MCMC trace plots for the four types of infection.

Second, rather than display the shedding data in the form recommended by the model, they display log(1+CFU/sec), which is arbitrary and problematic. Its arbitrariness stems from the fact that this quantity is sensitive to the units used for shedding rate.

A clear feature of our shedding data is that there is large variation in the level of shedding both within and between hosts. Because of this, data were presented as log(1+CFU/s) to reduce the skewness of the datasets, and thus the variance, and facilitate the visualization of the experimental and simulated results. The use of data in the form of CFU/s would have made the visualization much harder, especially at low shedding where a large fraction of the data come from.

The practice of displaying the data on a log-scale is appropriate when the underlying process is exponential or when the amount of relative variation is large, including when representing rates. This practice is widely used when modeling infectious diseases and describing biomedical results. A typical example is the overdispersion of macroparasite infections in host populations, or the large variation in the size of outbreaks by microparasite infections, these data are often described on a log-scale. An example closer to our case is the study on influenza-bacteria coinfection by Smith et al. 2013 Plos Pathogens. Given the nature of our data we found that plotting the level of shedding on a log-scale was the most effective way to represent our results.

Model adequacy: The authors' argument rests on the model's ability to adequately account for the data. The authors need to provide some evidence of this, in one form or another. Ultimately, the question is whether the data are a plausible realization of the model. The authors should show simulations from the model (including the measurement error and not merely the deterministic trajectories) and compare these simulations to the data. In particular, it seems worryingly possible that the fitted model is capable of capturing certain averages in the data while, at the same time, failing to describe the infection progression for any of the actual infected animals.

As previously reported, we have now provided full details on model fitting and model convergence in the section ’Parameter calibration and Model fitting’ and ‘Model validation’ in Material and Methods, and ‘Model validation’ and ‘Model convergence’ in Appendix (Appendix3 and 4).

Regarding the evidence that the data are a plausible realization of the model, we have moved the original figure S1 in the main text (now figure 5). This figure shows the good fit of the model to neutrophil, IgA and IgG, both using individual and group data from every infection. We have also revised the quality of the plot to highlight individual simulations. To avoid too much crowding the 95% CIs for every individual are not reported, however, in Appendix-1 we provide the posterior parameter estimations and their 95% CIs, for every individual and as a group average, for the three co-infections (simulations for B rabbits were performed at the group level only).

In the new figure 6 (original figure 5), we have now included the individual trajectories (without 95% CIs to avoid overcrowding), alongside the group trends, for the neutralization rates of neutrophils, IgA and IgG which are the important parameter regulating infection and where the CIs are large enough to show the individual data. The other rates have too narrow CIs to single out individual trajectories and, thus, we only reported the group trends.

In the revised figure 7 (original figure 6) we have revised the quality of the plots to highlight individual trajectories, in addition to the median trend, but have not included the individual 95% CIs, again to avoid overcrowding.

Finally, the main text associated to these figures has been updated accordingly.

Confusion of correlation and causation: At various points, the authors succumb to the temptation to interpret their model literally and to interpret the correlations they observe as evidence for a causal linkage between the three immune components they measure, bacterial shedding, and coinfection. They should be more careful and circumspect in the description of their results.

We have thoroughly revised the presentation and discussion of the results to avoid the overinterpretation of the findings.

Additional Issues:

Eqs 1-4. These equations are not mechanistic in any meaningful sense. Essentially, they posit the existence of exponential time-lags between the three immunity variables, and a simple linear killing relationship between each of the variables and pathogen load. To interpret the equations literally risks making unwarranted conclusions. For example, any physiological variable correlated with any of the three variables in the model might equally well be credited with the influence on shedding attributed to IgA, IgG, or neutrophils.

This work tests the hypothesis that neutrophils, IgA and IgG affect the dynamics of B. bronchispetica infection and, in turn, bacterial shedding. Of course, there are many other immunological mechanisms that could contribute to the pattern observed and that can be tested, as there are many other variables correlated with these dynamics that do not play any role in these patterns, as noted by the reviewer. We follow a parsimonious approach by focusing on three immune variables previously identified as important in regulating Bordetella infection. To avoid excessive complexity and allow model tractability, our informed decision was to simplify the relationship between immunity and infection, without losing the important role of the immune variables selected. Finally, by referring to previous work by others and us we do note that the immune mechanisms described can be much more complex.

l 456. Do the authors account for the variability in time spent with plates? Implicitly, the assumption is made that the amount of time a rabbit spends with a plate, i.e., the decision as to whether to engage in a behavior that will terminate the plate interaction, is independent of everything else. This raises the question: Does the time spent per plate correlate with anything?

We always recorded the amount of time spent with the plate, and every rabbit had a maximum interaction time of 10 minutes. Rabbits are very inquisitive and rarely we had animals that did not interact or had to remove the plate because they were chewing the media; usually animals used the entire 10 minutes. Analyses do account for the interaction time and are presented as Colony Forming Unit/second (CFU/s). As noted in the Material and Methods section ‘Observation model’: ‘The probability of having a shedding event is independent of time since inoculation, in that shedding can occur anytime during the experiment and anytime during the interaction with the petri dish”. This assumption is based on our observations of rabbit behavior during the trials.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors present a new technique for analysing low complexity regions (LCRs) in proteins- extended stretches of amino acids made up from a small number of distinct residue types. They validate their new approach against a single protein, compare this technique to existing methods, and go on to apply this to the proteomes of several model systems. In this work, they aim to show links between specific LCRs and biological function and subcellular location, and then study conservation in LCRs amongst higher species.

The new method presented is straightforward and clearly described, generating comparable results with existing techniques. The technique can be easily applied to new problems and the authors have made code available.

This paper is less successful in drawing links between their results and the importance biologically. The introduction does not clearly position this work in the context of previous literature, using relatively specialised technical terms without defining them, and leaving the reader unclear about how the results have advanced the field. In terms of their results, the authors further propose interesting links between LCRs and function. However, their analyses for these most exciting results rely heavily on UMAP visualisation and the use of tests with apparently small effect sizes. This is a weakness throughout the paper and reduces the support for strong conclusions.

We appreciate the reviewer’s comments on our manuscript. To address comments about the clarity of the introduction and the position of our findings with respect to the rest of the field, we have made several changes to the text. We have reworked the introduction to provide a clearer view of the current state of the LCR field, and our goals for this manuscript. We also have made several changes to the beginnings and ends of several sections in the Results to explicitly state how each section and its findings help advance the goal we describe in the introduction, and the field more generally. We hope that these changes help make the flow of the paper more clear to the reader, and provide a clear connection between our work and the field.

We address comments about the use of UMAPs and statistical tests in our responses to the specific comments below.

Additionally, whilst the experimental work is interesting and concerns LCRs, it does not clearly fit into the rest of the body of work focused as it is on a single protein and the importance of its LCRs. It arguably serves as a validation of the method, but if that is the author's intention it needs to be made more clearly as it appears orthogonal to the overall drive of the paper.

In response to this comment, we have made more explicit the rationale for choosing this protein at the beginning of this section, and clarify the role that these experiments play in the overall flow of the paper.

Our intention with the experiments in Figure 2 was to highlight the utility of our approach in understanding how LCR type and copy number influence protein function. Understanding how LCR type and copy number can influence protein function is clearly outlined as a goal of the paper in the Introduction.

In the text corresponding to Figure 2, we hypothesize how different LCR relationships may inform the function of the proteins that have them, and how each group in Figure 2A/B can be used to test these hypotheses. The global view provided by our method allows proteins to be selected on the basis of their LCR type and copy number for further study.

To demonstrate the utility of this view, we select a key nucleolar protein with multiple copies of the same LCR type (RPA43, a subunit of RNA Pol I), and learn important features driving its higher-order assembly in vivo and in vitro. We learned that in vivo, a least two copies of RPA43’s K-rich LCRs are required for nucleolar integration, and that these K-rich LCRs are also necessary for in vitro phase separation.

Despite this protein being a single example, we were able to gain important insights about how K-rich LCR copy number affects protein function, and that both in vitro higher order assembly and in vivo nucleolar integration can be explained by LCR copy number. We believe this opens the door to ask further questions about LCR type and copy number for other proteins using this line of reasoning.

Overall I think the ideas presented in the work are interesting, the method is sound, but the data does not clearly support the drawing of strong conclusions. The weakness in the conclusions and the poor description of the wider background lead me to question the impact of this work on the broader field.

For all the points where Reviewer #1 comments on the data and its conclusions, we provide explanations and additional analyses in our responses below showing that the data do indeed support our conclusions. In regards to our description of the wider background, we have reworked our introduction to more clearly link our work to the broader field, such that a more general audience can appreciate the impact of our work.

Technical weaknesses

In the testing of the dotplot based method, the manuscript presents a FDR rate based on a comparison between real proteome data and a null proteome. This is a sensible approach, but their choice of a uniform random distribution would be expected to mislead. This is because if the distribution is non-uniform, stretches of the most frequent amino will occur more frequently than in the uniform distribution.

Thank you for pointing this out. The choice of null proteome was a topic of much discussion between the authors as this work was being performed. While we maintain that the uniform background is the most appropriate, the question from this reviewer and the other reviewers made us realize that a thorough explanation was warranted. For a complete explanation for our choice of this uniform null model, please see the newly added appendix section, Appendix 1.

The authors would also like to point out that the original SEG algorithm (Wootton and Federhen, 1993) also made the intentional choice of using a uniform background model.

More generally I think the results presented suggest that the results dotplot generates are comparable to existing methods, not better and the text would be more accurate if this conclusion was clearer, in the absence of an additional set of data that could be used as a "ground truth".

We did not intend to make any strong claims about the relative performance of our approach vs. existing methods with regard to the sequence entropy of the called LCRs beyond them being comparable, as this was not the main focus of our paper. To clarify the text such that it reflects this, we have removed ‘or better’ from the text in this section.

The authors draw links between protein localisation/function and LCR content. This is done through the use of UMAP visualisation and wilcoxon rank sum tests on the amino acid frequency in different localisations. This is convincing in the case of ECM data, but the arguments are substantially less clear for other localisations/functions. The UMAP graphics show generally that the specific functions are sparsely spread. Moreover when considering the sample size (in the context of the whole proteome) the p-value threshold obscures what appear to be relatively small effect sizes.

We would first like to note that some of the amino acid frequency biases have been documented and experimentally validated by other groups, as we write and reference in the manuscript. Nonetheless, we have considered the reviewer's concerns, and upon rereading the section corresponding to Figure 3, we realize that our wording may have caused confusion in the interpretation there. In addition to clarifying this in the manuscript, we believe the following clarification may help in the interpretations drawn from that section.

Each point in this analysis (and on the UMAP) is an LCR from a protein, and as such multiple LCRs from the same protein will appear as multiple points. This is particularly relevant for considering the interpretation of the functional/higher order assembly annotations because it is not expected that for a given protein, all of the LCRs will be directly relevant to the function/annotation. Just because proteins of an assembly are enriched for a given type of LCR does not mean that they only have that kind of LCR. In addition to the enriched LCR, they may or may not have other LCRs that play other roles.

For example, a protein in the Nuclear Speckle may contain both an R/S-rich LCR and a Q-rich LCR. When looking at the Speckle, all of the LCRs of a protein are assigned this annotation, and so such a protein would contribute a point in the R/S region as well as elsewhere on the map. Because such "non-enriched" LCRs do not occur as frequently, and may not be relevant to Speckle function, they are sparsely spread.

We have now changed the wording in that section of the main text to reflect that the expectation is not all LCRs mapping to a certain region, but enrichment of certain LCR compositions.

Reviewer #3 (Public Review):

The authors present a systematic assessment of low complexity sequences (LCRs) apply the dotplot matrix method for sequence comparison to identify low-complexity regions based on per-residue similarity. By taking the resulting self-comparison matrices and leveraging tools from image processing, the authors define LCRs based on similarity or non-similarity to one another. Taking the composition of these LCRs, the authors then compare how distinct regions of LCR sequence space compare across different proteomes.

The paper is well-written and easy to follow, and the results are consistent with prior work. The figures and data are presented in an extremely accessible way and the conclusions seem logical and sound.

My big picture concern stems from one that is perhaps challenging to evaluate, but it is not really clear to me exactly what we learn here. The authors do a fine job of cataloging LCRs, offer a number of anecdotal inferences and observations are made - perhaps this is sufficient in terms of novelty and interest, but if anyone takes a proteome and identifies sequences based on some set of features that sit in the tails of the feature distribution, they can similarly construct intriguing but somewhat speculative hypotheses regarding the possible origins or meaning of those features.

The authors use the lysine-repeats as specific examples where they test a hypothesis, which is good, but the importance of lysine repeats in driving nucleolar localization is well established at this point - i.e. to me at least the bioinformatics analysis that precedes those results is unnecessary to have made the resulting prediction. Similarly, the authors find compositional biases in LCR proteins that are found in certain organelles, but those biases are also already established. These are not strictly criticisms, in that it's good that established patterns are found with this method, but I suppose my concern is that this is a lot of work that perhaps does not really push the needle particularly far.

As an important caveat to this somewhat muted reception, I recognize that having worked on problems in this area for 10+ years I may also be displaying my own biases, and perhaps things that are "already established" warrant repeating with a new approach and a new light. As such, this particular criticism may well be one that can and should be ignored.

We thank the reviewer for taking the time to read and give feedback for our manuscript. We respectfully disagree that our work does not push the needle particularly far.

In the section titled ‘LCR copy number impacts protein function’, our goal is not to highlight the importance of lysines in nucleolar localization, but to provide a specific example of how studying LCR copy number, made possible by our approach, can provide specific biological insights. We first show that K-rich LCRs can mediate in vitro assembly. Moreover, we show that the copy number of K-rich LCRs is important for both higher order assembly in vitro and nucleolar localization in cells, which suggests that by mediating interactions, K-rich LCRs may contribute to the assembly of the nucleolus, and that this is related to nucleolar localization. The ability of our approach to relate previously unrelated roles of K-rich LCRs not only demonstrates the value of a unified view of LCRs but also opens the door to study LCR relationships in any context.

Furthermore, our goal in identifying established biases in LCR composition for certain assemblies was to validate that the sequence space captures higher order assemblies which are known. In addition to known biases, we use our approach to uncover the roles of LCR biases that have not been explored (e.g. E-rich LCRs in nucleoli, see Figure 4 in revised manuscript), and discover new regions of LCR sequence space which have signatures of higher order assemblies (e.g. Teleost-specific T/H-rich LCRs). Collectively, our results show that a unified view of LCRs relates the disparate functions of LCRs.

In response to these comments, we have added additional explanations at the end of several sections to clarify the impact of our findings in the scope of the broader field. Furthermore, as we note in our main response, we have added experimental data with new findings to address this concern.

That overall concern notwithstanding, I had several other questions that sprung to mind.

Dotplot matrix approach

The authors do a fantastic job of explaining this, but I'm left wondering, if one used an algorithm like (say) SEG, defined LCRs, and then compared between LCRs based on composition, would we expect the results to be so different? i.e. the authors make a big deal about the dotplot matrix approach enabling comparison of LCR type, but, it's not clear to me that this is just because it combines a two-step operation into a one-step operation. It would be useful I think to perform a similar analysis as is done later on using SEG and ask if the same UMAP structure appears (and discuss if yes/no).

Thank you for your thoughtful question about the differences between SEG and the dotplot matrix approach. We have tried our best to convey the advantages of the dotplot approach over SEG in the paper, but we did not focus on this for the following reasons:

1) SEG and dotplot matrices are long-established approaches to assessing LCRs. We did not see it in the scope of our paper to compare between these when our main claim is that the approach as a whole (looking at LCR sequence, relationships, features, and functions) is what gives a broader understanding of LCRs across proteomes. The key benefits of dotplots, such as direct visual interpretation, distinguishing LCR types and copy number within a protein, are conveyed in Figure 1A-C and Figure 1 - figure supplements 1 and 4. In fact, these benefits of dotplots were acknowledged in the early SEG papers, where they recommended using dotplots to gain a prior understanding of protein sequences of interest, when it was not yet computationally feasible to analyze dotplots on the same scale as SEG (Wootton and Federhen, Methods in Enzymology, vol. 266, 1996, Pages 554-571). Thus, our focus is on the ability to utilize image processing tools to "convert" the intuition of dotplots into precise read-out of LCRs and their relationships on a multi-proteome scale. All that being said, we have considered differences between these methods as you can see from our technical considerations in part 2 below.

2) SEG takes an approach to find LCRs irrespective of the type of LCR, primarily because SEG was originally used to mask LCR-containing regions in proteins to facilitate studies of globular domains. Because of this, the recommended usage of SEG commonly fuses nearby LCRs and designates the entire region as "low complexity". For the original purpose of SEG, this is understandable because it takes a very conservative approach to ensure that the non-low complexity regions (i.e. putative folded domains) are well-annotated. However, for the purpose of distinguishing LCR composition, this is not ideal because it is not stringent in separating LCRs that are close together, but different in composition. Fusion can be seen in the comparison of specific LCR calls of the collagen CO1A1 (Figure 1 - figure supplement 3E), where even the intermediate stringency SEG settings fuse LCR calls that the dotplot approach keeps separate. Finally, we did also try downstream UMAP analysis with LCRs called from SEG, and found that although certain aspects of the dotplot-based LCR UMAP are reflected in the SEG-based LCR UMAP, there is overall worse resolution with default settings, which is likely due to fused LCRs of different compositions. Attempting to improve resolution using more stringent settings comes at the cost of the number of LCRs assessed. We have attached this analysis to our rebuttal for the reviewer, but maintain that this comparison is not really the focus of our manuscript. We do not make strong claims about the dotplot matrices being better at calling LCRs than SEG, or any other method.

UMAPs generated from LCRs called by SEG

LCRs from repeat expansions

I did not see any discussion on the role that repeat expansions can play in defining LCRs. This seems like an important area that should be considered, especially if we expect certain LCRs to appear more frequently due to a combination of slippy codons and minimal impact due to the biochemical properties of the resulting LCR. The authors pursue a (very reasonable) model in which LCRs are functional and important, but it seems the alternative (that LCRs are simply an unavoidable product of large proteomes and emerge through genetic events that are insufficiently deleterious to be selected against). Some discussion on this would be helpful. it also makes me wonder if the authors' null proteome model is the "right" model, although I would also say developing an accurate and reasonable null model that accounts for repeat expansions is beyond what I would consider the scope of this paper.

While the role of repeat expansions in generating LCRs has been studied and discussed extensively in the LCR field, we decided to focus on the question of which LCRs exist in the proteome, and what may be the function downstream of that. The rationale for this is that while one might not expect a functional LCR to arise from repeat expansion, this argument is less of a concern in the presence of evidence that these LCRs are functional. For example, for many of these LCRs (e.g. a K-rich LCR, R/S-rich LCR, etc as in Figure 3), we know that it is sufficient for the integration of that sequence into the higher order assembly. Moreover, in more recent cases, variation of the length of an LCR was shown to have functional consequences (Basu et al., Cell, 2020), suggesting that LCR emergence through repeat expansions does not imply lack of function. Therefore, while we think the origin of a LCR is an interesting question, whether or not that LCR was gained through repeat expansions does not fall into the scope of this paper.

In regards to repeat expansions as it pertains to our choice of null model, we reasoned that because the origin of an LCR is not necessarily coupled to its function, it would be more useful to retain LCR sequences even if they may be more likely to occur given a background proteome composition. This way, instead of being tossed based on an assumption, LCRs can be evaluated on their function through other approaches which do not assume that likelihood of occurrence inversely relates to function.

While we maintain that the uniform background is the most appropriate, the question from this reviewer and the other reviewers made us realize that a thorough explanation was warranted for this choice of null proteome. For a complete explanation for our choice of this uniform null model, please see the newly added appendix section, Appendix 1.

The authors would also like to point out that the original SEG algorithm (Wootton and Federhen, 1993) also made the intentional choice of using a uniform background model.

Minor points

Early on the authors discuss the roles of LCRs in higher-order assemblies. They then make reference to the lysine tracts as having a valence of 2 or 3. It is possibly useful to mention that valence reflects the number of simultaneous partners that a protein can interact with - while it is certainly possible that a single lysine tracts interacts with a single partner simultaneously (meaning the tract contributes a valence of 1) I don't think the authors can know that, so it may be wise to avoid specifying the specific valence.

Thank you for pointing this out. We agree with the reviewer's interpretation and have removed our initial interpretation from the text and simply state that a copy number of at least two is required for RPA43’s integration into the nucleolus.

The authors make reference to Q/H LCRs. Recent work from Gutiérrez et al. eLife (2022) has argued that histidine-richness in some glutamine-rich LCRs is above the number expected based on codon bias, and may reflect a mode of pH sensing. This may be worth discussing.

We appreciate the reviewer pointing out this publication. While this manuscript wasn’t published when we wrote our paper, upon reading it we agree it has some very relevant findings. We have added a reference to this manuscript in our discussion when discussing Q/H-rich LCRs.

Eric Ross has a number of very nice papers on this topic, but sadly I don't think any of them are cited here. On the question of LCR composition and condensate recruitment, I would recommend Boncella et al. PNAS (2020). On the question of proteome-wide LCR analysis, see Cascarina et al PLoS CompBio (2018) and Cascarina et al PLoS CompBio 2020.

We appreciate the reviewer for noting this related body of work. We have updated the citations to include work from Eric Ross where relevant.

Reviewer #3 (Public Review):

The authors present a systematic assessment of low complexity sequences (LCRs) apply the dotplot matrix method for sequence comparison to identify low-complexity regions based on per-residue similarity. By taking the resulting self-comparison matrices and leveraging tools from image processing, the authors define LCRs based on similarity or non-similarity to one another. Taking the composition of these LCRs, the authors then compare how distinct regions of LCR sequence space compare across different proteomes.

The paper is well-written and easy to follow, and the results are consistent with prior work. The figures and data are presented in an extremely accessible way and the conclusions seem logical and sound.

My big picture concern stems from one that is perhaps challenging to evaluate, but it is not really clear to me exactly what we learn here. The authors do a fine job of cataloging LCRs, offer a number of anecdotal inferences and observations are made - perhaps this is sufficient in terms of novelty and interest, but if anyone takes a proteome and identifies sequences based on some set of features that sit in the tails of the feature distribution, they can similarly construct intriguing but somewhat speculative hypotheses regarding the possible origins or meaning of those features.

The authors use the lysine-repeats as specific examples where they test a hypothesis, which is good, but the importance of lysine repeats in driving nucleolar localization is well established at this point - i.e. to me at least the bioinformatics analysis that precedes those results is unnecessary to have made the resulting prediction. Similarly, the authors find compositional biases in LCR proteins that are found in certain organelles, but those biases are also already established. These are not strictly criticisms, in that it's good that established patterns are found with this method, but I suppose my concern is that this is a lot of work that perhaps does not really push the needle particularly far.

As an important caveat to this somewhat muted reception, I recognize that having worked on problems in this area for 10+ years I may also be displaying my own biases, and perhaps things that are "already established" warrant repeating with a new approach and a new light. As such, this particular criticism may well be one that can and should be ignored.

That overall concern notwithstanding, I had several other questions that sprung to mind.

Dotplot matrix approach<br /> The authors do a fantastic job of explaining this, but I'm left wondering, if one used an algorithm like (say) SEG, defined LCRs, and then compared between LCRs based on composition, would we expect the results to be so different? i.e. the authors make a big deal about the dotplot matrix approach enabling comparison of LCR type, but, it's not clear to me that this is just because it combines a two-step operation into a one-step operation. It would be useful I think to perform a similar analysis as is done later on using SEG and ask if the same UMAP structure appears (and discuss if yes/no).

LCRs from repeat expansions<br /> I did not see any discussion on the role that repeat expansions can play in defining LCRs. This seems like an important area that should be considered, especially if we expect certain LCRs to appear more frequently due to a combination of slippy codons and minimal impact due to the biochemical properties of the resulting LCR. The authors pursue a (very reasonable) model in which LCRs are functional and important, but it seems the alternative (that LCRs are simply an unavoidable product of large proteomes and emerge through genetic events that are insufficiently deleterious to be selected against). Some discussion on this would be helpful. it also makes me wonder if the authors' null proteome model is the "right" model, although I would also say developing an accurate and reasonable null model that accounts for repeat expansions is beyond what I would consider the scope of this paper.

Minor points<br /> Early on the authors discuss the roles of LCRs in higher-order assemblies. They then make reference to the lysine tracts as having a valence of 2 or 3. It is possibly useful to mention that valence reflects the number of simultaneous partners that a protein can interact with - while it is certainly possible that a single lysine tracts interacts with a single partner simultaneously (meaning the tract contributes a valence of 1) I don't think the authors can know that, so it may be wise to avoid specifying the specific valence.

The authors make reference to Q/H LCRs. Recent work from Gutiérrez et al. eLife (2022) has argued that histidine-richness in some glutamine-rich LCRs is above the number expected based on codon bias, and may reflect a mode of pH sensing. This may be worth discussing.

Eric Ross has a number of very nice papers on this topic, but sadly I don't think any of them are cited here. On the question of LCR composition and condensate recruitment, I would recommend Boncella et al. PNAS (2020). On the question of proteome-wide LCR analysis, see Cascarina et al PLoS CompBio (2018) and Cascarina et al PLoS CompBio 2020.

Author Response

Reviewer #1 (Public Review):

The authors sought to create a machine learning framework for analyzing video recordings of animal behavior, which is both efficient and runs in an unsupervised fashion. The authors construct Selfee from recent computational neural network codes. As the paper is methodsfocused, the key metrics for success would be (1) whether Selfee performs similarly or more accurately than existing methods, and more importantly (2) whether Selfee uncovers new behavioral features or dynamics otherwise missed by those existing methods.

Weaknesses:

Although the basic schematics of Selfee are laid out, and the code itself is available, I feel that material in between these two levels of description is somewhat lacking. Details of what other previously published machine learning code makes up Selfee, and how those parts work would be helpful. Some of this is in the methods section, but an expanded version aimed at a more general readership would be helpful.

Thanks for the suggestions. We expanded the paragraphs describing training objectives and AR-HMM analysis. We also revised Figure 2C for clarity, and we have added a new figure, Figure 6, to describe how our pipeline works in detail. We also added a detailed instructions for Selfee usage on our GitHub page.

*The paper highlights efficiency as an important aspect of machine learning analysis techniques in the introduction, but there is little follow up with this aspect.

Our model only had a more efficient training process compared with other self-supervised learning methods. We also found our model could perform zero-shot domain transfer, so training may not even be necessary. However, we did not mean that our model was superior in terms of data efficiency or inference speed. We have revised some of the claims in the Discussion.

*In comparing Selfee to other approaches, the paper uses DeepLabCut, but perhaps running other recent methods for more comprehensive comparison would be helpful as well.

We compare Selfee feature extraction with features from FlyTracker or JAABA, two widely used software. We also visualized the tracking results of SLEAP and FlyTracker in complement to the DeepLabCut experiment.

*Using Selfee to investigate courtship behavior and other interactions was nicely demonstrated. Running it on simpler data (say, videos of individual animals walking around or exploring a confined space) might more broadly establish the method's usefulness.

We used Selfee with open field test (OFT) of mice after chronic immobilization stress (CIS) treatment. We demonstrated that our pipeline from data preprocessing to all the data mining algorisms with this experiment, and the results were added to the last section of Results.

Reviewer #2 (Public Review):

Jia et al. present a CNN based tool named "Selfee" for unsupervised quantification of animal behavior that could be used for objectively analyzing animal behavior recorded in relatively simple setups commonly used by various neurobiology/ethology laboratories. This work is very relevant but has some serious unresolved issues for establishing credibility of the method.

Overall Strengths: Jia et al have leveraged a recent development "Simple Siamese CNNs" to work for behavioral segmentation. This is a terrific effort and theoretically very attractive.

Overall Weakness: Unfortunately, the data supporting the method is not as promising. It is also riddled with incomplete information and lack of rationale behind the experiments.

Specific points of concern:

1) No formal comparison with pre-existing methods like JAABA which would work on similar videos as Selfee.

We added some comparisons with JAABA and FlyTracker extracted features, and also visualized FlyTracker and SLEAP tracking results aside from DeepLabCut. This result is now in the new Table 1. To avoid tracking inaccuracy during intensive interactions and potential inappropriately tuned parameters, we used a peer-reviewed dataset focused on wing extension behavior only. Our results showed a competitive performance of Selfee as other methods.

2) For all Drosophila behavior experiments, I'm concerned about the control and test genetic background. Several studies have reported that social behaviors like courtship and aggression are highly visual and sensitive to genetic background and presence of "white" gene. The authors use Canton S (CS) flies as control data. Whereas it is unclear if any or all of the test genotypes have been crossed into this background. It would be helpful if authors provide genotype information for test flies.

We have added a detailed sheet about their genotype in this version. The genetic information of all animals can also be found on the Bloomington fly center by the IDs provided. In brief, five fly lines used in this work are in the CS background: CCHa2-R-RAGal4, CCHa2-R-RBGal4, Dop2RKO, DopEcRGal4 and Tdc2RO54. We did not back cross other flies into the CS background for three reasons. First, most mutant lines are compared with their appropriate control lines. For example, in the original Figure 3B (the new Figure 4B), for CCHa2-R-RBGal4 > Kir2.1 flies contained wildtype white gene, so the comparison with CS flies would not cause any problem. For TrhGal4 flies, they were in white background, and so were other lines that had no phenotype. At the same time, in the original Figure 3G to J (the new Figure 4G to J), we used w1118 as controls for TrhGal4 flies, which were all in mutated white background. Second, in the original Figure 4F and G (the new Figure 5F and G), we admitted that the comparison between NorpA36, in mutated white background, and CS flies was not very convincing. Nevertheless, the delayed dynamic of NorpA mutants was reported before, and our experiment was just a demonstration of the DTW algorithm. Lastly, our method focused on the methodology of animal behavior analysis, and original videos were provided for research replications. Therefore, even if the behavioral difference was due to genetic backgrounds, it would not affect the conclusion that our method could detect the difference

3) Utility of "anomaly score" rests on Fig 3 data. Authors write they screened "neurotransmitter-related mutants or neuron silenced lines" (lines 251-252). Yet Figure 3B lacks some of the most commonly occurring neurotransmitter mutants/neuron labeling lines (e.g. Acetelcholine, GABA, Dopamaine, instead there are some neurotransmitter receptor lines, but then again prominent ones are missing). This reduces the credibility of this data.

First of all, this paper did not intend to conduct new screening assays, rather we used pre-existed data in the lab to demonstrate the application of Selfee. Previous work in our lab focused on the homeostatic control of fly behaviors, so most listed lines used here were originally used to test the roles of neuropeptides or neurons nutrient and metabolism regulation, such as CCHarelated lines, a CNMa mutant, and Taotie neuron silenced flies. There were some other important genes that were not involved in this dataset. Some most common transmitters are not included for two reasons. First, common neurotransmitters usually have a very global and broad effect on animal behaviors, and even if there is any new discovery, it could be difficult to interpret the phenomenon due to a large number of disturbed neurons. Second, most mutants of those common neurotransmitters are not viable, for example, paleGal4 as a mutant for dopamine; Gad1A30 for GABA, and ChATl3 for acetylcholine. However, we did perform experiments on serotonin-related genes (SerT and Trh), octopamine-related genes (Tdc and Oamb), and some other viable dopamine receptor mutants.

4) The utility of AR-HMM following "Selfee" analysis rests on the IR76b mutant experiment (Fig4). This is the most perplexing experiment! There are so many receptors implicated in courtship and IR76b is definitely not among the most well-known. None of the citations for IR76b in this manuscript have anything to do with detection of female pheromones. IR76b is implicated in salt and amino acid sensation. The authors still call this "an extensively studies (co)receptor that is known to detect female pheromones" (lines310-311). Unsurprisingly the AR-HMM analysis doesn't find any difference in modules related to courtship. Unless I'm mistaken the premise for this experiment is wrong and hence not much weight should be given to its results.

We have removed the Ir76b results from the Results. The demonstration of AR-HMM was now done with a mouse open field assay.

Reviewer #3 (Public Review):

This paper is describing a machine learning method applied to videos of animals. The method requires very little pre-processing (end-to-end) such as image segmentation or background subtraction. The input images have three channels, mapping temporal information (liveframes). The architecture is based on tween deep neural networks (Siamese network) and does not require human annotated labels (unsupervised learning). However, labels can still be used if they are produced, as in this case, by the algorithm itself - self-supervised learning. This flavor of machine learning is reflected in the name of the method: "Selfee." The authors are convincingly applying the Selfee to several challenging animal behavior tasks which results in biologically relevant discoveries.

A significant advantage of unsupervised and self-supervised learning is twofold: 1) it allows for discovering new behaviors, and 2) it doesn't require human-produced labels.

In this case of self-supervised learning the features (meta-representations) are learned from two views of the same original image (live-frame), where one of the views is augmented in several different ways, with a hope to let the deep neural network (ResNet-50 architecture in this case) learn to ignore such augmentations, i.e. learn the meta-representations invariant to natural changes in the data similar to the augmentations. This is accomplished by utilizing a Siamese Convolutional Neural Network (CNN) with the ResNet-50 version as a backbone. Siamese networks are composed of tween deep nets, where each member of the pair is trying to predict the output of another. In applications such as face recognition they normally work in the supervised learning setting, by utilizing "triplets" containing "negative samples." These are the labels.

However, in the self-supervised setting, which "Selfee" is implementing, the negative samples are not required. Instead the same image (a positive sample) is viewed twice, as described above. Here the authors use the SimSiam core architecture described by Chen, X. & He, K (reference 29 in the paper). They add Cross-Level Discrimination (CLD) to the SimSiam core. Together these two components provide two Loss functions (Loss 1 and Loss 2). Both are critical for the extraction of useful features. In fact, removing the CLD causes major deterioration of the classification performance (Figure 2-figure supplement 5).

The authors demonstrate the utility of the Selfee by using the learned features (metarepresentations) for classification (supervised learning; with human annotation), discovering short-lasting new behaviors in flies by anomaly detection, long time-scale dynamics by ARHMM, and Dynamic Time Warping (DTW).

For the classification the authors use k-NN (flies) and LightGBM (mice) classifiers and they infer the labels from the Selfee embedding (for each frame), and the temporal context, using the time-windows of 21 frames and 81 frames, for k-NN classification and LightGBM classification, respectively. Accounting for the temporal context is especially important in mice (LightGBM classification) so the authors add additional windowed features, including frequency information. This is a neat approach. They quantify the classification performance by confusion matrices and compute the F1 for each.

Overall, I find these classification results compelling, but one general concern is the criticality of the CLD component for achieving any meaningful classification. I would suggest that the authors discuss in more depth why this component is so critical for the extraction of features (used in supervised classification) and compare their SimSiam architecture to other methods where the CLD component is implemented. In other words, to what degree is the SimSiam implementation an overkill? Could a simpler (and thus faster) method be used - with the CLD component - instead to achieve similar end-to-end classification? The answer would help illuminate the importance of the SimSiam architecture in Selfee.

We added more about the contribution of the CLD loss in the last paragraph of Siamese convolutional neural networks capture discriminative representations of animal posture, the second section of Results. Further optimization of neural network architectures was discussed in the Discussion section. As for why CLD is that important, there are two main reasons. First of all, all behavior photos are so similar that it is not very easy to distinguish them from each other. In the field of so-called self-supervised learning without negative samples, researchers use either batch normalization or similar operations to implicitly utilize negative samples within a minibatch. However, when all samples are quite similar, it might not be enough. CLD uses explicit clusters to utilize negative samples within a minibatch, in the word of the authors “Our key insight is that grouping could result from not just attraction, but also common repulsion”, so that provides more powerful discrimination. The second reason is what the author argued in the CLD paper, CLD is very powerful in processing long-tailed datasets. As shown in the original Figure 2—figure supplement 5 (the new Figure 3—figure supplement 5), behavior data are highly unbalanced. As explained in the CLD paper. CLD fights against long-tailed distribution from two aspects. One is that it scales up the importance of negative samples within a mini-batch from 1/B to 1/K by k-means; another is that cluster operation could relieve the imbalance between the tail and head classes within a mini-batch. Here I quote: “While the distribution of instances in a random mini-batch is long-tailed, it would be more flattened across classes after clustering.” It was also visualized in Fig5 of the CLD paper.

To the best of our knowledge, SimSiam is the simplest method that would work with CLD. In the original CLD paper, they combined CLD method with other popular frameworks including BYOL and Mocov2. However, those popular frameworks are more complicated than SimSiam networks. We have attempted to combine CLD with BarlowTwins but failed. As the author of CLD suggested on Github: “Hi, good to know that you are trying to combine CLD with BarLowTwins! My concern is also on the high feature dimension, which may cause the low clustering quality. Maybe it is necessary to have a projection layer to project the highdimensional feature space to a low-dimensional one.” In terms of speed, there are two major parts. For inference, only one branch is used, so the major contribution of efficiency comes from CNN backbone. In theory, light backbones like MobileNet would work, but ResNet50 is already fast enough on a model GPU. As for training, the major computational cost aside from the CNN backbone is from Siamese branches. Two branches, two times of computation. Nevertheless, CLD relied on this kind of structure, so even if the learning framework is simpler than Simsiam, it is not likely to achieve a faster training speed. As for other structures, I think this new instance learning framework (https://arxiv.org/abs/2201.10728) is possible to achieve a similar result with fewer data and in a shorter time. However, this powerful method could be used with CLD. We might try it in the future.

One potential issue with unsupervised/self-supervised learning is that it "discovers" new classes based, not on behavioral features but rather on some other, irrelevant, properties of the video, e.g. proximity to the edges, a particular camera angle, or a distortion. In supervised learning the algorithm learns the features that are invariant to such properties, because humanmade labels are used and humans are great at finding these invariant features. The authors do mention a potential limitation, related to this issue, in the Discussion ("mode splitting"). One way of getting around this issue, other than providing negative samples, is to use a very homogeneous environment (so that only invariance to orientation, translation, etc, needs to be accomplished). This has worked nicely, for example, with posture embedding (Berman, G. J., et al; reference 19 in the manuscript). Looking at the t-SNE plots in Figure 2 one must wonder how many of the "clusters" present there are the result of such learning of irrelevant (for behavior) features, i.e. how good is the generalization of the meta-representations. The authors should explore the behaviors found in different parts of the t-SNE maps and evaluate the effect of the irrelevant features on their distributions. For example, they may ask: to what extent does the distance of an animal from the nearest wall affect the position in the t-SNE map? It would be nice to see how various simple pre-processing steps might affect the t-SNE maps, as well as the classification performance. Some form of segmentation, even very crude, or simply background subtraction, could go a very long way towards improving the features learned by Selfee.

In the new Figure 3—figure supplement 1, the visualization demonstrates that our features contained a lot of physical information, including wing angles, animal distance and positions in the chamber. “Mode-split” can be partially explained by those features. We actually performed background subtraction and image crop for mice behaviors, where we found them useful.

The anomaly detection is used to find unusual short-lasting events during male-male interaction behavior (Figure 3). The method is explained clearly. The results show how Selfee discovered a mutant line with a particularly high anomaly score. The authors managed to identify this behavior as "brief tussle behavior mixed with copulation attempts." The anomaly detection analyses were also applied to discover another unusual phenotype (close body contact) in another mutant line. Both results are significant when compared to the control groups.

The authors then apply AR-HMM and DTW to study the time dynamics of courtship behavior. Here too, they discover two phenotypes with unusual courtship dynamics, one in an olfactory mutant, and another in flies where the mutation affects visual transduction. Both results are compelling.

The authors explain their usage of DTW clearly, but they should expand the description of the AR-HMM so that the reader doesn't have to study the original sources.

We expanded the section that talks about AR-HMM mechanisms.

Author Response

Reviewer #1 (Public Review):

This work offers a simple explanation to a fundamental question in cell biology: what dictates the volume of a cell and of its nucleus, focusing on yeast cells. The central message is that all this can be explained by an osmotic equilibrium, using the classical Van't Hoff's Law. The novelty resides in an effort to provide actual numbers experimentally.

In this work, Lemière and colleagues combine physical modeling and quantitative measures to establish the basic principles that dictate the volume of a cell and of its nucleus. By doing so, they also explain an observation reported many times and in many different types of cells, of a proportionality between the volume of the cell and of its nucleus. The central message is that all this can be explained by an osmotic equilibrium, using the classical Van't Hoff's Law. This is because, in yeast cells, while the cell has a wall that can contribute to the equilibrium, the nucleus does not have a lamina and there is thus no elastic contribution in the force balance for the nucleus, as the authors show very nicely experimentally, using both cells and protoplasts and measuring the cell and nucleus volume for various external osmotic pressures (the Boyle Van't Hoff Law for a perfect gas, also sometimes called the Ponder relation) ¬- this was performed before for mammalian cells (Finan et al.), as cited and commented in the discussion by the authors, showing that mammalian cells have no significant elastic wall (linear relation) while the nucleus has one (non linear relation). This is well explained by the authors in the discussion. It is one of the clearer experimental results of the article. Together, the data and model presented in this article offer a simple explanation to a fundamental question in cell biology. In this matter, the principles are indeed seemingly simple, but what really counts are the actual numbers. While this article sheds some light on this aspect, it does not totally solve the question. The experiments are very well done and quantified, but some approximations made in the modeling are questionable and should at least be discussed in more length. Overall, this article is extremely valuable in the context of the recent effort of the cell biology and biophysics communities to understand the fundamental question of what dictates the size of cells and organelles. I have a few concerns detailed below. Importantly, there are many very interesting points of the article that I am not discussing below, simply because I completely agree with them.

1) The main concern is about the assumption made by the authors that the small osmolytes do not count to establish the volume of the nucleus. It was shown that small osmolytes such as ions are a vast majority of the osmolytes in a cell (more than ten times more abundant than proteins for example, which represent about 10 mM, for a total of 500 mM of osmolytes). This means that just a small imbalance in the amount of these between the nucleus and cytoplasm might have a much larger effect than the number of proteins, which is the osmolyte that authors choose to consider for the nuclear volume.

The point of the authors to disregard small osmolytes is that they can freely diffuse between the cytoplasm and the nucleus through the nuclear pores. They thus consider that the nuclear volume is established thanks to the barrier function of the nuclear envelope, which would retain larger osmolytes inside the nucleus and that the rest is balanced. This reasoning is not correct: for example, the volume of charged polymers depends on the concentration of ions in the polymer while there is no membrane at all to retain them. This is because of an important principle that the authors do not include in their reasoning, which is electro-neutrality.

Because most large molecules in the cell are charged (proteins and also DNA for the nucleus), the number of counterions is large, and is probably much larger than the number of proteins. So it is hard to argue that this could be ignored in the number of osmotically active molecules in the nucleus. This is known as the Donnan equilibrium and the question is thus whether this is actually the principle which dictates the nuclear volume.

The question then becomes whether the number of counterions differs between the cytoplasm and the nucleus, and more precisely whether the difference is larger than the difference considered by the authors in the number of proteins.

How is it possible to estimate this number? One of the numbers found in the literature is the electric potential across the nuclear envelope (Mazanti Physiological Reviews 2001). The number is between 1 and 10 mV, with more cations in the nucleus than in the cytoplasm. This number could correspond to much more cations than the number of proteins, although the precise number is not so simple to compute and the precision of the measure matters a lot, since there is an exponential relation between the concentrations and the potential.

This point above is simply made to explain that the authors cannot rule out the contribution of small osmolytes to the nuclear volume and should at least leave this possibility open in the discussion of their article.

As a conclusion, I totally agree with equation 3 which defines the N/C ratio, but I think that the Ns considered might not be the number of large macromolecules which cannot pass the nuclear envelope, but rather the small ones. Whether it is the case or not and what is actually the important species to consider depends on the actual numbers and these numbers are not established in this article. It is likely out of the scope of the article to establish them, but the point should at least be discussed and left open for future studies.

We appreciate these excellent points made by the reviewer and their numerous consultants. We amend the discussion of colloid osmotic pressure in the text to reflect these points.

2) The authors refer to the notion of colloidal pressure, discussed in the review by Mitchison et al. This term could be confusing and the authors should either explain it better or just not use it and call it perfect gas pressure or Van't Hoff pressure. Indeed, what is meant by colloidal pressure is simply the notion that all molecules could be considered as individual objects, independently of their size, and that it is then possible to apply the Van't Hoff Law just as it was a perfect gas, hence the notion of 'colloidal' pressure, which would be the osmotic pressure of all the individual molecules. The authors might want to discuss, or at least mention, that it is a bit surprising that all these crowded large macromolecules would behave like a perfect osmometer and that the Van't Hoff law applies to them. Alternatively, it could be simpler to consider that what actually counts for the volume is mostly small freely diffusing osmolytes, to which this law applies well, and which are much more numerous.

3) Very small point: on page 7 the authors refer to BVH's Law (Nobel, 1969). It is not clear what they mean. If they refer to the Nobel prize of Van't Hoff, it dates from 1901 (he died in 1911) and not 1969. I am not sure if there is something in one of the Nobel prizes delivered in 1969 which relates to this law. I checked but it does not seem to be the case, so it is probably a mistake in the date.

The citation is correct. It's a JTB paper by Park S. Nobel describing the BHV relation in biology.

4) On page 11, bottom, the result of the maintenance of the N/C ratio in protoplast is presented as an additional result, while it is a simple consequence of the previous results: both the cell and nuclear volume change linearly with the external osmotic pressure, so it is obvious that their ratio does not change when the external pressure is changed.

This result was not trivial. Although both cells and nuclei volume change linearly with the inverse of the external osmotic concentration in protoplasts, it was not obvious whether the two volumes change with the same proportion (ie same slope on the BVH graph).

Another result, not commented by the authors, is that this should be true only in protoplasts, since in whole cells, the cell wall is affecting the response of the cell volume, but not the nucleus, so the ratio should change.

In whole cells, the maintenance of the N/C ratio is in fact also maintained, consistent with the model. This result is now clarified in the manuscript (Figure 1C and D plus Figures 3D and S1C).

5) The results in Figure 5, with the inhibition of export from the nucleus, are presented as supporting the model. It is not really clear that they do. First the effect is very small, even if very clear. Again, the numbers matter here, so the interpretation of this result is not really direct and more calculation should be made to understand whether it can really be explained by a change of number of proteins. The result in panel F is even more problematic. The authors try to argue that the nucleus transiently gets denser, based on the diffusion of the GEMs and then adapts its density. It rather seems that it is overall quite constant in density, while it is the cell which has a decreasing density ¬- maybe, as suggested by the authors, because there are less ribosomes in the cytoplasm, so protein production is reduced. This could have an indirect effect on the number of amino acids (which would then be less consumed). A recent article by Neurohr et al (Trends in cell biology, 2020) suggests that such an effect can lead to cell dilution, in yeast, because the number of amino acids increases. In this particular case, this increase would affect the nuclear volume rather than the cell volume because of the presence of the cell wall and the rather small change.

We agree that there are different possible interpretations for these results. We have carefully reconsidered the interpretation and have rewritten the entire text for Figure 5

6) Page 16: it seems to me that the experiments presented in the chapter lines 360 to 376, on the ribosomal subunits, simply confirm that export is impaired, and they do not really contribute to confirm the hypothesis of the authors that it is the number of proteins in the nucleus which counts.

We agree. We highlight the ribosomal subunit proteins as they are very abundant nuclear shuttling proteins that provide a good example for the dynamics of nuclear protein accumulation.

The next paragraph with the estimation of the number of proteins in the nucleus and cytoplasm and how they change relatively upon export inhibition also appears to mostly demonstrate that export has been inhibited.

The authors propose to use the number they find, 8%, to compare it to the change in the N/C ratio, which is of the same order. Given how small these numbers are, and the precision of such measures, it is very hard to believe that these 8% are really precise at a level which could allow such a comparison. The authors should really estimate the precision of their measures if they want to claim that. It is more likely that what they observe is a small but significant change in both cases; a small change means it is small compared to the total, so it is a fraction of it, and it is measurable, which means it is more than just a few percent, which is usually not possible to measure. So it means that it is in the order of 10%. This is the typical value of any small but measurable change given a method for the measure which can detect changes around 10%. In conclusion, these numbers might not prove anything.

It could also be that the numbers match not just by chance, but that the osmolyte which matters is, for this type of experiment, changing in proportion to the amount of proteins (which would be possible for counter ions for example). But determining all that requires precise calculations and additional measures. It is thus more a matter of discussion and should be left more open by the authors.

We agree that these measurements are not so precise. We have carefully reworded this section and removed these specific comparisons.

Reviewer #2 (Public Review):

The goal of the paper is to test the idea that colloidal osmotic pressure controls nuclear growth as suggested by Tim Mitchison in a recent review.

In fleshing out the idea, Lemiere and colleagues develop a simple mathematical model that focuses on the forces generated by the movement of macromolecules across the nuclear-cytoplasmic boundary, ignoring any contribution of ions or small molecules which they assume equilibrate across the nuclear envelope. In testing this model, they focus their quantitative analysis on the response of cells that lack a wall (protoplasts) to osmotic shocks and to perturbations of nuclear export, protein synthesis and symmetric cell division. They also analyse the motion of small 40nm particles to test how diffusion is affected by these perturbations in both compartments.

Their analysis leads them to make some important observations that suggest that the system is even simpler than they might have hoped, since under the conditions tested nuclei (which lack lamins) behave as ideal osmometers. That is, the nuclei and cytoplasm grow and shrink in concert following sudden osmotic shocks. This suggests that the tension in the nuclear envelope, which gives nuclei their spherical shape, plays no role in constraining nuclear size.

While most of the paper's claims are well supported by their data under the assumptions of the model, there are a few claims that are less convincing.

For example, while their data are consistent with the idea that cells regulate their nuclear/cytoplasmic size ration using an adder type mechanism, in which a fix ratio of nuclear and cytoplasmic proteins are synthesised per unit time as cells grow, this has not been rigorously put to the test. In addition, while the diffusion analysis is very interesting, it does not fully support the authors' simple model linking diffusion, molecular crowding and colloidal osmotic pressure, something that could be more thoroughly discussed in the manuscript.

We added new data showing that slowing growth rate leads to a proportionate decrease in N/C ratio correction. This strengthens this portion of the paper.

We have added an improved discussion of the GEMs data and its limitations.

Reviewer #3 (Public Review):

This manuscript by Lemière and colleagues presents a view on how nuclear size is set by simple physical principles. The first part of the work describes a theoretical framework with the nucleus and the cell as two nested osmometers. Using fission yeast as a model, the authors then show that protoplasts and nuclei behave as ideal osmometers, i.e. show linear changes in volume upon change in external osmotic pressure. Consequently, the nuclear to cell volume ratio remains constant upon osmotic changes, but increases upon block of nuclear export, which leads to higher nuclear protein contents. Measurements of diffusion in the cytoplasm and nucleoplasm back these data. Finally, in the last part of the manuscript, the authors show that nuclear growth through a passive osmotic model can explain the previously described homeostasis of nuclear volume.

The manuscript is clearly written, and the data are clean and overall solid. I very much liked the simple view on the phenomenon of constant nuclear to cytosol ratio and the mix of modelling and experiments supporting the model that nuclear size is set passively by osmotic principles.

There are however a few points that are slightly at odds with the model and/or require further explanation to make the model compelling and discuss it in view of previous findings.

1) Isn't the finding that diffusion rates are faster in the nucleus (line 298, Fig S4C), indicating lower crowding in the nucleus, at odds with the finding that the non-osmotic volumes are similar in the two compartments? If the nucleus is less crowded, does this not suggest a lower pressure than the cytosol? I would also like to see this finding appear in Figure 4, which only reports on the normalized diffusion rates in both nuclei and cytosol.

We have added this figure to the main Figure 4, as requested. We agree that this raises some interesting questions. Our current interpretation is that composition of the nucleoplasm and cytoplasm are different and therefore affect GEMs diffusion and colloid osmotic pressure slightly differently.

2) Similarly, I don't understand the observed change in diffusion rates of GEMs upon LMB treatment (Fig 5F). If the nucleus behaves as an ideal osmometer, then any change in protein density between the nucleus and the cytosol, leading to change in osmotic pressure, will lead to a change in nuclear size that should re-equilibrate the osmotic pressures between the two compartments. The prediction would thus be that, if LMB treatment does not change overall protein concentration, at equilibrium there is no change in either osmotic pressure or density as measured by GEM diffusion rates. This is indeed illustrated by the constant normalized non-osmotic volume of the nucleus after LMB treatment. Is the change in diffusion rates perhaps only transient until a new steady state is reached? Or is there a change upon total protein content in the cell after LMB treatment?

3) In the experiments labelling proteins with FITC, are the reported values really those of protein concentrations or rather protein amounts? Isn't the enlargement of the nucleus upon LMB treatment compensating for this increase in amounts, returning the nucleus to a similar concentration as before treatment? A change in concentration is not in agreement with the reported constant non-osmotic volume of the nucleus.

These measurements of intensity are of concentrations. We add in the text this prediction that changes in concentration will be compensated for by swelling in nuclear volume and now interpret the data in light of this prediction. We add new data that total FITC staining for protein and RNA shows no change in concentration in compartments, consistent with this model.

4) The authors state that "a previous paper proposed a model for N/C ratio homeostasis based upon an active feedback mechanism (Cantwell and Nurse, 2019)" (lines 471-472). My understanding of this previous study is that nuclear size was proposed to be set by a limiting component, itself proportional to cell volume. No feedback was postulated. This previous model is in fact not too different from what the authors propose here, with the previously proposed limiting component now corresponding to the nuclear macromolecules that produce colloid osmotic pressure and thus set nuclear size. Though the present study goes significantly further in presenting the passive role of osmosis in setting nuclear size, it is a misrepresentation to portray this previous model as fundamentally different. Furthermore, it is not clear whether the new osmotic pressure-based model produces a better fit than the previous 'limiting component model'. Figure 7E here is very similar to Fig 4I in Cantwell and Nurse 2019, but it is difficult to judge the similarity of the fits.

The Cantwell and Nurse paper tested two models. The first was based upon nuclear growth being a fraction of cell growth. This model is qualitatively similar to ours. However, they discarded this initial model because it fitted poorly with their data. They then went to propose a second model, which contains a critical equation in which nuclear growth rate is a function of the N/C ratio, i.e. the system is sensing the N/C ratio and adjusting nuclear growth rate as a function of the N/C ratio. In other words, this is a feedback mechanism. The Cantwell paper does not describe this "feedback" term explicitly in the text, but it is clearly present in the equations. Therefore, our model which lacks any feedback term is fundamentally different from the Cantwell limiting component model.

We show that our model fits our data much better than the Cantwell model. We believe that the different views in these studies arise from differences in the experimental data. These differences may arise from two technical differences: 1) Their use of binning could be responsible for flattening the nuclear growth rate as a function of the nuclear volume at start. 2) Their estimates of cell and nuclear volumes using a 2D image and geometric assumptions may be less accurate than our automated 3D volume method.

5) If nuclear size is set purely by osmotic regulation, how do you explain that mutants in membrane regulation (such as nem1 and spo7, see Kume et al 2017; or lem2, see Kume et al 2019) previously shown to have an enlarged nucleus, display increased nuclear size?

This is an interesting question that we are currently pursuing. It is likely that these mutants affect multiple processes besides nuclear envelope expansion. For example, at least some of these mutants have altered chromatin organization could cause increase in colloid pressure. There may also be significant defects in chromosome segregation, which leads to production of different-sized nuclei with abnormal number of chromosomes. Some of the N/C ratio defects reported in these papers may arise from their 2D measurement methods, which are not accurate for misshapen nuclei. In our preliminary results, lem2 mutants do not have N/C ratio defects.

Author Response

Reviewer #1 (Public Review):

Weaknesses:

The data presented in the first part of the study are convincing. However, it is unclear whether each step of cell elongation and alignment, cell migration, cell dedifferentiation and regenerative response, is required for fin regeneration following amputation. As indicated in the discussion, the authors cannot provide evidence for the requirement of migration or dedifferentiation for the overall success of fin regeneration. Such limitations should be more clearly stated.

We have modified the title and abstract to avoid overstating the requirement of the particular responses to successful regeneration. Furthermore, we have stated the limitations of our study more clearly in the discussion.

We have removed the word “requires” from the title, it now reads: Zebrafish fin regeneration involves generic and regeneration-specific osteoblast injury responses

In the discussion we state the limitations on page 21 as follows:

“Unfortunately, currently existing tools to block dedifferentiation are either mosaic (activation of NF- κB signalling using the Cre-lox system) or cannot be targeted to osteoblasts alone (treatment with retinoic acid). Due to these limitations in our assays, we can currently not test what consequences specific, unmitigated perturbation of osteoblast dedifferentiation has for overall fin / bone regeneration. Conversely, the interventions presented here that specifically perturb osteoblast migration are limited as they act only transiently, that is they can severely delay, but not fully block migration. Furthermore, while interference with actomyosin dynamics reduces regenerative growth, we cannot distinguish whether this is caused by the inhibition of osteoblast migration or due to other more direct effects on cell proliferation and tissue growth. Thus, an unequivocal test of the importance of osteoblast migration for bone regeneration requires different tools.”

In the second part of the study, the term trauma needs to be clarified or reconsidered. A trauma model would imply that healing is impaired. Evidence for a non-healing phenotype is lacking and is expected in support of a trauma model.

We apologize if our use of the term trauma has caused confusion. We have simply used it interchangeably with “injury”. We have now removed all references to “trauma” in the text.

The authors describe the process of fin regeneration that may share common features with bone regeneration in other species. In the absence of direct evidence of common mechanisms between fin regeneration and bone regeneration in other systems, the authors should remain focused on "fin regeneration" in their conclusions rather than referring to "bone regeneration" and "bone formation" in more general terms.

We have rephrased the conclusion to have it more centred on bone regeneration in the fin. The relevant parts of the discussion now read on page 25 as follows:

In conclusion, our findings support a model in which zebrafish fin bone regeneration involves both generic and regeneration-specific injury responses of osteoblasts. Morphology changes and directed migration towards the injury site as well as dedifferentiation represent generic responses that occur at all injuries even if they are not followed by regenerative bone formation. While migration and dedifferentiation can be uncoupled and are (at least partially) independently regulated, they appear to be triggered by signals that emanate from all bone injuries. In contrast, migration off the bone matrix into the bone defect, formation of a population of (pre-) osteoblasts and regenerative bone formation represent regeneration-specific responses that require additional signals that are only present at distal-facing injuries. The identification of molecular determinants of the generic vs regenerative responses will be an interesting avenue for future research.

Reviewer #2 (Public Review):

The study by Sehring et al. depends on an extensive and thoroughly acquired collection of data points in combination with a robust and rigorous statistical analysis. I see that the authors have spent a lot of effort into this and I am overwhelmed by the number of analyzed data points that again depend on careful measurements at the cellular level in a more or less intact tissue. However, since just a fraction of cells has been chosen to be incorporated into the statistical analysis, there is a certain risk of a biased selection. I think the reader of the paper would appreciate a somewhat clearer picture of how the authors get to their final numbers, starting from the original image data. This appears of particular importance when it comes to determining the elongation of cells and the angular deviations from the proximo-distal axis. In many cases (e.g. Fig.2 A, B, D and E), the reader has to take those numbers without seeing any primary image data. A practicable solution to that issue would be to complement the accompanying Excel sheets of raw data with corresponding image material. This should show an overview of a representative sample for the dedicated experiment, together with some appropriate magnifications of analyzed cells including the axes along which those measurements have been performed. Also, it would be important to state within the methods section of the paper whether the measurements have been done manually using Fiji or whether a certain automated Fiji plug-in has been used for this part of the analysis.

Osteoblasts line the bony hemirays on the inner and outer surface (see Figure 1A), and for quantifications of osteoblast morphology, we analysed the osteoblasts of the outer layer of one hemiray (the hemiray facing the objective in whole mount imaging). While we have no direct evidence for this, we think it is reasonable to assume that osteoblasts in the other “sister” hemiray behave the same, and we have anecdotal evidence that osteoblasts on the inner surface of the hemirays also migrate and dedifferentiate. Thus, we don’t think that restriction of the analysis to one hemiray and the outer surface introduces bias.

For measurement of morphology, we used a transgenic line expressing a fluorescent protein (FP) in osteoblasts in combination with Zns5 antibody labelling. Zns5 is a pan-osteoblastic marker which localizes to the cell membrane. Therefore, combination of a cytosolic FP labelling with the membrane labelling by Zns5 provides solid definition of single cell outlines. For general morphology studies and drug intervention studies, we used bglap:GFP transgenics. In the transgenic intervention studies (manipulation of NF-kB signalling), mCherry is expressed together with CreERT2 under the osterix promoter and used as cytosolic labelling of osteoblasts. Our analyses are always based on segments, e.g. we present data for segments 0, -1, 2. Within these segments all FP+ Zns5+ cells were included into the analysis, and cells along the whole proximodistal axis of a segment were measured. Measurements were performed manually, and the analysist was blinded. With these set-ups, not only a fraction but all FP+ Zns5+ osteoblasts present in those segments that we analysed were included into the analysis, and thus no selection was necessary that could have introduced bias. As suggested by Reviewer #2, we have added representative sample images to the accompanying Excel sheets of raw data for the dedicated experiments. Within these, the axes along which the measurements have been performed are indicated.

We have expanded the description of the analysis in the method section. It now reads on page 36 as follows:

“To quantify osteoblast cell shape and orientation, the transgenic line bglap:GFP in combination with Zns5 AB labelling was used. Osteoblasts of the outer layer of one hemiray (facing the objective in whole fin mounting) were imaged and analysed. As Zns5 localizes to the plasma membrane of all osteoblasts, the combination of both markers provides solid definition of single cell outlines. All GFP+ Zns5+ cells with such a defined outline within an analysed segment were included into the analysis, and cells along the whole proximodistal axis of a segment were measured. In the transgenic intervention studies, mCherry is expressed under the osx promoter and was used as cytosolic labelling of osteoblasts. Using Fiji (Schindelin et al., 2012), the longest axis of a FP+ Zns5+ cell was measured as maximum length, the short axis as maximum width, and the ratio calculated. Simultaneously, the angle of the maximum length towards the proximodistal ray axis was measured for angular deviation. All measurements were performed manually, with the analyst being blinded.”

Along the same line, it would strengthen the statement provided by the statistical diagram in Fig.3A if the authors could show images of cells from segment -1 and -2 for all three experimental conditions. In particular, since the depicted segment -1 osteoblasts look rather roundish than elongated (compare with Fig.1 C and D, images and width/length ratio).

As suggested by the reviewer, we have added representative sample images of cells in segment -1 to the figure, the images that were already there in the previous version of the figure were from segment -2 (new data in Figure 4A). As legible from the graphs, there is a certain range of morphology within each segment / assay with an obvious overlap between the segments. This can make it difficult to realize the difference between the segments by looking on the images alone, and we have therefore added arrowheads to highlight examples of roundish and elongated cells. Yet as mentioned above, all cells were included into the analysis.

In regards to the biology itself, Sehring and colleagues claim that the complement system is required for injury-induced directed osteoblast migration. To strengthen this point it would be beneficial if the authors could show that the central complement components C3 and C5 are indeed expressed at the amputation site where the dedifferentiated pre-osteoblasts migrate to. It would be interesting to learn about the localization of C3 and C5 expression in the conventional amputation as well as the double-injury condition. Apparently, the RNAscope-based in situ hybridization seems to work quite well in the Weidinger lab.

Complement precursor proteins are thought to be mainly expressed in the liver and distributed throughout the body via the circulation. Injury would then result in local production of the activated C3a and C5a peptides via a cascade of proteolytic processing. Unfortunately, we lack the tools to detect the C3 and C5 precursor proteins or the mature cleavage products of the complement factors, which mediate the biological function of the cascade (e.g. antibodies against the zebrafish proteins / peptides). We have also attempted RNAScope for c5a and c3a.1 in fins, but these turned out to not produce any specific stainings, thus the results of these experiments remained inconclusive and we have not included them in the manuscript.

However, we analysed expression of the RNA coding for the precursors of the complement factors c5 and the six zebrafish paralogs of c3 using qRT-PCR on liver, non-injured fins and fins at 6 hpa (samples derived from segment -1 plus segment 0). These new data can be found in Figure 5B. Compared to the expression levels in the liver, expression in non-injured fins could hardly be detected. Interestingly, c5 and c3a.5 levels were upregulated in injured fins, but compared to the expression in the liver still only slightly, e.g. c5 is about 17 Ct values (2 to the power of 17 = 130000 times) more highly expressed in the liver than in the injured fin. These results are consistent with the idea that the majority of complement factors that are activated after injury is derived from precursors that are expressed in the liver and are distributed via the circulation to the fin, as is considered standard for the complement system. Interestingly, however, local production might contribute as well.

Overall our new data support our conclusion that the complement system is an important regulator of osteoblast migration in vivo, since the receptors are present in osteoblasts (see also response to the next issue), while systemic and local expression can provide the precursors for injury-induced production of the activated factors that might act as guidance cues.

To judge whether this osteoblast's migratory response is cell-type specific and cell-autonomous it would be good to know if c5ar1 and c3ar are solely expressed in osteoblasts, or rather broadly within tissue lining the hemirays.

While we had already shown that c5aR1 is expressed in osteoblasts, we have now added additional RNAscope in situ analysis for c5aR1 showing that the receptor is also expressed in other cell types (new data in Figure 5 – figure supplement 1A). We have also attempted RNAScope for c3aR in fins, which however did not produce specific staining, thus remained inconclusive; we have not added these data to the manuscript. However, we established fluorescent activated cell sorting from bglap:GFP transgenic fins, which gives us an additional tool to analyse to which extent expression is specific to osteoblasts. By qRT-PCR analysis we found that c5aR1 and c3aR are expressed in both GFP+ osteoblasts and other cells that are GFP– (these will mainly represent epidermis and fibroblasts, to a lesser extent endothelial and other cell types). These new data can be found in Figure 5 – figure supplement 1B.

While our qRT-PCR data and the c5aR1 RNAScope results show that the complement receptors are not specifically expressed in osteoblasts, we do not consider this result to be in conflict with our model that the complement system regulates osteoblast migration. Other cell types migrate after fin amputation as well, which is best described for epidermal cells (Chen et al., Dev Cell 2016, 10.1016/j.devcel.2016.02.017), but likely also occurs for fibroblasts (Poleo et al., DevDyn 2001, doi: 10.1002/dvdy.1152), and it is conceivable that the complement system plays a role in regulating these events as well.

Reviewer #3 (Public Review):

Weaknesses:

1) The major conclusions on osteoblast dedifferentiation and migration are solely based on a bglap:GFP strain, which does not allow a pulse-chase approach in injury responses. Specificity of this strain to osteoblasts is also doubtful because as many as 20% of GFP+ cells are in proliferation. Specificity of bglap:GFP to mature osteoblasts is a major concern. Important caveats associated with this reporter strain are not carefully considered.

To address these comments, we have performed several additional experiments as described below. In addition, we would like to refer the reviewer to our previous papers, where we have analysed the process of osteoblast dedifferentiation (Knopf et al., Dev Cell 2011, doi: 10.1016/j.devcel.2011.04.014; Geurtzen et al., Development 2014, doi: 10.1242/dev.105817; Mishra et al. Dev Cell 2020, doi: 10.1016/j.devcel.2019.11.016). Using transgenic reporters and immunofluorescence we have shown in these previous papers that osteoblasts in the non-injured fin express Bglap but not the pre-osteoblast marker Runx2 (and are thus by our definition differentiated). We apologize if we failed to explain the logic of our approach in this manuscript, we have restructured the results to clarify these, as indicated below.

We have also performed the following additional experiments.

1) To confirm the specificity of the bglap:GFP line for mature osteoblasts, we have performed three experiments:

a) immunofluorescence against Runx2 on 7 dpa regenerates, at a stage where blastema proliferation at the distal tip of the regenerate produces new osteoblast progenitors, while in more proximal (older) regions osteoblasts have already started to differentiate and new bone matrix has formed. We found that Runx2 is expressed in distal regions in pre-osteoblasts, while bglap:GFP is only expressed in proximal regions in osteoblasts which do not express Runx2. Thus, formation of new bony segment during regenerative growth, bglap:GFP is activated in mature osteoblasts and the population does not include osteoblast precursor cells. These new data are found in Figure 2 – figure supplement 2B.

b) we have refined and expanded our methods and are now able to determine the expression patterns of markers of the osteoblast differentiation status with single cell resolution using RNAScope in situ hybridization. Using this, we can now show that at 1 day post amputation, in segment -2 of the fin stump, which represents a segment equivalent to the non-injured state, since no dedifferentiation occurs here, bglap:GFP+ cells do not express endogenous runx2a. These new data are found in Figure 1 – figure supplement 1A.

c) Using RNAScope, we can show that cyp26b1, a gene associated with dedifferentiated osteoblasts, is likewise not detected in bglap:GFP+ cells in segment -2 at 1 dpa (new data in Figure 1 – figure supplement 1B).

Together, these data confirm that the bglap:GFP line is specific for differentiated osteoblasts, and does not label osteoblast progenitors. See the response to issue 2 below for how we describe these new data in the revised version of the manuscript.

2) Regarding the proliferation of bglap:GFP osteoblasts: In the experiment the reviewer refers to (now Figure 5 – figure supplement 3A), we make use of the persistence of the GFP protein in the bglap:GFP line to detect dedifferentiated osteoblasts. Thus, at the time of analysis, when these GFP+ cells proliferate, they are not differentiated anymore. We can show this as follows:

Although bglap expression is downregulated during osteoblast dedifferentiation and thus also GFP levels eventually drop in the transgenic line, we can nevertheless use this line to trace osteoblasts, since GFP protein persists for up to three days in cells that shut down endogenous bglap and also bglap:GFP transgene transcription. While we have already shown this previously (Knopf et al., Dev Cell 2011, doi: 10.1016/j.devcel.2011.04.014; Geurtzen et al., Development 2014, doi: 10.1242/dev.105817; Mishra et al. Dev Cell 2020, doi: 10.1016/j.devcel.2019.11.016), we have now also used RNAScope to confirm this. We analysed the expression of GFP on protein and RNA level in the bglap:GFP line. In bglap:GFP fish, in a mature segment in non-injured fins the regions close to the joints are devoid of cells expressing GFP (Figure 1G). Yet after amputation, we observe GFP+ cells in this distal part of segment -1 (Figure 1G, D). RNAscope in situ shows that these GFP+ cells are negative for gfp RNA (new data in Figure 1D). Thus, the observed fluorescence is due to the persistence of the GFP protein and not due to a potential upregulation of the transgene (Figure 1E).

Importantly, we have now also added data describing the proliferative state of bglap:GFP+ osteoblasts. First, in the non-injured fin, bglap:GFP+ cells are non-proliferative (new data in Figure 5 – figure supplement 2B). After amputation, proliferation can be detected in GFP+ cells at 2 dpa (Figure 5 – figure supplement 2B), and proliferation is restricted to segment -1 and segment 0 (new data in Figure 5 – figure supplement 2C). As we show in Figure 1B, at 2 dpa, dedifferentiation as defined by bglap downregulation is not complete in segment -1, rather here a mixture of cells with different bglap levels are found. We have thus combined EdU labelling with RNAscope against bglap in segment -1 to analyse to which extent bglap and EdU anticorrelate. These data show that EdU is hardly ever incorporated into cells expressing high levels of bglap, while the majority of the proliferating osteoblasts are dedifferentiated, as they express only low levels of bglap (new data in Figure 5 – figure supplement 2D). Together, these data show that mature osteoblasts are non-proliferative, and upon amputation, when they are dedifferentiated, they become proliferative. Thus, the absence of proliferation in bglap:GFP+ cells in the non-injured fin adds to the evidence that this line is specific for mature osteoblasts, but due to the persistence of the GFP protein it can be used to analyse dedifferentiated osteoblasts.

These data are described on page 14 of the manuscript as follows:

“In the non-injured fin, bglap:GFP+ osteoblasts are non-proliferative, but upon amputation osteoblasts proliferate at 2 dpa (Figure 5 – figure supplement 2A, B). Proliferation is restricted to segment -1 and segment 0 (Figure 5 – figure supplement 2C), and RNAscope in situ analysis of bglap expression revealed that the majority of EdU+ osteoblasts have strongly downregulated bglap (Figure 5 – figure supplement 2D). Inhibition of C5aR1 with PMX205 had no effect on osteoblast proliferation in segment -1 at 2 dpa (Figure 5 – figure supplement 3A). Furthermore, upregulation of Runx2 was not changed by PMX205 treatment (Figure 5 – figure supplement 3B), and regenerative growth was not affected in fish treated with either W54011, PMX205 or SB290157 (Figure 5 – figure supplement Figure 3C). We conclude that the complement system specifically regulates injury-induced osteoblast migration, but not osteoblast dedifferentiation or proliferation in zebrafish.”

3) To support our conclusion that osteoblasts migrate, we performed time-lapse imaging using a transgenic line expressing the photoconvertible protein kaede in osteoblasts (entpd5:kaede). Local photoconversion of only the proximal half of a segment allowed us to trace these photoconverted osteoblasts. This revealed that converted cells appear in the distal part of the segment within 1 dpa, which can only be explained by relocation of the cells. These new data can be found in Figure 1F and they are described on page 7 of the revised manuscript as follows: To trace osteoblasts, we used the transgenic line entpd5:kaede (Geurtzen et al., 2014), in which Kaede fluorescence can be converted from green to red by UV light (Ando et al., 2002). We photoconverted osteoblasts in the proximal half of segment -1, while osteoblasts in the distal half remained green (Fig. 1F). At 1 dpa, red osteoblasts were found in the distal half (Fig. 1F), showing that photoconverted osteoblasts had relocated distally.

2) The authors poorly define dedifferentiation. They use reduced bglap:GFP or bglap mRNA expression as a sole criterion for dedifferentiation. The authors state that NF-kB and retinoic acid can inhibit osteoblast dedifferentiation. However, this simply reflects of the well-described fact that these signals promote osteoblast differentiation.

We define dedifferentiation as the reversion of a mature cell into an undifferentiated progenitor-like status. This involves the following characteristics: 1) the expression of markers of the differentiated state are downregulated; 2) early lineage markers are re-expressed; 3) the cells become proliferative; and 4) they have the ability to re-differentiate into mature cells. Based in this definition, the downregulation of an osteoblast-specific marker can be used as a read-out for osteoblast dedifferentiation. Bglap is an established marker for mature osteoblasts (Kaneto et al., 2016 doi.org/10.1186/s12881-016-0301-7¸ Yoshioka et al., 2021 doi: 10.1002/jbm4.10496; Kannan et al., 2020 doi: 10.1242/bio.053280; Sojan et al., 2022 doi.org/10.3389/fnut.2022.868805; Valenti et al., 2020 doi.org/10.3390/cells9081911). While we use downregulation of bglap expression as our main read-out for osteoblast dedifferentiation in our experimental interventions (actomyosin inhibition, retinoic acid treatment, complement inhibition), we have expanded our methods to characterize osteoblast dedifferentiation, and have re-arranged our manuscript to show these data in the beginning of the results.

Already in the previous version of the manuscript we have shown that endogenous bglap is strongly expressed in segment -2, (the segment that does not respond to fin amputation and thus represents the non-injured state), while it is downregulated in a graded manner in segment -1 and segment 0 (the segments where dedifferentiation happens). We have now moved this data to the re-designed Figure 1B. In addition to bglap, we can now show that entpd5, a gene required for bone mineralization, is strongly expressed in osteoblasts of segment -2, while it is massively downregulated in segment -1 and segment 0. These new data can be found in Figure 1C. Thus, entpd5 is another differentiation marker whose loss characterizes osteoblast dedifferentiation. Importantly, we can confirm by RNAScope that the pre-osteoblast marker runx2a is absent in mature segments but is upregulated in segment 0 and segment -1 at 1 dpa (new data in Figure 1 – figure supplement 1A). Similarly, cyp26b1, an enzyme shown to regulate dedifferentiation, is upregulated in segment 0 and segment -1, but not expressed in segment -2. (new data in Figure 1 – figure supplement 1B). Furthermore, we have repeated all experiments where we have previously quantified dedifferentiation upon experimental interventions using downregulation of bglap:GFP (actomyosin inhibition, retinoic acid treatment, complement inhibition). We now can fully confirm the previous conclusions using the more rigorous quantification of dedifferentiation using RNAScope analysis of endogenous bglap levels. We have replaced all bglap:GFP data with the new bglap RNAScope data. These new data are found in Figure 3F, Figure 3 – figure supplement 1A, Figure 4B and Figure 5F.

Overall, we support our conclusion that osteoblasts dedifferentiate by the loss of the two differentiation markers bglap and entpd5, the upregulation of the pre-osteoblast marker runx2a and the dedifferentiation-associated gene cyp26b1, and the fact that osteoblasts become proliferative. We hope that the reviewer considers this sufficient evidence.

In mammals, the available literature relatively convincingly concludes that NF-kB signaling negatively regulates osteoblast differentiation (Yao et al., 2014, doi: 10.1002/jbmr.2108; Swarnkar et al., 2014 doi.org/10.1371/journal.pone.0091421, Chang et al., 2009, doi.org/10.1038/nm.1954). Yet in zebrafish osteoblasts, we have previously shown that NF-kB signaling is active in mature osteoblasts and needs to be downregulated for dedifferentiation to occur (Mishra et al., 2020, 10.1016/j.devcel.2019.11.016). Importantly, in our previous work we showed that at least during fin regeneration, NF-kB signalling is not involved in osteoblast differentiation (Mishra et al., 2020, 10.1016/j.devcel.2019.11.016). Specifically, osteoblasts in which Nf-kappaB signaling is enhanced or inhibited differentiate completely normally during the later stages of fin regeneration in the fin regenerate. Hence, our findings with the Nf-kappaB intervention studies done in this manuscript, where we look at osteoblasts in the stump within 1 dpa, cannot be explained by them affecting osteoblast differentiation.

For retinoic acid signalling, multiple roles in bone development and repair have been described in mammals. For zebrafish osteoblasts, it was shown that during the outgrowth phase of bone regeneration, retinoic acid negatively regulates osteoblast differentiation in the blastema (Blum & Begemann, 2015, 10.1242/dev.120204). Yet importantly, it also negatively controls the dedifferentiation of osteoblasts in the stump right after amputation (Blum & Begemann, 2015, 10.1242/dev.120204). Thus, the effect we observe at the early timepoints we analyse in our intervention studies (retinoic acid treatment) are due to the effect on osteoblast dedifferentiation.

We have added a short definition of dedifferentiation to the results section (page 6). There it reads as follows:

“We have previously shown that osteoblasts dedifferentiate in response to fin amputation, that is they revert from a mature, non-proliferative state into an undifferentiated progenitor-like state, which includes loss of bglap expression and upregulation of the pre-osteoblast marker runx2 (Knopf et al., 2011; Geurtzen et al., 2014).”

In addition, we have restructured the results to describe our use of tools and the new data on page 6 of the revised manuscript as follows:

Using RNAScope in situ hybridization, we can now show that downregulation of bglap occurs in a graded manner and that entpd5 expression is similarly downregulated during dedifferentiation (Figure 1B, C). At 1 day post amputation (1 dpa), expression of entpd5 and bglap remains high in segment -2, but gradually decreases towards the amputation plane and is almost entirely absent from segment 0, with entpd5 downregulation being more pronounced (Figure 1B, C). While RNA expression of these genes is downregulated within hours after injury, GFP or Kaede fluorescent proteins (FPs) expressed in bglap or entpd5 reporter transgenic lines persist for up to three days, even though transgene transcription is shut down rapidly as well (Knopf et al., 2011). We can confirm these earlier findings using the more sensitive RNAScope in situs. In bglap:GFP transgenics at 2 dpa, gfp RNA and GFP protein colocalized to the same cells in segment -2, where osteoblasts do not dedifferentiate (Fig. 1D). In contrast, in the distal segment -1 GFP protein was present, but barely any gfp transcript could be detected (Fig. 1D). Thus, persistence of FPs in reporter lines can be used for short-term tracing of dedifferentiated osteoblasts (Fig. 1E). At 1 dpa, bglap:GFP+ cells upregulated expression of the pre-osteoblast marker runx2a and of cyp26b1, an enzyme involved in retinoic acid signalling (Blum and Begemann, 2015), which regulates dedifferentiation (Figure 1 – figure supplement 1A, B). Both markers were exclusively upregulated in segment -1 and segment 0 at 1 dpa, but were absent in segment -2. Together, these data show that osteoblasts in segment -1 and segment 0 lose expression of mature markers and gain expression of dedifferentiation markers.

3) The authors do not rigorously demonstrate that mature osteoblasts indeed migrate. What they showed in this study is simply cell shape changes.

We have the following evidence for osteoblast migration:

1) bglap:GFP+ cells relocate from the centre of segments towards the amputation plane (after fin amputations) or towards both injuries in the hemiray model. In this revised manuscript we show that transgene expression is not upregulated in these regions, but that GFP fluorescence there must be due to relocation of cells in which GFP protein persists (new data in Figure 1D, E; see also response to “Weaknesses, issue 1” above)

2) Using the entpd5:kaede transgenic line, which is expressed in mature osteoblasts throughout segments, we have photoconverted only the proximal half of a segment, which allowed us to trace these photoconverted osteoblasts. This revealed that converted cells appear in the distal part of the segment within 1 dpa, which can only be explained by relocation of the cells. These new data can be found in Figure 1F.

3) Already in the previous version of the manuscript, we have performed live imaging to track single cell behaviour. Using double transgenic fish expressing both GFP and kaede in osteoblasts, we deliberately only partly converted kaedeGreen to kaedeRed, which resulted in different hues for each osteoblast. This distinct colouring facilitates observing single cells. Video 1 shows the directed movement of cell bodies relative to their surroundings within 2 hours (see also Figure 2 – figure supplement 1A).

4) Osteoblasts display the typical cell shape changes associated with active migration (elongation along the axis of migration, extension of dynamic protrusions), data in Figure 2.

Together, we think these are convincing data supporting the conclusion that osteoblasts actively migrate.

4) The hemiray removal model is highly innovative, but this part of the study is not very well connected to the rest of the study.

We have rephrased the first sentence of the hemiray paragraph to make the connection more perceptible. It now reads as follows:

In response to fin amputation, all osteoblast injury responses occur directed towards the amputation plane, that is dedifferentiation is more pronounced distally, osteoblasts migrate distal wards and the proliferative pre-osteoblast population forms distally of the amputation plane. We wondered how osteoblasts respond to injuries that occur proximal to their location. To test this, we established a fin ray injury model featuring internal bone defects.

Author Response

Reviewer #2 (Public Review):

Summary: This substantial collaborative effort utilized virus-based retrograde tracing from cervical, thoracic and lumbar spinal cord injection sites, tissue clearing and cutting-edge imaging to develop a supraspinal connectome or map of neurons in the brain that project to the spinal cord. The need for such a connectome-atlas resource is nicely described, and the combination of the actual data with the means to probe that data is truly outstanding.

They then compared the connectome from intact mice to those of mice with mild, moderate and severe spinal cord injuries to reveal the neuronal populations that retain axons and synapses below the level of injury. Finally, they look for correlations between the remaining neuronal populations and functional recovery to reveal which are likely contributing to recovery and its variability after injury. Overall, they successfully achieve their primary goals with the following caveats: The injury model chosen is not the most widely employed in the field, and the anatomical assessment of the injuries is incomplete/not ideal.

Concerns/issues:

1) I would like to see additional discussion/rationale for the chosen injury model and how it compares to other more commonly employed animal models and clinical injuries. Please relate how what is being observed with the supraspinal connectome might be different for these other models and for clinical injuries.

We have added text to the Results and Discussion to explain our rationale for selecting the crush injury model, and to acknowledge differences between this model and more clinically relevant contusion models. (Results: line 360-364, Discussion 608-615). We agree wholeheartedly that a critical future direction will be to deploy brain-wide quantification in contusion models, and we are currently seeking funding to obtain the needed equipment.

2) The assessment of the thoracic injuries employed is not ideal because it provides no anatomical description of spared white matter (or numbers of spared axons) at the injury epicenter.

We address this more fully in the related point below. Briefly, we agree with a need to improve the assessment of the lesion but are hampered by tissue availability. We are unable to assess white matter sparing but can offer quantification of the width of residual astrocyte tissue bridges in four spinal sections from each animal (new Figure 5 – figure supplement 3). As discussed below, however, we recognize the limitations of the lesion assessment and agree with the larger point that the current quantification methods do not position us to make claims about the relative efficacy of spinal injury analyses versus whole-brain sparing analyses to stratify severity or predict outcomes. Our approach should be seen as a complement, not a substitute, for existing lesion-based analyses. We have edited language throughout the manuscript to make this position clearer.

3) Related to this, but an issue that requires separate attention is the highly variable appearance of the injury and tracer/virus injection sites, the variability in the spatial relationship with labeled neurons (lumbar) and how these differences could influence labeling, sprouting of axons of passage and interpretation of the data. In particular this is referring to the data shown in Figure 6 (and related data).

It is true that there is some variability in the relative position of the injury and injection, a surgical reality. The degree of variability was perhaps exaggerated in the original Figure 6 (Now Figure 5), in which one image came from one of two animals in the cohort with a notably larger gap between the injury and injection. Nevertheless, this comment raises the important question of how variability in injection-to-injury distance might affect supraspinal label. First, we would emphasize the data in Figure 1 – Figure Supplement 6, in which we showed that the number of retrogradely labeled supraspinal neurons is relatively stable as injection sites are deliberately varied across the lower thoracic and lumbar cord. Indeed, the question raised here is precisely the reason we performed this early test to determine how sensitive the results might be to shifts in segmental targeting. The results indicate that retrograde labeling is fairly insensitive to L1 versus L4 targeting. As an additional check for this specific experiment we also measured the distance between the rostral spread of viral label and the caudal edge of the lesion and plotted it against the total number of retrogradely labeled neurons in the brain. If a smaller injury/injection gap favored more labeling we might expect negative correlation, but none is apparent. We conclude that although the injury/injection distance did vary in the experiment, it likely did not exert a strong influence on retrograde labeling.

Reviewer #3 (Public Review):

In this manuscript, Wang et al describe a series of experiments aimed at optimizing the experimental and computational approach to the detection of projection-specific neurons across the entire mouse brain. This work builds on a large body of work that has developed nuclear-fused viral labelling, next-generation fluorophores, tissue clearing, image registration, and automated cell segmentation. They apply their techniques to understand projection-specific patterns of supraspinal neurons to the cervical and lumbar spinal cord, and to reveal brain and brainstem connections that are preferentially spared or lost after spinal cord injury.

Strengths:

Although this work does not put forward any fundamentally new methodologies, their careful optimization of the experimental and quantification process will be appreciated by other laboratories attempting to use these types of methods. Moreover, the observations of topological arrangement of various supraspinal centres are important and I believe will be interesting to others in the field.

The web app provided by the authors provides a nice interface for users to explore these data. I think this will be appreciated by people in the field interested in what happens to their brain or brainstem region of interest.

Weaknesses:

Overall the work is well done; however, some of the novelty claims should be better aligned with the experimental findings. Moreover, the statistical approaches put forward to understand the relationship between spinal cord injury severity and cell counts across the mouse brain needs to be more carefully considered.

The authors state that they provide an experimental platform for these types of analysis to be done. My apologies if I missed it but I could not find anywhere the information on viral construct availability or code availability to reproduce the results. Certainly both of these aspects would be required for people to replicate the pipeline. Moreover, the described methodology for imaging and processing is quite sparse. While I appreciate that this information is widely provided in papers that have developed these methods, I do not think it is appropriate to claim to have provided a platform for people to enable these types of analyses without a more in-depth description of the methods. Alternatively, the authors could instead focus on how they optimized current methodologies and avoid the overstatement that this work provides a tool for users. The exception to this is of course the viral constructs, the plasmids of which should be deposited.

We agree that we have not provided a tool per se, more of an example that could be followed. We have revised language in the abstract, introduction, and discussion to make it clear that we optimized existing methods and provide an example of how this can be done, but are not offering a “plug and play” solution to the problem of registration that would, for example, allow upload of external data. For example, in the abstract we replaced “We now provide an experimental platform” with “Here we assemble an experimental workflow.” (Line 28). The term “platform” no longer appears in the manuscript and has been replaced throughout by “example.” We how this matches the intention of the comment and are happy to revise further as needed. Note that the plasmids have been deposited to Addgene.

It was not completely to me clear why or when the authors switch back and forth between different resolutions throughout the manuscript. In the abstract it states that 60 regions were examined, but elsewhere the number is as many as 500. My understanding is that current versions of the Allen Brain Annotation include more than 2000 regions. I think it would make things clear for the readers if a single resolution was used throughout, or at least justified narratively throughout the text to avoid confusion.

Thank you for pointing this out. The Cellfinder application recognizes 645 discrete regions in the brain, and across all experiments we detected supraspinal nuclei in 69 of these. This number, however, includes some very fine distinctions, for example three separate subregions of vestibular nuclei, three subregions of the superior olivary complex, etc. True experts may desire this level of information, but with the goal of accessibility we find it useful to collapse closely related / adjacent regions to an umbrella term. Doing so generates a list of 25 grouped or summary regions. In the revised version we move the 69-region data completely to the supplemental data (there for the experts who wish to parse), and use the consistent 25-region system (plus cervical spinal cord in later sections) to present data in the main figures. We have added text to the Results section (lines 157-162) to clarify this grouping system.

The others provide an interesting analysis of the difference between cervical and lumbar projections. I think this might be one of the more interesting aspects of the paper - yet I found myself a bit confused by the analysis, and whether any of the differences observed were robust. Just prior to this experiment the authors provide a comparison of the mScarlet vs. the mGL, and demonstrate that mGL may label more cells. Yet, in the cervical vs. lumbar analysis it appears they are being treated 1 to 1. Moreover, I could not find any actual statistical analysis of this data? My impression would be that given the potential difference in labelling efficiency between the mScarlet and mGL this should be done using some kind of count analysis that takes into account the overall number of neurons labelled, such as a Chi-sq test or perhaps something more sophisticated. Then, with this kind of statistical analysis in place, do any of the discussed differences hold up? If not, I do not think this would detract from the interesting topological observations - but would call on the authors to be a bit more conservative about their statements and discussion regarding differences in the proportions of neurons projecting to certain supraspinal centers.

This is an important point. In response to this input and related comments from other reviewers we performed new experiments to assess co-localization. The new data address the point above by including quantification of the degree of colocalization that results from titer-matched co-injection of the two fluorophores, providing baseline data. The results of this can be found in Figure 3 – figure supplement 3 and form the basis for statistical comparisons to experimental animals shown in Figure 3.

Finally, I do have some concerns about the author's use of linear regression in their analysis of brain regions after varying severities of SCI. First of all, the BMS score is notoriously non-linear. Despite wide use of linear regressions in the field to attempt to associate various outcomes to these kinds of ordinal measures, this is not appropriate. Some have suggested a rank conversion of the BMS prior to linear analyses, but even this comes with its own problems. Ultimately, the authors have here 2-3 clear cohorts of behavioral scores and drawing a linear regression between these is unlikely to be robustly informative. Moreover, it is unclear whether the authors properly adjusted their p-values from running these regressions on 60 (600?) regions. Finally, the statement in the abstract and discussion that the authors "explain more variability" compared to typical lesion severity analysis is also unsupported. My suggestion would be the following:

Remove the linear regression analyses associated with BMS. I do not think these add value to the paper, and if anything provide a large window of false interpretation due to a violation of the assumptions of this test.

Consider adding a more appropriate statistical analysis of the brain regions, such as a non-parametric group analysis. Knowing which brain regions are severity dependent, and which ones are not, would already be an interesting finding. This finding would not be confounded by any attempt to link it to crude measures of behavior.

We agree that the linear regression approach was flawed and appreciate the opportunity to correct it. After consultation with two groups of statisticians we were forced to conclude that the data are simply underpowered for mixed model and ranking approaches. We therefore adopted a much simpler strategy. As you point out (and as noted by the statisticians), the behavioral data are bimodal; one group of animals regained plantar stepping ability, albeit with varying degrees of coordination (BMS 6-8), while the others showed at most rare plantar steps (BMS 0-3.5). We therefore asked whether the number of spared neurons in each brain region differed between the two groups and also examined the degree of “overlap” in the sparing values between the two groups. The data are now presented in Figure 6.

If the authors would like to state anything about 'explaining more variability' then the proper statistical analysis should be used, which in this case would be to compare the models using a LRT or equivalent. However, as I mentioned it does not seem to be appropriate to be doing this with linear models so the authors should consider a non-linear equivalent if they choose to proceed with this.

We thank the reviewer for the excellent suggestion. However as we explained above after consultation with two groups of statisticians we were forced to conclude that the data are underpowered and could not apply some of the methods suggested. Especially in light of our simplified analysis, we think it is better to remove any claims of the relative success of the sparing in different regions to explain more or less variability. Instead we can simply report that sparing in some regions, but not others, is significantly different between “low-performing” and “high-performing” groups.

This is quite a bold statement, especially for an opening paragraph. It makes the reader stop and think, potentially reflecting on their own life. It also allows us to connect with the narrator as they think about the terror they may have experienced in their own lives.

Author Response

Reviewer #1 (Public Review):

Using Tet-off system, Kir2.1 was expressed (or not) during the key time of callosal development from E15 to P15. Restoring activity either by adding Dox during a critical period from P6 to P15 or using DREADDs from P10-14 could rescue the callosal projection to the cortex, whereas later restoration of activity (with Dox) was not successful. Did this successful rescue lead to normal activity? Calcium imaging in animals with Kir2.1 had low levels of any kind of activity, both highly correlated and low correlation, but P6-13 dox treatment partially restored only low-correlation activity and not high correlation activity at P13. The effects of DREADDs on activity was not similarly measured though it was effective for at least partially restoring the callosal projection.

Overall this study builds on earlier findings regarding the importance of neuronal activity in the formation of a normal callosal projection, using in utero electroporation which is particularly well suited for this subject. It makes the case very compellingly that near-normal callosal connectivity can be produced if activity is permitted during a critical period window from P6 or P10 to P15, though the exact timing of this window is imprecise because the elimination of Kir expression was not systematically quantified. For transmembrane proteins like channels it can often take many days for protein expression to completely abate.

We thank the reviewer for their positive evaluation and the constructive comments. Based on the comment on Kir expression, we conducted new experiments using pTRE-Tight2Kir2.1EGFP, with which EGFP signals reflect localization of over-expressed Kir2.1, and examined when the expression of Kir2.1EGFP went down after Dox treatment at P6. At P6 (before Dox treatment), the signals of Kir2.1EGFP (stained with anti-GFP antibody) were observed in the periphery of the soma and along dendrites, implying that Kir2.1EGFP was transported to the cellular membrane. At P10 and P15 (4 days and 9 days after Dox treatment), Kir2.1EGFP signals were not observed in the periphery of the soma and along dendrites. We noted that low-level green signals were observed in the central part of the cell body. These may stem from low-level expression of Kir2.1EGFP in nuclei or cytosol even after Dox treatment. Alternatively, and more likely, these may reflect bleed-through of RFP signals into GFP channel. Overall, we confirmed that Kir2.1 proteins that were localized to the cellular membrane were largely down-regulated. We described these observations in detail in the figure legend of Figure 1-figure supplement 3, and added the result as Figure 1-figure supplement 3.

I found the quantification of the callosal projection to be rather minimal and the normalization approach not entirely transparent. For example does activity from P10-15 restore the full normal PATTERN of callosal connectivity or merely the density of input overall?

We thank the reviewer for this comment. Based on the comment, we added analyses of the pattern of callosal projections; the width of callosal axon innervation zone in layers 2/3 and 5, and densitometric line scans across all cortical layers. Our original quantification showed that the density of callosal axons reaching their target layer (i.e. cortical layer 2/3) is almost recovered in P6-P15 DOX condition (Fig1B-D), but new analyses suggest some aspects of callosal axon projections (the width of the innervation zone in layer 2/3 and 5 (Figure 1-figure supplement 4A,B), and lamina specific innervation pattern (Figure 1-figure supplement 4C)) might be only partially recovered. We have added these new results as Figure 1-figure supplement 4. In future study, we would like to assess the effect of the manipulations at finer resolution by 3D morphological reconstruction of axons of individual neurons.

Also in the discussion it would be nice to more clearly establish whether activity is thought to be maintaining a projection already formed by P10 or permitting the emergence of such a pattern.

Thank you for the suggestion. We have added thorough discussions about this point as follows. Page 7, lines 198-208:

“In the previous study, we showed that callosal axons could reach the innervation area almost normally under activity-reduction, and that the effects of activity-reduction became apparent afterwards (Mizuno et al., 2007). Callosal axons elaborate their branches extensively in P10P15 (Mizuno et al., 2010), and axon branching is regulated by neuronal activity (Matsumoto and Yamamoto, 2016). It is likely that activity is required for the processes of formation, rather than the maintenance of the connections already formed by P10, but the current study employed massive labeling of callosal axons which is not suited to clarify this. In addition, the restoration of activity in the Tet-off (Figure 1) or DREADD (Figure 2) experiment may not completely rescue the ramification pattern of individual axons. Single axon tracing experiments (Mizuno et al., 2010; Dhande et al., 2011) would be required to clarify this. Nonetheless, our findings suggest that callosal axons retain the ability, or are permitted, to grow and make region- and lamina-specific projections in the cortex during a limited period of postnatal cortical development under an activity-dependent mechanism.”

The calcium imaging is a valuable validation of the Kir expression approach, but it the study here appears to overinterpret what may simply be an intermediate level of activity restoration rather than a specific restoration of L events, as it seems that L events would be the most likely to occur under conditions of reduced overall activity. One possibility is that the absence of H events at P13 in the calcium is due to residual Kir expression creating a drag on high level network activation rather than any more complicated change in patterned spontaneous activity/connectivity. The conclusions from this study regarding the permissive role of activity during a critical window and the lack of a requirement for highly correlated activity are valuable, even if somewhat imprecise on both counts. The authors should probably refrain from use of the term patterned activity given that this was measured but not systematically compared to unpatterned spontaneous activity.

We thank the reviewer for this constructive comment. Based on this comment, we removed the term “patterned activity” throughout the manuscript and revised the title, abstract, introduction, results, and discussion extensively. For example, in the Discussion, we revised as follows.

“We have shown that the projections could be established even without fully restoring highly synchronous activity (Figure 4). L events, but not H events, were present in P13 cortex after Dox treatment at P6. L events may be sufficient for the formation of callosal projections. Alternatively, any form of activity with certain level(s) (i.e., “sufficiently” high activity with no specific pattern) could be permissive for the formation of callosal connections.”

Reviewer #2 (Public Review):

Tezuka et al. use in vivo manipulations of spontaneous activity to identify the activitydependent mechanisms of callosal projection development. Previous research of the authors' and other labs had shown that overexpressing the potassium channel Kir2.1, which reduces activity levels in the developing cortical network, blocks the formation of callosal connections almost entirely.

The current manuscript corroborates and extends these previous discoveries by:

1) Demonstrating that the effect of Kir overexpression can be rescued by pharmacogenetic network activation using DREADDs.<br /> 2) Revealing the requirement of network activity for the development of callosal projections during a particular developmental time window and by<br /> 3) Directly relating perturbed callosal development to the actual changes in activity patterns caused by the experimental manipulations.

Thus, this paper is important for our understanding of the role of neuronal activity in the development of long-range connections in the brain. In addition it provides strong evidence for a role of specific activity patterns in this process.

In general, the approach is very straightforward and the results clearly interpreted. Nevertheless, there are a few points to consider.

We thank the reviewer for these positive and supportive comments.

1) It is not clear in which cortical area(s) the in vivo 2-photon recordings were performed and in how far cortical areas that actually receive/send callosal projections were included or not in the analysis.

In response to this comment, we revised the text in the method section as follows.

“We aimed to record spontaneous neuronal activity in putative binocular zones in V1 (2.5 mm lateral of midline and 1 mm anterior of the posterior suture). Since the boundaries between V1 and higher visual areas, AL/LM are not as obvious as those in adult, our recordings likely contained juxtaposed lateral monocular V1 and AL/LM as well.”

Based on our colleaguesʼ unpublished observations, V1 and AL/LM can be distinguished solely by spontaneous activity patterns even before eye-opening. They also found frequencies of spontaneous activity are similar across mono/binocular regions of V1 and AL/LM (Murakami, Ohki, et al. unpublished). Thus, our results should hold even with the variability in recording sites.

2) It is not discussed what the duration of the CNO effect is. Do daily injections rescue activity patterns for 24 hours or a significant proportion of this period?

In response to this critical comment, we revised the text in the method section as follows.

“A previous study showed that an intraperitoneally injected CNO was effective (in terms of increasing activity) for about 9hrs (Alexander et al., 2009). The “partial rescue” effect we observed (Figure 2) may suggest that activity was not fully restored during 24hrs by our daily CNO injections.”

Reviewer #3 (Public Review):

The manuscript by Tezuka adds to an emerging story about the role of activity in the formation of callosal connections across the brain. Here, the authors show that they can use a TET system to switch off the activity of an exogenous potassium channel, in order to probe when activity might be necessary or sufficient for the formation of callosal connections. The authors find that artificial restoration of activity with DREADS is sufficient to rescue the formation of callosal connections, and that there is a critical period (somewhere between P5-P15) where activity must occur in order for the connections to form within the cortex. Finally, the authors show that when the potassium channel is removed during the critical period, the cortex exhibits activity, but few highly synchronous events. These results indicate that it is activity in general and not specifically highly synchronous activity that is necessary for the final innervation of the callosal cortex.

In general, the study is well done, and the writeup is polished, well summarized. The figures are solid. There are only a few criticisms/suggestions.

We thank the reviewer for the positive evaluation.

Major issue: Have the authors demonstrated a requirement for "patterned spontaneous activity"?

The authors claim variously in the abstract ("a distinct pattern of spontaneous activity") and in the results (pg 6, "our observations indicate that patterned spontaneous activity") and discussion (pg 6, "we demonstrated that patterned spontaneous activity") that it is "patterned" spontaneous activity that is key for the formation of callosal connections. However, when I was reading the paper, I came to the opposite conclusion: that any sufficiently high spontaneous activity is sufficient for the formation of these connections.

The authors showed that relieving the KIR expression from P5-15 allows the connections to form; however, in Figure 4, the authors show that the nature of the activity produced in the cortex (in terms of mixtures of H and L events) is very different. Nevertheless, the connections can form. Further, the authors showed that increasing activity when KIR is expressed using DREADS restores the connections. The pattern of activity produced by this DREADS + KIR expression is likely to be very different from the pattern of activity of a typically-developing animal. In total, I thought that the authors demonstrated, quite nicely, that it is just the presence of sufficient activity that is key to the innervation of the contralateral cortex. (It's not cell autonomous, as the authors showed before; there seems to be a "sufficient activity" requirement).

Therefore, I think the authors should remove references to the requirement of patterned activity and instead say something about sufficiently high activity (or some characterization that the authors choose). I think they've shown quite nicely that a specific pattern of the spontaneous activity is not important.

We thank the reviewer for this very important insight and interpretation. After considering all the currently presented data again, we have come to agree with the interpretation stated by the reviewer. We removed the term “patterned activity” throughout the manuscript and revised the title, abstract, introduction, results, and discussion extensively. Nevertheless, we would not completely discard the possibility that specific patterns of spontaneous activity, such as L-events, could potentially have some active contribution to the development of projection circuits, and would like to further address this in future study.

For example, in the Discussion, we revised the text as follows.

“We have shown that the projections could be established even without fully restoring highly synchronous activity (Figure 4). L events, but not H events, were present in P13 cortex after Dox treatment at P6. L events may be sufficient for the formation of callosal projections. Alternatively, any form of activity with certain level(s) (i.e., “sufficiently” high activity with no specific pattern) could be permissive for the formation of callosal connections.”

Author Response

Reviewer #1 (Public Review):

In computational modeling studies of behavioral data using reinforcement learning models, it has been implicitly assumed that parameter estimates generalize across tasks (generalizability) and that each parameter reflects a single cognitive function (interpretability). In this study, the authors examined the validity of these assumptions through a detailed analysis of experimental data across multiple tasks and age groups. The results showed that some parameters generalize across tasks, while others do not, and that interpretability is not sufficient for some parameters, suggesting that the interpretation of parameters needs to take into account the context of the task. Some researchers may have doubted the validity of these assumptions, but to my knowledge, no study has explicitly examined their validity. Therefore, I believe this research will make an important contribution to researchers who use computational modeling. In order to clarify the significance of this research, I would like the authors to consider the following points.

1) Effects of model misspecification

In general, model parameter estimates are influenced by model misspecification. Specifically, if components of the true process are not included in the model, the estimates of other parameters may be biased. The authors mentioned a little about model misspecification in the Discussion section, but they do not mention the possibility that the results of this study itself may be affected by it. I think this point should be discussed carefully.

The authors stated that they used state-of-the-art RL models, but this does not necessarily mean that the models are correctly specified. For example, it is known that if there is history dependence in the choice itself and it is not modeled properly, the learning rates depending on valence of outcomes (alpha+, alpha-) are subject to biases (Katahira, 2018, J Math Pscyhol). In the authors' study, the effect of one previous choice was included in the model as choice persistence, p. However, it has been pointed out that not including the effect of a choice made more than two trials ago in the model can also cause bias (Katahira, 2018). The authors showed taht the learning rate for positive RPE, alpha+ was inconsistent across tasks. But since choice persistence was included only in Task B, it is possible that the bias of alpha+ was different between tasks due to individual differences in choice persistence, and thus did not generalize.

However, I do not believe that it is necessary to perform a new analysis using the model described above. As for extending the model, I don't think it is possible to include all combinations of possible components. As is often said, every model is wrong, and only to varying degrees. What I would like to encourage the authors to do is to discuss such issues and then consider their position on the use of the present model. Even if the estimation results of this model are affected by misspecification, it is a fact that such a model is used in practice, and I think it is worthwhile to discuss the nature of the parameter estimates.

We thank the reviewer for this thoughtful question, and have added the following paragraph to the discussion section that is aims to address it:

“Another concern relates to potential model misspecification and its effects on model parameter estimates: If components of the true data-generating process are not included in a model (i.e., a model is misspecified), estimates of existing model parameters may be biased. For example, if choices have an outcome-independent history dependence that is not modeled properly, learning rate parameters have shown to be biased [63]. Indeed, we found that learning rate parameters were inconsistent across the tasks in our study, and two of our models (A and C) did not model history dependence in choice, while the third (model B) only included the effect of one previous choice (persistence parameter), but no multi-trial dependencies. It is hence possible that the differences in learning rate parameters between tasks were caused by differences in the bias induced by misspecification of history dependence, rather than a lack of generalization. Though pressing, however, this issue is difficult to resolve in practicality, because it is impossible to include all combinations of possible parameters in all computational models, i.e., to exhaustively search the space of possible models ("Every model is wrong, but to varying degrees"). Furthermore, even though our models were likely affected by some degree of misspecification, the research community is currently using models of this kind. Our study therefore sheds light on generalizability and interpretability in a realistic setting, which likely includes models with varying degrees of misspecification. Lastly, our models were fitted using robust computational tools and achieved good behavioral recovery (Fig. D.7), which also reduces the likelihood of model misspecification.“

2) Issue of reliability of parameter estimates

I think it is important to consider not only the bias in the parameter estimates, but also the issue of reliability, i.e., how stable the estimates will be when the same task is repeated with the same individual. For the task used in this study, has test-retest reliability been examined in previous studies? I think that parameters with low reliability will inevitably have low generalizability to other tasks. In this study, the use of three tasks seems to have addressed this issue without explicitly considering the reliability, but I would like the author to discuss this issue explicitly.

We thank the reviewer for this useful comment, and have added the following paragraph to the discussion section to address it:

“Furthermore, parameter generalizability is naturally bounded by parameter reliability, i.e., the stability of parameter estimates when participants perform the same task twice (test-retest reliability) or when estimating parameters from different subsets of the same dataset (split-half reliability). The reliability of RL models has recently become the focus of several parallel investigations [...], some employing very similar tasks to ours [...]. The investigations collectively suggest that excellent reliability can often be achieved with the right methods, most notably by using hierarchical model fitting. Reliability might still differ between tasks or models, potentially being lower for learning rates than other RL parameters [...], and differing between tasks (e.g., compare [...] to [...]). In this study, we used hierarchical fitting for tasks A and B and assessed a range of qualitative and quantitative measures of model fit for each task [...], boosting our confidence in high reliability of our parameter estimates, and the conclusion that the lack of between-task parameter correlations was not due to a lack of parameter reliability, but a lack of generalizability. This conclusion is further supported by the fact that larger between-task parameter correlations (r>0.5) than those observed in humans were attainable---using the same methods---in a simulated dataset with perfect generalization.“

3) About PCA

In this paper, principal component analysis (PCA) is used to extract common components from the parameter estimates and behavioral features across tasks. When performing PCA, were each parameter estimate and behavioral feature standardized so that the variance would be 1? There was no mention about this. It seems that otherwise the principal components would be loaded toward the features with larger variance. In addition, Moutoussis et al. (Neuron, 2021, 109 (12), 2025-2040) conducted a similar analysis of behavioral parameters of various decision-making tasks, but they used factor analysis instead of PCA. Although the authors briefly mentioned factor analysis, it would be better if they also mentioned the reason why they used PCA instead of factor analysis, which can consider unique variances.

To answer the reviewer's first question: We indeed standardized all features before performing the PCA. Apologies for missing to include this information - we have now added a corresponding sentence to the methods sections.

We also thank the reviewer for the mentioned reference, which is very relevant to our findings and can help explain the roles of different PCs. Like in our study, Moutoussis et al. found a first PC that captured variability in task performance, and subsequent PCs that captured task contrasts. We added the following paragraph to our manuscript:

“PC1 therefore captured a range of "good", task-engaged behaviors, likely related to the construct of "decision acuity" [...]. Like our PC1, decision acuity was the first component of a factor analysis (variant of PCA) conducted on 32 decision-making measures on 830 young people, and separated good and bad performance indices. Decision acuity reflects generic decision-making ability, and predicted mental health factors, was reflected in resting-state functional connectivity, but was distinct from IQ [...].”

To answer the reviewer's question about PCA versus FA, both approaches are relatively similar conceptually, and oftentimes share the majority of the analysis pipeline in practice. The main difference is that PCA breaks up the existing variance in a dataset in a new way (based on PCs rather than the original data features), whereas FA aims to identify an underlying model of latent factors that explain the observable features. This means that PCs are linear combinations of the original data features, whereas Factors are latent factors that give rise to the observable features of the dataset with some noise, i.e., including an additional error term.

However, in practice, both methods share the majority of computation in the way they are implemented in most standard statistical packages: FA is usually performed by conducting a PCA and then rotating the resulting solution, most commonly using the Varimax rotation, which maximizes the variance between features loadings on each factor in order to make the result more interpretable, and thereby foregoing the optimal solution that has been achieved by the PCA (which lack the error term). Maximum variance in feature loadings means that as many features as possible will have loadings close to 0 and 1 on each factor, reducing the number of features that need to be taken into account when interpreting this factor. Most relevant in our situation is that PCA is usually a special case of FA, with the only difference that the solution is not rotated for maximum interpretability. (Note that this rotation can be minor if feature loadings already show large variance in the PCA solution.)

To determine how much our results would change in practice if we used FA instead of PCA, we repeated the analysis using FA. Both are shown side-by-side below, and the results are quite similar:

We therefore conclude that our specific results are robust to the choice of method used, and that there is reason to believe that our PC1 is related to Moutoussis et al.’s F1 despite the differences in method.

Reviewer #2 (Public Review):

I am enthusiastic about the comprehensive approach, the thorough analysis, and the intriguing findings. This work makes a timely contribution to the field and warrants a wider discussion in the community about how computational methods are deployed and interpreted. The paper is also a great and rare example of how much can be learned from going beyond a meta-analytic approach to systematically collect data that assess commonly held assumptions in the field, in this case in a large data-driven study across multiple tasks. My only criticism is that at times, the paper misses opportunities to be more constructive in pinning down exactly why authors observe inconsistencies in parameter fits and interpretation. And the somewhat pessimistic outlook relies on some results that are, in my view at least, somewhat expected based on what we know about human RL. Below I summarize the major ways in which the paper's conclusions could be strengthened.

One key point the authors make concerns the generalizability of absolute vs. relative parameter values. It seems that at least in the parameter space defined by +LRs and exploration/noise (which are known to be mathematically coupled), subjects clustered similarly for tasks A and C. In other words, as the authors state, "both learning rate and inverse temperature generalized in terms of the relationships they captured between participants". This struck me as a more positive and important result than it was made out to be in the paper, for several reasons:

• As authors point out in the discussion, a large literature on variable LRs has shown that people adapt their learning rates trial-by-trial to the reward function of the environment; given this, and given that all models tested in this work have fixed learning rates, while the three tasks vary on the reward function, the comparison of absolute values seems a bit like a red-herring.

We thank the reviewers for this recommendation and have reworked the paper substantially to address the issue. We have modified the highlights, abstract, introduction, discussion, conclusion, and relevant parts of the results section to provide equal weight to the successes and failures of generalization.

Highlights:

● “RL decision noise/exploration parameters generalize in terms of between-participant variation, showing similar age trajectories across tasks.”

● “These findings are in accordance with previous claims about the developmental trajectory of decision noise/exploration parameters.”

Abstract:

● “We found that some parameters (exploration / decision noise) showed significant generalization: they followed similar developmental trajectories, and were reciprocally predictive between tasks.“

The introduction now introduces different potential outcomes of our study with more equal weight:

“Computational modeling enables researchers to condense rich behavioral datasets into simple, falsifiable models (e.g., RL) and fitted model parameters (e.g., learning rate, decision temperature) [...]. These models and parameters are often interpreted as a reflection of ("window into") cognitive and/or neural processes, with the ability to dissect these processes into specific, unique components, and to measure participants' inherent characteristics along these components.

For example, RL models have been praised for their ability to separate the decision making process into value updating and choice selection stages, allowing for the separate investigation of each dimension. Crucially, many current research practices are firmly based on these (often implicit) assumptions, which give rise to the expectation that parameters have a task- and model-independent interpretation and will seamlessly generalize between studies. However, there is growing---though indirect---evidence that these assumptions might not (or not always) be valid.

The following section lays out existing evidence in favor and in opposition of model generalizability and interpretability. Building on our previous opinion piece, which---based on a review of published studies---argued that there is less evidence for model generalizability and interpretability than expected based on current research practices [...], this study seeks to directly address the matter empirically.”

We now also provide more even evidence for both potential outcomes:

“Many current research practices are implicitly based on the interpretability and generalizability of computational model parameters (despite the fact that many researchers explicitly distance themselves from these assumptions). For our purposes, we define a model variable (e.g., fitted parameter, reward-prediction error) as generalizable if it is consistent across uses, such that a person would be characterized with the same values independent of the specific model or task used to estimate the variable. Generalizability is a consequence of the assumption that parameters are intrinsic to participants rather than task dependent (e.g., a high learning rate is a personal characteristic that might reflect an individual's unique brain structure). One example of our implicit assumptions about generalizability is the fact that we often directly compare model parameters between studies---e.g., comparing our findings related to learning-rate parameters to a previous study's findings related to learning-rate parameters. Note that such a comparison is only valid if parameters capture the same underlying constructs across studies, tasks, and model variations, i.e., if parameters generalize. The literature has implicitly equated parameters in this way in review articles [...], meta-analyses [...], and also most empirical papers, by relating parameter-specific findings across studies. We also implicitly evoke parameter generalizability when we study task-independent empirical parameter priors [...], or task-independent parameter relationships (e.g., interplay between different kinds of learning rates [...]), because we presuppose that parameter settings are inherent to participants, rather than task specific.

We define a model variable as interpretable if it isolates specific and unique cognitive elements, and/or is implemented in separable and unique neural substrates. Interpretability follows from the assumption that the decomposition of behavior into model parameters "carves cognition at its joints", and provides fundamental, meaningful, and factual components (e.g., separating value updating from decision making). We implicitly invoke interpretability when we tie model variables to neural substrates in a task-general way (e.g., reward prediction errors to dopamine function [...]), or when we use parameters as markers of psychiatric conditions (e.g., working-memory parameter and schizophrenia [...]). Interpretability is also required when we relate abstract parameters to aspects of real-world decision making [...], and generally, when we assume that model variables are particularly "theoretically meaningful" [...].

However, in midst the growing recognition of computational modeling, the focus has also shifted toward inconsistencies and apparent contradictions in the emerging literature, which are becoming apparent in cognitive [...], developmental [...], clinical [...], and neuroscience studies [...], and have recently become the focus of targeted investigations [...]. For example, some developmental studies have shown that learning rates increased with age [...], whereas others have shown that they decrease [...]. Yet others have reported U-shaped trajectories with either peaks [...] or troughs [...] during adolescence, or stability within this age range [...] (for a comprehensive review, see [...]; for specific examples, see [...]). This is just one striking example of inconsistencies in the cognitive modeling literature, and many more exist [...]. These inconsistencies could signify that computational modeling is fundamentally flawed or inappropriate to answer our research questions. Alternatively, inconsistencies could signify that the method is valid, but our current implementations are inappropriate [...]. However, we hypothesize that inconsistencies can also arise for a third reason: Even if both method and implementation are appropriate, inconsistencies like the ones above are expected---and not a sign of failure---if implicit assumptions of generalizability and interpretability are not always valid. For example, model parameters might be more context-dependent and less person-specific that we often appreciate [...]“

In the results section, we now highlight findings more that are compatible with generalization: “For α+, adding task as a predictor did not improve model fit, suggesting that α+ showed similar age trajectories across tasks (Table 2). Indeed, α+ showed a linear increase that tapered off with age in all tasks (linear increase: task A: β = 0.33, p < 0.001; task B: β = 0.052, p < 0.001; task C: β = 0.28, p < 0.001; quadratic modulation: task A: β = −0.007, p < 0.001; task B: β = −0.001, p < 0.001; task C: β = −0.006, p < 0.001). For noise/exploration and Forgetting parameters, adding task as a predictor also did not improve model fit (Table 2), suggesting similar age trajectories across tasks.”

“For both α+ and noise/exploration parameters, task A predicted tasks B and C, and tasks B and C predicted task A, but tasks B and C did not predict each other (Table 4; Fig. 2D), reminiscent of the correlation results that suggested successful generalization (section 2.1.2).”

“Noise/exploration and α+ showed similar age trajectories (Fig. 2C) in tasks that were sufficiently similar (Fig. 2D).” And with respect to our simulation analysis (for details, see next section):

“These results show that our method reliably detected parameter generalization in a dataset that exhibited generalization. ”

We also now provide more nuance in our discussion of the findings:

“Both generalizability [...] and interpretability (i.e., the inherent "meaningfulness" of parameters) [...] have been explicitly stated as advantages of computational modeling, and many implicit research practices (e.g., comparing parameter-specific findings between studies) showcase our conviction in them [...]. However, RL model generalizability and interpretability has so far eluded investigation, and growing inconsistencies in the literature potentially cast doubt on these assumptions. It is hence unclear whether, to what degree, and under which circumstances we should assume generalizability and interpretability. Our developmental, within-participant study revealed a nuanced picture: Generalizability and interpretability differed from each other, between parameters, and between tasks.”

“Exploration/noise parameters showed considerable generalizability in the form of correlated variance and age trajectories. Furthermore, the decline in exploration/noise we observed between ages 8-17 was consistent with previous studies [13, 66, 67], revealing consistency across tasks, models, and research groups that supports the generalizability of exploration / noise parameters. However, for 2/3 pairs of tasks, the degree of generalization was significantly below the level of generalization expected for perfect generalization. Interpretability of exploration / noise parameters was mixed: Despite evidence for specificity in some cases (overlap in parameter variance between tasks), it was missing in others (lack of overlap), and crucially, parameters lacked distinctiveness (substantial overlap in variance with other parameters).”

“Taken together, our study confirms the patterns of generalizable exploration/noise parameters and task-specific learning rate parameters that are emerging from the literature [13].”

• Regarding the relative inferred values, it's unclear how high we really expect correlations between the same parameter across tasks to be. E.g., if we take Task A and make a second, hypothetical, Task B by varying one feature at a time (say, stochasticity in reward function), how correlated are the fitted LRs going to be? Given the different sources of noise in the generative model of each task and in participant behavior, it is hard to know whether a correlation coefficient of 0.2 is "good enough" generalizability.

We thank the reviewer for this excellent suggestion, which we think helped answer a central question that our previous analyses had failed to address, and also provided answers to several other concerns raised by both reviewers in other section. We have conducted these additional analyses as suggested, simulating artificial behavioral data for each task, fitting these data using the models used in humans, repeating the analyses performed on humans on the new fitted parameters, and using bootstrapping to statistically compare humans to the hence obtained ceiling of generalization. We have added the following section to our paper, which describes the results in detail:

“Our analyses so far suggest that some parameters did not generalize between tasks, given differences in age trajectories (section 2.1.3) and a lack of mutual prediction (section 2.1.4). However, the lack of correspondence could also arise due to other factors, including behavioral noise, noise in parameter fitting, and parameter trade-offs within tasks. To rule these out, we next established the ceiling of generalizability attainable using our method.

We established the ceiling in the following way: We first created a dataset with perfect generalizability, simulating behavior from agents that use the same parameters across all tasks (suppl. Appendix E). We then fitted this dataset in the same way as the human dataset (e.g., using the same models), and performed the same analyses on the fitted parameters, including an assessment of age trajectories (suppl. Table E.8) and prediction between tasks (suppl. Tables E.9, E.10, and E.11). These results provide the practical ceiling of generalizability. We then compared the human results to this ceiling to ensure that the apparent lack of generalization was valid (significant difference between humans and ceiling), and not in accordance with generalization (lack of difference between humans and ceiling).

Whereas humans had shown divergent trajectories for parameter alpha- (Fig. 2B; Table 1), the simulated agents did not show task differences for alpha- or any other parameter (suppl. Fig E.8B; suppl. Table E.8, even when controlling for age (suppl. Tables E.9 and E.10), as expected from a dataset of generalizing agents. Furthermore, the same parameters were predictive between tasks in all cases (suppl. Table E.11). These results show that our method reliably detected parameter generalization in a dataset that exhibited generalization.

Lastly, we established whether the degree of generalization in humans was significantly different from agents. To this aim, we calculated the Spearman correlations between each pair of tasks for each parameter, for both humans (section 2.1.2; suppl. Fig. H.9) and agents, and compared both using bootstrapped confidence intervals (suppl. Appendix E). Human parameter correlations were significantly below the ceiling for all parameters except alpha+ (A vs B) and epsilon / 1/beta (A vs C; suppl. Fig. E.8C). This suggests that humans were within the range of maximally detectable generalization in two cases, but showed less-than-perfect generalization between other task combinations and for parameters Forgetting and alpha-.”

• The +LR/inverse temp relationship seems to generalize best between tasks A/C, but not B/C, a common theme in the paper. This does not seem surprising given that in A and C there is a key additional task feature over the bandit task in B -- which is the need to retain state-action associations. Whether captured via F (forgetting) or K (WM capacity), the cognitive processes involved in this learning might interact with LR/exploration in a different way than in a task where this may not be necessary.

We thank the reviewer for this comment, which raises an important issue. We are adding the specific pairwise correlations and scatter plots for the pairs of parameters the reviewer asked about below (“bf_alpha” = LR task A; “bf_forget” = F task A; “rl_forget” = F task C; “rl_log_alpha” = LR task C; “rl_K” = WM capacity task C):

Within tasks:

Between tasks:

To answer the question in more detail, we have expanded our section about limitations stemming from parameter tradeoffs in the following way:

“One limitation of our results is that regression analyses might be contaminated by parameter cross-correlations (sections 2.1.2, 2.1.3, 2.1.4), which would reflect modeling limitations (non-orthogonal parameters), and not necessarily shared cognitive processes. For example, parameters alpha and beta are mathematically related in the regular RL modeling framework, and we observed significant within-task correlations between these parameters for two of our three tasks (suppl. Fig. H.10, H.11). This indicates that caution is required when interpreting correlation results. However, correlations were also present between tasks (suppl. Fig. H.9, H.11), suggesting that within-model trade-offs were not the only explanation for shared variance, and that shared cognitive processes likely also played a role.

Another issue might arise if such parameter cross-correlations differ between models, due to the differences in model parameterizations across tasks. For example, memory-related parameters (e.g., F, K in models A and C) might interact with learning- and choice-related parameters (e.g., alpha+, alpha-, noise/exploration), but such an interaction is missing in models that do not contain memory-related parameters (e.g., task B). If this indeed the case, i.e., parameters trade off with each other in different ways across tasks, then a lack of correlation between tasks might not reflect a lack of generalization, but just the differences in model parameterizations. Suppl. Fig. \ref{figure:S2AlphaBetaCorrelations} indeed shows significant, medium-sized, positive and negative correlations between several pairs of Forgetting, memory-related, learning-related, and exploration parameters (though with relatively small effect sizes; Spearman correlation: 0.17 < |r| < 0.22).

The existence of these correlations (and differences in correlations between tasks) suggest that memory parameters likely traded off with each other, as well as with other parameters, which potentially affected generalizability across tasks. However, some of the observed correlations might be due to shared causes, such as a common reliance on age, and the regression analyses in the main paper control for these additional sources of variance, and might provide a cleaner picture of how much variance is actually shared between parameters.

Furthermore, correlations between parameters within models are frequent in the existing literature, and do not prevent researchers from interpreting parameters---in this sense, the existence of similar correlations in our study allows us to address the question of generalizability and interpretability in similar circumstances as in the existing literature.”

• More generally, isn't relative generalizability the best we would expect given systematic variation in task context? I agree with the authors' point that the language used in the literature sometimes implies an assumption of absolute generalizability (e.g. same LR across any task). But parameter fits, interactions, and group differences are usually interpreted in light of a single task+model paradigm, precisely b/c tasks vary widely across critical features that will dictate whether different algorithms are optimal or not and whether cognitive functions such as WM or attention may compensate for ways in which humans are not optimal. Maybe a more constructive approach would be to decompose tasks along theoretically meaningful features of the underlying Markov Decision Process (which gives a generative model), and be precise about (1) which features we expect will engage additional cognitive mechanisms, and (2) how these mechanisms are reflected in model parameters.

We thank the reviewer for this comment, and will address both points in turn:

(1) We agree with the reviewer's sentiment about relative generalizability: If we all interpreted our models exclusively with respect to our specific task design, and never expected our results to generalize to other tasks or models, there would not be a problem. However, the current literature shows a different pattern: Literature reviews, meta-analyses, and discussion sections of empirical papers regularly compare specific findings between studies. We compare specific parameter values (e.g., empirical parameter priors), parameter trajectories over age, relationships between different parameters (e.g., balance between LR+ and LR-), associations between parameters and clinical symptoms, and between model variables and neural measures on a regular basis. The goal of this paper was really to see if and to what degree this practice is warranted. And the reviewer rightfully alerted us to the fact that our data imply that these assumptions might be valid in some cases, just not in others.

(2) With regard to providing task descriptions that relate to the MDP framework, we have included the following sentence in the discussion section:

“Our results show that discrepancies are expected even with a consistent methodological pipeline, and using up-to-date modeling techniques, because they are an expected consequence of variations in experimental tasks and computational models (together called "context"). Future research needs to investigate these context factors in more detail. For example, which task characteristics determine which parameters will generalize and which will not, and to what extent? Does context impact whether parameters capture overlapping versus distinct variance? A large-scale study could answer these questions by systematically covering the space of possible tasks, and reporting the relationships between parameter generalizability and distance between tasks. To determine the distance between tasks, the MDP framework might be especially useful because it decomposes tasks along theoretically meaningful features of the underlying Markov Decision Process.“

Another point that merits more attention is that the paper pretty clearly commits to each model as being the best possible model for its respective task. This is a necessary premise, as otherwise, it wouldn't be possible to say with certainty that individual parameters are well estimated. I would find the paper more convincing if the authors include additional information and analysis showing that this is actually the case.

We agree with the sentiment that all models should fit their respective task equally well. However, there is no good quantitative measure of model fit that is comparable across tasks and models - for example, because of the difference in difficulty between the tasks, the number of choices explained would not be a valid measure to compare how well the models are doing across tasks. To address this issue, we have added the new supplemental section (Appendix C) mentioned above that includes information about the set of models compared, and explains why we have reason to believe that all models fit (equally) well. We also created the new supplemental Figure D.7 shown above, which directly compares human and simulated model behavior in each task, and shows a close correspondence for all tasks. Because the quality of all our models was a major concern for us in this research, we also refer the reviewer and other readers to the three original publications that describe all our modeling efforts in much more detail, and hopefully convince the reviewer that our model fitting was performed according to high standards.

I am particularly interested to see whether some of the discrepancies in parameter fits can be explained by the fact that the model for Task A did not account for explicit WM processes, even though (1) Task A is similar to Task C (Task A can be seen as a single condition of Task C with 4 states and 2 possible visible actions, and stochastic rather than deterministic feedback) and (2) prior work has suggested a role for explicit memory of single episodes even in stateless bandit tasks such as Task B.

We appreciate this very thoughtful question, which raises several important issues. (1) As the reviewer said, the models for task A and task C are relatively different even though the underlying tasks are relatively similar (minus the differences the reviewer already mentioned, in terms of visibility of actions, number of actions, and feedback stochasticity). (2) We also agree that the model for task C did not include episodic memory processes even though episodic memory likely played a role in this task, and agree that neither the forgetting parameters in tasks A and C, nor the noise/exploration parameters in tasks A, B, and C are likely specific enough to capture all the memory / exploration processes participants exhibited in these tasks.

However, this problem is difficult to solve: We cannot fit an episodic-memory model to task B because the task lacks an episodic-memory manipulation (such as, e.g., in Bornstein et al., 2017), and we cannot fit a WM model to task A because it lacks the critical set-size manipulation enabling identification of the WM component (modifying set size allows the model to identify individual participants’ WM capacities, so the issue cannot be avoided in tasks with only one set size). Similarly, we cannot model more specific forgetting or exploration processes in our tasks because they were not designed to dissociate these processes. If we tried fitting more complex models that include these processes to these tasks, they would most likely lose in model comparison because the increased complexity would not lead to additional explained behavioral variance, given that the tasks do not elicit the relevant behavioral patterns. Because the models therefore do not specify all the cognitive processes that participants likely employ, the situation described by the reviewer arises, namely that different parameters sometimes capture the same cognitive processes across tasks and models, while the same parameters sometimes capture different processes.

And while the reviewer focussed largely on memory-related processes, the issue of course extends much further: Besides WM, episodic memory, and more specific aspects of forgetting and exploration, our models also did not take into account a range of other processes that participants likely engaged in when performing the tasks, including attention (selectivity, lapses), reasoning / inference, mental models (creation and use), prediction / planning, hypothesis testing, etc., etc. In full agreement with the reviewer’s sentiment, we recently argued that this situation is ubiquitous to computational modeling, and should be considered very carefully by all modelers because it can have a large impact on model interpretation (Eckstein et al., 2021).

If we assume that many more cognitive processes are likely engaged in each task than are modeled, and consider that every computational model includes just a small number of free parameters, parameters then necessarily reflect a multitude of cognitive processes. The situation is additionally exacerbated by the fact that more complex models become increasingly difficult to fit from a methodological perspective, and that current laboratory tasks are designed in a highly controlled and consequently relatively simplistic way that does not lend itself to simultaneously test a variety of cognitive processes.

The best way to deal with this situation, we think, is to recognize that in different contexts (e.g., different tasks, different computational models, different subject populations), the same parameters can capture different behaviors, and different parameters can capture the same behaviors, for the reasons the reviewer lays out. Recognizing this helps to avoid misinterpreting modeling results, for example by focusing our interpretation of model parameters to our specific task and model, rather than aiming to generalize across multiple tasks. We think that recognizing this fact also helps us understand the factors that determine whether parameters will capture the same or different processes across contexts and whether they will generalize. This is why we estimated here whether different parameters generalize to different degrees, which other factors affect generalizability, etc. Knowing the practical consequences of using the kinds of models we currently use will therefore hopefully provide a first step in resolving the issues the reviewer laid out.

It is interesting that one of the parameters that generalizes least is LR-. The authors make a compelling case that this is related to a "lose-stay" behavior that benefits participants in Task B but not in Task C, which makes sense given the probabilistic vs deterministic reward function. I wondered if we can rule out the alternative explanation that in Task C, LR- could reflect a different interpretation of instructions vis. a vis. what rewards indicate - do authors have an instruction check measure in either task that can be correlated with this "lose-stay" behavior and with LR-? And what does the "lose-stay" distribution look like, for Task C at least? I basically wonder if some of these inconsistencies can be explained by participants having diverging interpretations of the deterministic nature of the reward feedback in Task C. The order of tasks might matter here as well -- was task order the same across participants? It could be that due to the within-subject design, some participants may have persisted in global strategies that are optimal in Task B, but sub-optimal in Task C.

The PCA analysis adds an interesting angle and a novel, useful lens through which we can understand divergence in what parameters capture across different tasks. One observation is that loadings for PC2 and PC3 are strikingly consistent for Task C, so it looks more like these PCs encode a pairwise contrast (PC2 is C with B and PC2 is C with A), primarily reflecting variability in performance - e.g. participants who did poorly on Task C but well on Task B (PC2) or Task A (PC3). Is it possible to disentangle this interpretation from the one in the paper? It also is striking that in addition to performance, the PCs recover the difference in terms of LR- on Task B, which again supports the possibility that LR- divergence might be due to how participants handle probabilistic vs. deterministic feedback.

We appreciate this positive evaluation of our PCA and are glad that it could provide a useful lens for understanding parameters. We also agree to the reviewer's observation that PC2 and PC3 reflect task contrasts (PC2: task B vs task C; PC3: task A vs task C), and phrase it in the following way in the paper:

“PC2 contrasted task B to task C (loadings were positive / negative / near-zero for corresponding features of tasks B / C / A; Fig. 3B). PC3 contrasted task A to both B and C (loadings were positive / negative for corresponding features on task A / tasks B and C; Fig. 3C).”

Hence, the only difference between our interpretation and the reviewer’s seems to be whether PC3 contrasts task C to task B as well as task A, or just to task A. Our interpretation is supported by the fact that loadings for tasks A and C are quite similar on PC3; however, both interpretations seem appropriate.

We also appreciate the reviewer's positive evaluation of the fact that the PCA reproduces the differences in LR-, and its relationship to probabilistic/deterministic feedback. The following section reiterates this idea:

“alpha- loaded positively in task C, but negatively in task B, suggesting that performance increased when participants integrated negative feedback faster in task C, but performance decreased when they did the same in task B. As mentioned before, contradictory patterns of alpha- were likely related to task demands: The fact that negative feedback was diagnostic in task C likely favored fast integration of negative feedback, while the fact that negative feedback was not diagnostic in task B likely favored slower integration (Fig. 1E). This interpretation is supported by behavioral findings: "Lose-stay" behavior (repeating choices that produce negative feedback) showed the same contrasting pattern as alpha- on PC1. It loaded positively in task B, showing Lose-stay behavior benefited performance, but it loaded negatively on task C, showing that it hurt performance (Fig. 3A). This supports the claim that lower alpha- was beneficial in task B, while higher alpha- was beneficial in task C, in accordance with participant behavior and developmental differences.“

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Reply to the reviewers

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

The manuscript by Sasaki et al titled "Conditional GWAS of non-CG transposon methylation in Arabidopsis thaliana reveals major polymorphisms in five genes" employed conditional GWAS to identify trans-regulators of mCHG levels in Arabidopsis natural accessions, after controlling for mCHH. Using loss of function mutants for couple of these genes, the authors also tested their effects on mCHG levels.

Overall, this manuscript makes a nice contribution. I suggest the following improvements to enhance the quality of this manuscript.

Comments:

1. MSI1 has been shown to be copurified with TCX5, a component of DREAM Complex. The DREAM complex transcriptional regulates CMT3, MET1, DDM1 in a cell cycle dependent manner (ref: Yong-Qiang Ning, 2020 nature plants). Tcx5/6 double mutants have ectopic gain of TE and genic mCHG. It would be nice to refer this paper and add to the MSI1 part accordingly. Absolutely: thanks for suggesting this!

Multifaceted regulation of mCHG levels seems to be evident from this and previous studies. Why would such complex pathways evolv to regulate mCHG? Bewick et al 2016 and Wendte et al 2019 showed lack of CMT3 or ectopic expression of CMT3 can influence CG gene body methylation (gbM). One possibility is that these five factors regulate CHG to maintain it at a level that is just enough to target TE. Irrespective of the functional relevance of gbM, differences in the levels of these five factors might result in erroneous gbM. It would be interesting to look for the rates of gbM and number of gbM genes in the natural accession carrying 1 to 4 number of mCHG-decreasing alleles. Also, in the one line from Iberian peninsula carrying polymorphisms in all five genes.

Yes, the connection between CHG and gbM is very interesting and deserves more attention. We looked for the effect of cumulative mCHG-decreasing alleles on gbM, but there was no association with gbM — but this is really not expected given the stable epigenetic inheritance of gbM. The Iberian peninsula line carrying all decreasing alleles did slightly lower gbM levels, but it is impossible to exclude the effects of population structure. Since we have nothing to add beyond speculation, we prefer not to go into this topic.

The authors mentioned a significant peak for mCHG|mCHH on RdDM-targeted transposons was located 196 bp downstream of MIR823a and not on mature miRNA. Therefore, this cannot directly impair miR823 base pairing with CMT3 mRNA transcripts and its cleavage. Moreover, natural accessions carrying alternative MIRNA823 allele show reduced CMT3 and mCHG levels, meaning more miR823 levels? Does this 196 downstream region contain any regulatory feature that effects miR823 transcription? Or this region still falls in the primary miRNA hairpin region? A single nucleotide change in pri-miRNA can have a significant impact on its secondary structure that can impede DICER processivity and effectively levels of mature miR823 molecules? It will be beyond the scope of this paper to pin down the exact mechanism. But a simple stem loop RT-PCR for miR823 levels in reference and alternative accessions would be informative (on accessions that grow at the same speed). Perhaps, the authors can at least model SNP induced pri-miRNA secondary structure variations using Vienna RNAFold (http://rna.tbi.univie.ac.at/cgi-bin/RNAWebSuite/RNAfold.cgi) and present MEF values (maximum free energy) for representative accessions.

Stem-loop qRT-PCR for MIR823a expression would indeed be helpful to confirm allelic effects. However, comparing lines with wildly different genetic backgrounds is fraught with difficulty due to trans-effects. Furthermore, MIR823a is expressed specifically during embryogenesis, and the expression quickly decreases after the early heart stage (Papareddy et al., 2021). Thus, we would need to extract microRNA from embryos at exactly the same developmental stage, from lines that may develop at different speeds.. Most likely, time-series data would be required, and generating such data is a massive undertaking. As noted in the paper, we did measure MIR823a expression by stem-loop qRT-PCR for several lines carrying reference and alternative alleles but the results were inconclusive. A proper study of this is beyond the scope of this paper.

Testing predicted effects on RNA secondary structure, on the other hand, is eminently feasible. As suggested, we used Vienna RNAFold for the region, including the GWAS peak. Since the SNP is linked to a 35 bp deletion (shown in S4A), it is closer to the MIR823A coding region than 196 bp. However, the results indicate that the SNP (Chr3:4496626) is not within the stem-loop. It remains possible that this SNP tags multiple SNPs in the annotated stem regions. This is now mentioned.

Figure 1A can be made more reader friendly. Perhaps this can be broken down into correlation plots for individual conditions or tissue types. In addition, it might be good to add individual r-square values for each of them instead of compound r-square.

We respectfully disagree, since the main point of the figure is the overall correlation and heterogeneity, rather than the correlation within sub-sets. Instead of splitting the plot, we changed color contrasts to make it easier to read.

Page 3, Paragraph 1 from line 3 to end of paragraph. The authors wrote "Much of this variation is due to differences in the environment (including tissue, which can be viewed as a cellular environment)". A possible explanation is these two tissues have different mitotic indices (fraction of cells diving and non-diving; flowers have more dividing cell, leaves have more non dividing and endoreduplicated cells) that explains non-CG variation. I would suggest authors to change the text to this and refer to Filipe Borges et al 2021 Current biology paper.

This is certainly a possibility, although higher mCHG levels in flower buds presumably also reflect higher CMT3 expression during embryogenesis (Feng et al. 2020; Gutzat et al. 2020; Papareddy et al. 2021). We now mention both explanations and cite Borges et al. (2021).

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

Summary:

Sasaki et al. carried out a conditional GWAS analysis of TE-CHG methylation in Arabidopsis thaliana natural accessions. They revealed multiple associations with SNPs in known DNA methylation genes. A new finding is the association found proximal to JMJ26, which had no previously described role in the maintenance/establishment of RdDM-targeted transposons. The authors validate the JMJ26 association using a loss-of-function mutant of JMJ26, which essentially recapitulates the GWAS effect, suggesting that JMJ26 is likely causal. An important point of the study is that the associations detected with conditional GWAS have not been seen in previous univariate (i.e. unconditional) GWAS, probably due to to a lack of power. At the sub-genome-wide threshold the authors discovered further, albeit weaker, associations that were also highly enriched for known DNA methylation genes.

Overall impression:

The manuscript is clearly written, and the functional validation of the JMJ26 GWAS signal is commendable and certainly goes beyond the typical GWA study. Beyond this validated association however, the GWAS results are mainly confirmatory. They essentially highlight that methylation genes previously identified by way of mutant screens are variable in natural populations, and (probably) causative of non-CG methylation variation in TEs. What I personally found very distracting throughout the manuscript was the strong emphasis on the methodological aspect; that is, the conditional GWAS, which is really not new. Furthermore, the conceptual/philosophical discussion about what is a complex trait or what can be called polygenic was slightly pedantic and distracted from the biological message.

There are three points here. First, we disagree that the GWAS results are confirmatory. Sure, only one of our associations is connected with a novel gene, but the fact that the four other genes apparently harbor major polymorphism is a new finding that contributes to our understanding of the function of this trait (and, possibly, these genes). Second, while it is possible that we emphasize statistical methodology too much, we do this for clarity, not to claim that what we are doing is novel. Third, we are similarly not interested in defining what is polygenic and what isn’t, but rather put the results in the context of other studies. We have changed the writing in various places to make it clearer (and hopefully less distracting/pedantic).

A conceptual comment:

• The conditional GWAS presented here is conceptually very similar to conditional QTL mapping approaches where candidate loci are included, a priori, as covariates in the model, and a scan is performed to search for additional modifiers. It is known that this approach increases power because the scan is performed on the residual trait variation (having accounting for effect of candidate loci). This is also the idea behind MQM mapping, although in the latter the inclusion is not restricted to candidate loci. Instead of including candidate SNPs as covariate the authors include TE-CHH methylation levels as a covariate as it is highly correlated with TE-CHG methylation. By doing this, the authors essentially "control" for any SNP affecting the covariance between CHG and CHH, even if these SNPs (and their genetic architecture) remain unknown. Hence, the conditional scan is mainly on the residual variation in TE-CHG methylation that is unique to this context (i.e. independent of CHH). That additional TE-CHG associated loci pop up in this scan is perhaps not so surprising.

We agree, and have even written papers on this very subject. We were surprised by this comment as we felt we had included lengthy sections (see also comment above) about methodology, emphasizing that multi-trait analysis is a good idea in principle. One of our purposes here is to provide a beautiful example demonstrating this. We have tried to make these points clearer.

The finding that this conditional GWAS yields again a handful of loci of that explain a considerable part of the trait (now residual trait) variation leads the authors to suggest that the genetic architecture underlying non-CG methylation of TEs is not "polygenic". I think this is semantics. All the authors have done is relegate any causal SNPs underlying the covariance between TE-CHG and TE-CHH to the right hand side of the equation of their GWAS model, and subsumed it under the predictor "TE-CHH methylation levels". That is, the genetic architecture underlying this covariance is still unknown, difficult to identify and probably highly polygenic.

Again we agree, and fail to see why the reviewer thinks we do not. Nowhere do we claim that the overall covariance has a simple basis, and we explicitly state that it is the conditional mCHG variation that has an oligogenic basis. We did write that “univariate GWAS of mCHG variation failed to detect any significant associations, leading us to conclude, erroneously, that the trait was simply too polygenic”, which was imprecise, and arguably erroneous. The word “erroneously” has been removed in the revision.

The authors essentially decompose a complex traits into parts and map genetic architectures for each part. Although each part seems less complex and more oligogenic than polygenic, when putting all the parts back together, I would argue we are getting close to a complex trait with a polygenic architecture. The study by Hüther et al, which the authors also cite, is another example of how a complex trait can be decomposed into parts. In reference to one of the authors' GWAS associations, they say "...this association was also recently found by Hüther et al. (2022) using GWAS for unconditional mCHG levels of individual transposons. The MIR823A polymorphism appears to almost exclusively affect mCHG (Figs. S2, S3), primarily targeting the same transposons as a CMT3 knock-out...". In the case of Hüther et al., the complex TE-CHG methylation trait is simplified by selecting specific TEs, a priori, that are differential methylated in CMT3 knock-out lines. One could go on like this, and continue to peel away this complex trait. But, again, this does not mean that the overall TE-CHG methylation trait is not complex nor polygenic. It spirals down into a discussion of what is actually meant by "complex" or "polygenic", which is an interesting discussion, but - in the case - of this manuscript takes away from the biological message. My point is perhaps best reflected in the following statement from the discussion section: "Despite high heritability, univariate GWAS of mCHG variation failed to detect any significant associations, leading us to conclude, erroneously, that the trait was simply too polygenic (Kawakatsu et al., 2016)." But a few lines below the authors seem to realize what they have actually done "We believe that, by controlling for mCHH, we have effectively simplified the trait, revealing genetic factors affecting mCHG only, perhaps by affecting the maintenance of this type of DNA methylation."

The phrase “seem to realize” is unwarranted and unnecessary sarcasm. Given that we cite the two century-old papers that first demonstrated that it was possible to decompose complex traits into Mendelian ones, it should be obvious that we understand what we have done. That our writing could have been better is another matter. As noted above, the word “erroneously” has been dropped, and we have also changed the second sentence to make it obvious that this is obvious. We suspect that whether one finds this part of the Discussion “distracting” or not depends on training and background — our objective was to explain our results to readers who (unlike us and the reviewer) are not well-versed in quantitative genetics.

Specific comments

1. A large part of the manuscript focuses on SNPs that enriched for a priori genes that fall below the genome-wide significance threshold. While I see the reasons for doing this in this particular manuscript, I do not see how this is useful in general (again this approach is partly "sold" on methodological grounds). The approach can obviously not be extended to study traits where a priori gene sets are unavailable or incomplete. Moreover, the "FDR" approach based on the a priori gene set labels GWAS hits that are not within the a priori set "false discoveries", which may or may not be true. Moreover, there is no "natural" stopping point for going below GWAS thresholds. An alternative, to this would be to perform a targeted GWAS for a priori genes (+ a LD window around them). Since this alleviates the multiple testing burden, I would be curious to see what this yields both in terms of conditional and unconditional analysis. Candidates that show a signal could be included as covariates and a conditional scan for unknown genes could then be performed.

The FDR analysis using a set of a priori genes should be explained in detail in this ms. It is cumbersome to go to another manuscript to see what was done exactly, especially since this information is also difficult to dig up in the Atwell 2010 study. Although I understand the idea behind this approach, I would be concerned that this type of "FDR" analysis assumes that that all methylation genes are known. A novel candidate that was perhaps never identified in mutants screens before would be classified as a false discovery. Similarly, known candidates that carry no functional polymorphisms in nature, perhaps because they are highly constraint, will never become a discovery.

Comments 1 and 9 largely overlap, and so we moved 9 here for clarity and respond to both at the same time. We agree that the enrichment analysis should be explained in this article as well, so as to save the reader from finding the supplement to an old paper. A new section has been added to Methods. In this section, we also try to preempt some of the misunderstandings in the reviewer's comments.

First, our approach is indeed generally applicable. Whether it is useful depends on what you want to do, and yes, the utility will depend on the quality of the independent data, but note that the a priori gene set does not have to be genes: you could use this approach to compare coding vs non-coding regions of the genome, for example.

Second, we are not trying to “sell” our approach (or anything else for that matter).

Third, the approach does not label GWAS hits that are not within the a priori set as false discoveries: it says nothing about these hits.

Fourth, we are not sure what is meant by a ‘“natural” stopping point for going below GWAS thresholds’, but our approach does provide a simple way to explore how FDR (in the a priori set!) depends on the threshold used.

Fifth, the proposed alternative of “targeted GWAS” (non-genomewide association, as it were) is not equivalent, because our approach was not designed to increase power by alleviating the multiple testing burden, but rather to rigorously demonstrate that there is a signal in the data when faced with uncalibrated p-values. That it can also be used to explore sub-significant associations is a nice side-effect that we exploit here.

Sixth, we do not assume that all methylation genes are known, nor is our goal to find them all.

With regards to the CMT2 signals (particularly section "Further evidence for allelic heterogeneity at CMT2") it would have been useful/clearer to break down CHH into CWA and non-CWA.

While this is a sensible suggestion, the focus of this paper is on mCHG, and refining the mCHH measurement would essentially amount to re-doing all analyses.

I understand that the authors set out to do this conditional analysis because previously no hits could be found for CHG TE methylation. However, have the authors considered going the other way around and performing a CHH|CHG analysis to find additional QTL affecting CHH methylation, partly indepedently of CHG?

Yes, this was in the paper, but we only mention it in the Discussion (and Fig S13) as the results were only of methodological interest (as expected, they were very similar).

The authors write: "While both mCHG and mCG showed high heritability, GWAS yielded little in terms of significant associations. This might be because these "traits" are highly polygenic, or because they are at least partly transgenerationally inherited, and hence do not behave like standard phenotypes." Please clarify what they mean by "not behave like standard phenotypes".

Done.

The authors write: "Our starting point is the observation that mCHG and mCHH levels on transposons are strongly correlated in the 1001 Epigenomes data set (Kawakatsu et al., 2016), especially for RdDM- targeted transposons (Fig. 1A; see Methods). Much of this variation ....". What is mean by "this variation"?

The sentence has been changed to make this clearer.

A few lines below, they write "...huge". Please rephrase.

Done.

The authors write: "sample data set ("Leaf SALK ambient temperature"; n=846). Interestingly, the covariance between mCHH and mCHG showed the same pattern in data generated by knocking out known or potential DNA methylation regulators in the same genetic background (Fig. 1B) (Stroud et al., 2013). This demonstrates strong co-regulation of these types of methylation, in particular for RdDM-targeted transposons." It is noticeable that many double mutants are off the diagonal. To me this indicates that they affect one context more than the other (i.e. they break covariance). Second, it suggests that they are probably interacting non-additively. It would be great if the authors could comment on this observation; perhaps also later in the ms, where they make a case for additivity.

We are not convinced that the double- or triple-mutant show non-additivity. Adding up effects in Figure 1 works pretty well. As for our GWAS results, it is clear that small effects (like the ones in our GWAS) will always tend to look additive for simple mathematical reasons. This does not mean that no interactions exist, and we emphasize this in the paper. We also have an example of non-linearity when it comes to TE activity. This is now also emphasized.

The authors write: " it is difficult to say what fraction of these factors is genetic and what is environmental, but, regardless of this, we hypothesized that the substantial covariance could reduce power of GWAS for either mCHH or mCHG (when using a standard univariate model), and that an analysis accounting for this covariance might perform better...". The arguments given thus far are not sufficient to understand why a "substantial covariance" between traits would reduce the power to map individual traits. I think more needs to be done here to motivate this.

The sentence following the one quoted is “In essence, we sought to simplify a complex trait by breaking it into constituent parts”, which is very much part of the motivation. As the reviewer noted above, it is not surprising that a conditional analysis turns out to be more powerful. The comment may have arisen from the statement “This insight is the basis for this paper”, which is misleading — there is no insight here, just a very obvious hypothesis, which turned to be correct. We have changed the writing to make this clearer.

The authors write" "However, MSI1 is required to control DNA methylation via repression of MET1, and a loss of FAS2 in CAF-1 induces mCHG hypermethylation (Fig 1B) (Stroud et al., 2013; Jullien et al., 2008)...", where is the "FAS2 in CAT-1" result visible in Fig. 1B?

fas2 induces mCHG hypermethylation in CMT2-targeted TEs, presumably via a complex that also involves MSI1. It is marked in Fig. 1B. We have rephrased the sentence to make this clearer.

The results presented in "A jmjC gene is a novel modifier of mCHG in RdDM-targeted transposons" could have been showcased better. Only after reading the methods part did I realize that the authors generated CRISPR mutants. It reads as if the authors just picked up some available loss of function mutants and profiled them. But, clearly, much more work was involved here and the authors could have brought that out more. Perhaps more generally, I think all the new functional analysis the authors perform is largely "under-sold" in this manuscript at the expense of unnecessary methodological/concpetual discussion (see point above).

We actually generated CRISPR/CAS9 mutants only for MIR823A (Table S5). For JMJ26, a t-DNA insertion line was available, and results based on this and rescue lines provided sufficient results. To clarify this, we corrected the subsection titles.

In section "The power and complexity of conditional GWAS", the authors write "The performance of GWAS relies on using the right model for the relation between genotype and phenotype. As with other statistical methods, using the wrong model may lead to unpredictable results." This seems like a too obvious of a statement.

Indeed: it is meant ironically. It is obvious, yet people do it.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Sasaki et al. carried out a conditional GWAS analysis of TE-CHG methylation in Arabidopsis thaliana natural accessions. They revealed multiple associations with SNPs in known DNA methylation genes. A new finding is the association found proximal to JMJ26, which had no previously described role in the maintenance/establishment of RdDM-targeted transposons. The authors validate the JMJ26 association using a loss-of-function mutant of JMJ26, which essentially recapitulates the GWAS effect, suggesting that JMJ26 is likely causal. An important point of the study is that the associations detected with conditional GWAS have not been seen in previous univariate (i.e. unconditional) GWAS, probably due to to a lack of power. At the sub-genome-wide threshold the authors discovered further, albeit weaker, associations that were also highly enriched for known DNA methylation genes.

Overall impression:

The manuscript is clearly written, and the functional validation of the JMJ26 GWAS signal is commendable and certainly goes beyond the typical GWA study. Beyond this validated association however, the GWAS results are mainly confirmatory. They essentially highlight that methylation genes previously identified by way of mutant screens are variable in natural populations, and (probably) causative of non-CG methylation variation in TEs. What I personally found very distracting throughout the manuscript was the strong emphasis on the methodological aspect; that is, the conditional GWAS, which is really not new. Furthermore, the conceptual/philosophical discussion about what is a complex trait or what can be called polygenic was slightly pedantic and distracted from the biological message.

A conceptual comment:

• The conditional GWAS presented here is conceptually very similar to conditional QTL mapping approaches where candidate loci are included, a priori, as covariates in the model, and a scan is performed to search for additional modifiers. It is known that this approach increases power because the scan is performed on the residual trait variation (having accounting for effect of candidate loci). This is also the idea behind MQM mapping, although in the latter the inclusion is not restricted to candidate loci. Instead of including candidate SNPs as covariate the authors include TE-CHH methylation levels as a covariate as it is highly correlated with TE-CHG methylation. By doing this, the authors essentially "control" for any SNP affecting the covariance between CHG and CHH, even if these SNPs (and their genetic architecture) remain unknown. Hence, the conditional scan is mainly on the residual variation in TE-CHG methylation that is unique to this context (i.e. independent of CHH). That additional TE-CHG associated loci pop up in this scan is perhaps not so surprising.

The finding that this conditional GWAS yields again a handful of loci of that explain a considerable part of the trait (now residual trait) variation leads the authors to suggest that the genetic architecture underlying non-CG methylation of TEs is not "polygenic". I think this is semantics. All the authors have done is relegate any causal SNPs underlying the covariance between TE-CHG and TE-CHH to the right hand side of the equation of their GWAS model, and subsumed it under the predictor "TE-CHH methylation levels". That is, the genetic architecture underlying this covariance is still unknown, difficult to identify and probably highly polygenic.

The authors essentially decompose a complex traits into parts and map genetic architectures for each part. Although each part seems less complex and more oligogenic than polygenic, when putting all the parts back together, I would argue we are getting close to a complex trait with a polygenic architecture. The study by Hüther et al, which the authors also cite, is another example of how a complex trait can be decomposed into parts. In reference to one of the authors' GWAS associations, they say "...this association was also recently found by Hüther et al. (2022) using GWAS for unconditional mCHG levels of individual transposons. The MIR823A polymorphism appears to almost exclusively affect mCHG (Figs. S2, S3), primarily targeting the same transposons as a CMT3 knock-out...". In the case of Hüther et al., the complex TE-CHG methylation trait is simplified by selecting specific TEs, a priori, that are differential methylated in CMT3 knock-out lines. One could go on like this, and continue to peel away this complex trait. But, again, this does not mean that the overall TE-CHG methylation trait is not complex nor polygenic. It spirals down into a discussion of what is actually meant by "complex" or "polygenic", which is an interesting discussion, but - in the case - of this manuscript takes away from the biological message. My point is perhaps best reflected in the following statement from the discussion section: "Despite high heritability, univariate GWAS of mCHG variation failed to detect any significant associations, leading us to conclude, erroneously, that the trait was simply too polygenic (Kawakatsu et al., 2016)." But a few lines below the authors seem to realize what they have actually done "We believe that, by controlling for mCHH, we have effectively simplified the trait, revealing genetic factors affecting mCHG only, perhaps by affecting the maintenance of this type of DNA methylation."

Specific comments

• A large part of the manuscript focuses on SNPs that enriched for a priori genes that fall below the genome-wide significance threshold. While I see the reasons for doing this in this particular manuscript, I do not see how this is useful in general (again this approach is partly "sold" on methodological grounds). The approach can obviously not be extended to study traits where a priori gene sets are unavailable or incomplete. Moreover, the "FDR" approach based on the a priori gene set labels GWAS hits that are not within the a priori set "false discoveries", which may or may not be true. Moreover, there is no "natural" stopping point for going below GWAS thresholds. An alternative, to this would be to perform a targeted GWAS for a priori genes (+ a LD window around them). Since this alleviates the multiple testing burden, I would be curious to see what this yields both in terms of conditional and unconditional analysis. Candidates that show a signal could be included as covariates and a conditional scan for unknown genes could then be performed.
• With regards to the CMT2 signals (particularly section "Further evidence for allelic heterogeneity at CMT2") it would have been useful/clearer to break down CHH into CWA and non-CWA.
• I understand that the authors set out to do this conditional analysis because previously no hits could be found for CHG TE methylation. However, have the authors considered going the other way around and performing a CHH|CHG analysis to find additional QTL affecting CHH methylation, partly indepedently of CHG?
• The authors write: "While both mCHG and mCG showed high heritability, GWAS yielded little in terms of significant associations. This might be because these "traits" are highly polygenic, or because they are at least partly transgenerationally inherited, and hence do not behave like standard phenotypes." Please clarify what they mean by "not behave like standard phenotypes".
• The authors write: "Our starting point is the observation that mCHG and mCHH levels on transposons are strongly correlated in the 1001 Epigenomes data set (Kawakatsu et al., 2016), especially for RdDM- targeted transposons (Fig. 1A; see Methods). Much of this variation ....". What is mean by "this variation"?
• A few lines below, they write "...huge". Please rephrase.
• The authors write: "sample data set ("Leaf SALK ambient temperature"; n=846). Interestingly, the covariance between mCHH and mCHG showed the same pattern in data generated by knocking out known or potential DNA methylation regulators in the same genetic background (Fig. 1B) (Stroud et al., 2013). This demonstrates strong co-regulation of these types of methylation, in particular for RdDM-targeted transposons." It is noticeable that many double mutants are off the diagonal. To me this indicates that they affect one context more than the other (i.e. they break covariance). Second, it suggests that they are probably interacting non-additively. It would be great if the authors could comment on this observation; perhaps also later in the ms, where they make a case for additivity.
• The authors write: " it is difficult to say what fraction of these factors is genetic and what is environmental, but, regardless of this, we hypothesized that the substantial covariance could reduce power of GWAS for either mCHH or mCHG (when using a standard univariate model), and that an analysis accounting for this covariance might perform better...". The arguments given thus far are not sufficient to understand why a "substantial covariance" between traits would reduce the power to map individual traits. I think more needs to be done here to motivate this.
• The FDR analysis using a set of a priori genes should be explained in detail in this ms. It is cumbersome to go to another manuscript to see what was done exactly, especially since this information is also difficult to dig up in the Atwell 2010 study. Although I understand the idea behind this approach, I would be concerned that this type of "FDR" analysis assumes that that all methylation genes are known. A novel candidate that was perhaps never identified in mutants screens before would be classified as a false discovery. Similarly, known candidates that carry no functional polymorphisms in nature, perhaps because they are highly constraint, will never become a discovery.
• The authors write" "However, MSI1 is required to control DNA methylation via repression of MET1, and a loss of FAS2 in CAF-1 induces mCHG hypermethylation (Fig 1B) (Stroud et al., 2013; Jullien et al., 2008)...", where is the "FAS2 in CAT-1" result visible in Fig. 1B?
• The results presented in "A jmjC gene is a novel modifier of mCHG in RdDM-targeted transposons" could have been showcased better. Only after reading the methods part did I realize that the authors generated CRISPR mutants. It reads as if the authors just picked up some available loss of function mutants and profiled them. But, clearly, much more work was involved here and the authors could have brought that out more. Perhaps more generally, I think all the new functional analysis the authors perform is largely "under-sold" in this manuscript at the expense of unnecessary methodological/concpetual discussion (see point above).
• In section "The power and complexity of conditional GWAS", the authors write "The performance of GWAS relies on using the right model for the relation between genotype and phenotype. As with other statistical methods, using the wrong model may lead to unpredictable results." This seems like a too obvious of a statement.

Significance

The manuscript is clearly written, and the functional validation of the JMJ26 GWAS signal is commendable and certainly goes beyond the typical GWA study. Beyond this validated association however, the GWAS results are mainly confirmatory. They essentially highlight that methylation genes previously identified by way of mutant screens are variable in natural populations, and (probably) causative of non-CG methylation variation in TEs.

Feynman’s approach encouraged him to follow his interests wherever they might lead. He posed questions and constantly

Creating strong and clever connections between disparate areas of knowledge can appear to others to be a flash of genius, in part because they didn't have the prior knowledges nor did they put in the work of collecting, remembering, or juxtaposition.

This method may be one of the primary (only) underpinnings supporting the lone genius myth. This is particularly the case when the underlying ideas were not ones fully developed by the originator. As an example if Einstein had fully developed the ideas of space and time by himself and then put the two together as spacetime, then he's independently built two separate layers, but in reality, he's cleverly juxtaposed two broadly pre-existing ideas and combined them in an intriguing new framing to come up with something new. Because he did this a few times over his life, he's viewed as an even bigger genius, but when we think about what he's done and how, is it really genius or simply an underlying method that may have shaken out anyway by means of statistical thermodynamics of people thinking, reading, communicating, and writing?

Are there other techniques that also masquerade as genius like this, or is this one of the few/only?

Link this to Feynman's mention that his writing is the actual thinking that appears on the pages of his notes. "It's the actual thinking."

imitations and constraints, leaving you happily unoptimized and free to roam, to wonder, to wander toward whatever makes you feel alive here and now in each moment.

Some may categorize handbooks on note taking within the productivity space as "self-help" or "self-improvement", but still view it as something that happens outside of ones' self. Doesn't improving one's environment as a means of improving things for oneself count as self-improvement?

Marie Kondo's minimalism techniques are all external to the body, but are wholly geared towards creating internal happiness.

Because your external circumstances are important to your internal mental state, external environment and decoration can be considered self-improvement.

Could note taking be considered exbodied cognition? Vannevar Bush framed the Memex as a means of showing associative trails. (Let's be honest, As We May Think used the word trail far too much.)

How does this relate to orality vs. literacy?

Orality requires the immediate mental work for storage while literacy removes some of the work by making the effort external and potentially giving it additional longevity.

Joint Public Review:

The present manuscript compares the connectomes of a large range of mammal species using diffusion MRI data. The manuscript reports two main findings: (1) connectomes of more related species are generally more similar, as assessed using Laplacian eigenspectra, than of unrelated species; (2) differences between species' connectomes are generally driven by local regional connectivity profiles, whereas global features are generally preserved.

The first finding is comforting, but in a way not extremely surprising. It would be extremely surprising if more related species do not show more similarity in their connectome. Indeed, this is the reason many phylogenetic analyses use statistical techniques that take the relatedness of species explicitly into account. I find the statement that connectome organization recapitulates traditional taxonomies a bit over the top, as this suggests that a phylogenetic tree constructed based on connectomes would be similar to a tree based on other measures, such as morphology or genetics. This will probably be the case, but is not what the authors have tested here.

The second result is in my opinion the key result of the paper. The main novelty of the paper is that -finally, for the field-bridges approaches taken by some researchers in searching for differences across species (these are usually researchers interested in anatomy) and researchers searching for conserved principles across species (usually researchers approaching connectivity from a network or graph theory perspective). By showing what aspects of a connectome are generally conserved and which are changed, this paper starts unifying the two views and this is an important contribution.

It would, however, have been nice if the authors had explored this notion a bit further. Now, they just state that taking certain features into account means the connectomes look more different, but they do not zoom into the specific brains to see what this means at a biological level. Some of the authors have published, for instance, on the unique connectivity profiles of parts of the human brain and it would have been nice to show that these fall under the local regional connectivity profile aspects of the connectomes. This is a missed opportunity to even further unify the different research traditions.

The manuscript suggests that white matter connectivity in mammals is more similar between species within one taxonomic group than across different groups, proposing that the brain's connectome reflects phylogenetic relationships. The manuscript further details which features of the network organisation are associated with larger differences across groups and hence may drive speciation; and which features seem to be a common principle across mammals.

The authors present evidence based on the analysis of diffusion-weighted brain imaging data across 124 species, 111 of which were included in the comparison. The dataset is a great resource to address their research question.

The paper is clear and the evidence compelling. The manuscript adds valuable insights into the connectome architecture across species, potentially opening a new perspective on the link between genetics and behaviour. I would like to point out the great open science practice of the authors - code is available with a great ReadMe to guide potential users, connectivity matrices are available, and all software packages used in the analyses have been cited.

The figures are clear and complement the manuscript.

Technical Comments:

- Spectral approach / Interpretation<br /> It would be good to have more insight into the meaning of the spectral distance results. My understanding is this: the eigenvalues of the normalised Laplacian obviously have a mean of 1 (because their sum equals the trace of the Laplacian, which is equal to N [number of nodes]). Therefore, the distances between the spectra essentially amounts to comparing higher moments, and in particular the variance (as the histograms look quite Gaussian, I am guessing the distances are dominated by differences in the variance). But what does it mean that bats have a higher variance in these Eigenvalues than primates? I know that the authors try to give *some* insight, e.g. that when the distribution is peaky around 1, it means there are more stereotypical local patterns of connectivity. I understand that. But what are these patterns?

- Effect Size / Null Distribution<br /> I like the idea and the ambition of this paper. My main concern is that the differences are very small. Pretty much all the measures (laplacian eigenspectra and network-theoretic measures) are very similar between animals. This can be interpreted in two ways. (1) it may mean that the brain organisation is preserved, which is the interpretation of the authors. But it could also mean that (2) the metrics are not very informative. How do we know if we are in situation (1) or (2)? There is no comparison to a good null model (except in Fig4 but I don't think a random network is a good null). One possible null is two random networks connected to each other with a few random connections (to mimic left-right brains)?

* The authors use cosine similarity to compare the eigenspectra distributions. I think this does them a disservice. cosine similarity normalises the distributions quadratically instead of linearly. But the main thing that is changing is the variance. So normalising quadratically diminishes the dissimilarities between distributions. I have looked at their data (thanks for sharing!) and using multidimensional scaling with Euclidean looks much better than with cosine distance. I would suggest using euclidean.

* The authors use a bootstrapping method to calculate an average distance which they claim is useful because they don't have the same number of animals in each category. I don't think this bootstrapping is useful at all. If anything, it just adds noise. Averaging 10,000 samples with replacement does not change the outcome compared to simply averaging the matrices without the sampling. To test this: vary n and it should converge to the average of the original non-sampled data. (I've tried it!)

* The authors should clarify whether they are using the weighted or binarised connectivity matrices in the spectral approach (and also what threshold). I suspect that they are using binarised matrices, which probably explains why the spectral results fit better with the graph topology results when the latter uses binarised matrices.

- Parcellation.<br /> One main issue is the way in which the connectomes are divided up into 200 regions each, independent of the brain size. This to me seems a confound. I know it's rather standard practise in the field, but I have yet to see a validation that this does not influence the results. Given the enormity of the dataset here I would ask the authors to run their analyses in a way that the number of regions is a function of the size of the brain-this is a much more realistic assumption, as we know that a shrew size brain has about 20 cortical areas, whereas the human has about 180 according to Glasser et al.

Author Response

Reviewer #1 (Public Review):

This paper presents an approach to estimate Rt for 170 countries. While it is an impressive amount of work, I think the pipeline is similar to many currently available frameworks. The paper claims the following novelties over current framework, but more efforts are needed to be done to make it convincing.

1) Obtain stable estimate from multiple types of data:

It turns out the stable estimates just repeatedly use the same approaches to different time series (Figure 3A middle). From the wording I think there should be some methods to combine these time series to have a single estimate of Rt. Overall, the Rt and the time series of infection should be unique. It would be suboptimal, for example if there are big differences in the results from death time series and reported cases time series, which one should I trust?

We think it is a strength to compute different Rt values based on different data, as this allows researchers, policy makers and the public alike to compare the information from different observation types directly. Any discrepancy between two Re trajectories (e.g. between the Re based on cases, Rcc(t), and that based on hospitalisations Rh(t)) is an indication to investigate which external variables (e.g. testing strategy) have changed. We have found it a great advantage when communicating and sharing our results outside of academia that we could point to these separately obtained Re estimates: if the estimates all agreed, more confidence could be given to them.

If one would want to estimate a single estimate, this would require adopting a fundamentally different framework to estimate Re, which exceeds the scope of this work. One could use heuristics (weights representing the trustworthiness of a given source at a given time) to combine the various Re estimates into a single ensemble estimate. Alternatively, one could model the full underlying population dynamics (e.g. with a compartmental model including hospitalization and death) and adopt a fully Bayesian approach to fitting such a model. However, both options require heuristics or priors that will vary substantially through time and per country (as discussed in the Supplementary Discussion), and thus limit how widely the pipeline can be applied.

We have revised the manuscript to make it more clear (early on) that we estimate multiple Re values from separate types of data (see also the response to reviewer 3, item #5). In addition, we now discuss more explicitly what the advantages and disadvantages are of showing these estimates separately (lines 281-290).

2) Adequate representation of uncertainty:

This is the result in Figure 2, suggesting the CI from EpiEstim is too narrow. This would be expected given that EpiEstim assumed the input infection time series is observed and fixed. It would be expected that the proposed approach would provide wider CI and hence the proportion covered would be more. However, I think to validate the wider CI is the correct one, simulation studies are required. I think the most related one would be Figure 1B. The results suggested that the approach works when the Rt is not rapidly changing. However, I have concern on the methods for simulation (details below).

Indeed, the difference in coverage between our method and EpiEstim is due to observation noise. We agree the CI from EpiEstim should be correct assuming that the infection incidence time series can be observed perfectly. However, in reality quite a bit of variability is introduced between infection and case observation: not only due to the delay from infection to observation, but also due to e.g. reduced testing capacity on weekends or reporting errors. To accurately assess the coverage of our method (and whether the CIs are too narrow or too wide) we need to include realistic amounts of observation noise in the simulations. This is why we add autocorrelated noise to our simulated observations, where this noise mimics observed residuals in Switzerland and other countries (Figs. S3, S4, S15, S17).

We have now added explicit comparison to the EpiEstim confidence intervals to supplementary Fig. S4. In addition, we extended the corresponding method section to describe more extensively why and how we added observation noise to our simulations (lines 498-518; see also the detailed response to comment 4 below).

3) Real-time of the Rt

There is no simulation about the real-time property of the Rt. The most related one is still Figure 1B. However, looks at the right-tail of the figure (the real-time performance), the proportion covered the true value is decreasing and more efforts are needed to support the framework can be accurate in real-time. For example, how is the real-time performance when Rt is increasing, or Rt decrease sharply due to lock down?

As suggested, we included an additional simulation study to investigate the accuracy and stability of the last possible Re estimate. We present this analysis in a new results paragraph (subsection "Stability of Re estimates in an outbreak monitoring context"; line 121) and Figure S10. Using this analysis, we highlight the trade-off that exists between the timeliness of the Re estimates and their stability.

4) simulation methods to estimate Rt

Both 2) and 3) need simulation to support the results, and hence the simulation approach would be critical. The first part based on Poisson distribution to generate an infection time series, which is OK. However, the issue is the secondary part about how the authors obtained the time series for death/hospitalization/reported cases. To me, after generating the infection time series, based on the delay distribution from infection to death/hospitalization/reported, we could obtain those time series. I am not clear and sure if the authors approach is correct by using smoothing and fitting ARIMA to get those time series.

We believe there may have been some confusion about how our simulation set-up works, and we provided insufficient detail on the design decisions behind this set-up. We have added more explanation for both points to the paper (lines 503-518; additional supplementary Figs. S15-S17). In brief, our simulation process consists of three parts. We first conduct the two steps the reviewer also mentioned: (i) simulating the infection time series, and (ii) simulating the observed time series by using the delay distribution from infection to death/hospitalisation/case report.

However, we find that the observations simulated this way are too smooth compared to real data (see Figure S17). Possible reasons for this are that the delay distribution does not account for weekend and holiday effects, the random and occasional delay in recording confirmed cases, nor irregular components such as confirmed cases that are imported from abroad. We therefore added a noise term in our simulations, resulting in a third step: (iii) adding noise generated from an ARIMA model.

To obtain a realistic ARIMA model for this third step, we fitted a model based on the confirmed case data for SARS-CoV-2 in Switzerland. Specifically, we first obtained the additive residuals based on the log-transformed confirmed cases. We then fitted ARIMA models of various orders and assessed the resulting ACF and PACF plots of their residuals. Based on this, we chose an ARIMA(2,0,1)(0,1,1) model. We refer to Figure S16 to support this: The first row shows the ACF and PACF plots of the original residuals, showing strong autocorrelation. The second row shows the ACF and PACF plots of the residuals after fitting the ARIMA model. We see that there is little autocorrelation left, indicating that this model is reasonable.

In Figure S17, we present simulated observations based on all three steps, and one can see that they look more realistic than the simulated observations after step (ii).

We would also like to point out that the ARIMA model is only used to obtain simulated observations. Our main method to estimate Re and obtain the related confidence intervals does not require fitting an ARIMA model.

Minor comments:

1) What does near real-time mean? The estimates of Rt are delayed for a few days like other approaches?

Indeed, the estimates of Rt are delayed by the time it takes from infection to a case to be observed. We have replaced the term “near real-time” by “timely” throughout the manuscript, and added this explanation of the delay more explicitly to the text (line 86).

2) For the results in Table 1, I think if there are some results suggesting that other approaches (like EpiEstim) perform worse than the proposed approach, it would be better to illustrate the value of the proposed approach.

We have improved and extended the comparison of our method against others in two ways: (i) we added further comparison of the coverage of our method vs. that of EpiEstim to Fig. S4 (see also the response to major comment 2), and (ii) we added comparison against different commonly used pipelines (see minor comment 3 below). Instead of comparing to other approaches, the analysis in Table 1 was meant to illustrate the use of the Re estimates resulting from our method alone.

3) I think more discussions are needed for the similarity and differences for current approach. For example, Abbott et al (https://wellcomeopenresearch.org/articles/5-112) used a similar pipeline.

We added a section to the results (paragraph starting line 182; Fig. 3), dedicated to comparing our approach with relevant alternatives. We compared some of our empirical results with the estimates published on epiforecasts.io (based on EpiNow2 package from Abbott et al.), as well as official COVID-19 Re estimates for Austria (by AGES) and Germany (by RKI). We find that estimates published by the RKI and AGES health authorities are likely to be overconfident and to suffer from previously-identified biases (notably in Gostic et al., 2020, PLOS Computational Biology). We provide a detailed comparison of the features and approaches of these methods (EpiNow2, AGES, RKI), with the addition of the epidemia R-package (Supp File S2). This comparison highlights the unique features of the method developed: its ability to account for time-varying delay distributions and to combine symptom onset data with case data.

4) Figure S11 is about accounting for known imports. While if the local cases are dominant and hence imported cases would not have a big impact on estimates of Rt. The impact of imported cases on estimates of Rt could be complicated, as suggested in Tsang et al. (https://pubmed.ncbi.nlm.nih.gov/34086944/). In addition to assuming imported cases and 'exported' cases could be canceled, it is also assumed that the imported cases had similar transmissibility to the local cases, which may not be true if there is border control.

We thank the reviewer for this interesting comment and reference. We added a brief discussion in the result section of the manuscript to address this limitation (lines 174-177).

Reviewer #2 (Public Review):

This manuscript describes an algorithm of estimating real time effective reproductive number R_e (t). This algorithm combines several methods in a reasonable way: deconvolution of time series of reported case into time series of infection, a Poisson model for generation of infections, and block-bootstrap of residuals to assess uncertainty. Each component is not necessarily novel, but the performance of this algorithm has been validated using comprehensive simulation studies. The algorithm was applied to COVID-19 surveillance data in selected countries across continents, revealing a great deal of heterogeneity in the association of R_e (t) with nonpharmaceutical interventions. Overall, the conclusions seem reliable.

I have several moderate critiques and suggestions:

1) From a statistical point of view, it seems much more natural to integrate the infection generation process and the delay from infection to reporting, possibly with reporting errors, into the same model, with which you will avoid combining the bootstrap and the credible intervals in a somewhat awkward way. I understand you can take advantage of EpiEstim package, but the likelihood is very simple and easy to program up. Nevertheless, I'm not strongly against the current paradigm.

We agree that such an integrated approach is useful, and makes the uncertainty interval estimation more coherent. However, in such an integrated approach one can not use the analytical solution for the likelihood, and methods that choose this approach (like EpiNow2 and epidemia) tend to pay for it in computational complexity. It also makes it harder to include time-varying delay distributions into the model, one aspect that sets our pipeline apart from existing alternatives.

An additional advantage of our method is that estimates for the infection incidence are not influenced by priors on Re. In case of a bad model fit this allows us to separate more easily which part of the model may be misbehaving; and as such can help as a sanity check.

Lastly, our framework has the advantage of modularity: pieces of the pipeline can be (and were) continuously refined or replaced with better pieces. This continuous improvement process allowed a flexible response to the pressing circumstances (the COVID-19 pandemic), and allowed us to extend it to entirely new types of proxy data (e.g., wastewater viral loads - https://ehp.niehs.nih.gov/doi/10.1289/EHP10050 ).

2) Is there a strong reason to believe the residuals are autocorrelated? The block sampling with block size 10 seems arbitrary. The authors fitted an ARIMA model to the residuals for some countries, how good was the fitting? If the block size doesn't matter, then probably the stronger but simpler assumption of independent residuals may not compromise the estimation of R_e (t) much.

Yes, there is reason to believe the residuals are autocorrelated. New supplementary Figure S15 shows the ACF and PACF of the residuals based on the confirmed cases of Switzerland, China, New Zealand, France and the US, and one can see that for most countries, the obtained residuals are clearly autocorrelated. We added this point to the simulations method section in the paper (lines 503-518). Please also see our response to Reviewer 2, major point 4 above.

Choosing an optimal block size for the block bootstrap method is generally difficult. To capture weekly patterns, we need a block size of at least 7. We tried different sizes and found that 10 tended to work well in a variety of simulation settings (an example is given in Fig. S19).

3) I don't see the necessity of using segmented R_e (t) instead of a smooth curve in the simulation studies. The inferential performance, especially the coverage of the CI's, is much less satisfactory when a segment has a steep slope. The authors may consider constructing splines based on the segments or using basis functions directly.

We started using a segmented Re(t) trajectory to allow for simple parametric generation of different scenarios (e.g. in new Fig. S10), and to specifically study our ability to estimate sudden transitions in Re (discussed wrt. Table 1, Fig. S2). We agree this approach makes our method look worse than necessary, since it is generally difficult to estimate such abrupt changes in Re. However, we thought this would be the more stringent test of our method, as we will perform better on any more smooth trajectory.

4) The authors smoothed the log-transformed observed incidences to come up with the residuals. For Poisson data, a variance-stabilized transformation is taking the square root, not the logarithm. In addition, as you already have bootstrap estimates, why not using quantiles directly for CIs but instead using a normal approximation (asymptotic)? When incidence is low, the normal approximation may be much less satisfactory. Also, when using normal approximation for CI, it's much safer to calculate standard deviation and construct CI at the log-scale, i.e., log(θ ̂^*(t)), and then exponentiate back.

Our goal of transforming the original case observations is to stabilize the variance of the residuals. Indeed, the square root transformation is generally recommended if the data to be transformed is Poisson distributed. In our case, however, the original case observations are not quite Poisson. Specifically, the infection incidence at time t given the past incidence is modelled with a Poisson process (see Section 4.4), but the case observations are modelled with an additional convolution step of the infection incidence with a delay distribution, and there is additional variation due to e.g. weekday effects. It is thus not clear a priory which transformation works best for our data, and we therefore investigated various possible transformations (including the square root transformation). We found that no transformation was uniformly the best for data of different countries, but that the log-transformation tended to perform best overall. This is why we chose the log-transformation. Please see the new supplementary Figure S14, where we show the residuals after the square root transformation and the log transformations for various countries.

Regarding the bootstrap confidence intervals, we also investigated different options. Again it is not clear a priory which bootstrap confidence interval performs best for our data, so we compared common choices like quantile, reversed quantile and normal-based in a simulation study. Specifically, we assessed their coverage and found that the normal-based confidence intervals performed best overall (see Fig. S4).

For low incidence settings, none of the bootstrap methods perform very well (as bootstrap consistency does not apply). We now mention this consideration in the paper (line 442).

Finally, regarding the suggestion to compute exp(SD(log(X)): This quantity is generally different from SD(X), which we need for the confidence intervals. We also refer to the coverage in the various supplementary figures (e.g. S2, S4, S5) to support that our approach works well.

5) The stringency index is a convenient metric for intervention intensity. However, it doesn't reflect actual compliance as the authors admitted. Another likely more pertinent metric is human movement (could be multiple movement indices). Human movement indices may not be available in all countries, but they are available in some, e.g., the US, and first wave in China. In some states of the US, it was clear that human movement decreased substantially even before initiation of lockdown. Lack of human movement metrics most likely has contributed to the difficulty in the interpretation of Figure 4.

We have added mobility data (from Apple and Google location data) to our general dashboard, and to the analysis shown in Fig. 5. The mobility traces give more detailed insight in the behavior that may have led to decreases in Re. However, we find similar patterns wrt. decreases in Re as with the stringency index. A more extensive analysis that focuses on different phases of the pandemic may allow for more detailed insights, but we believe this is beyond the scope of our manuscript.

Reviewer #1 (Public Review):

This paper presents an approach to estimate Rt for 170 countries. While it is an impressive amount of work, I think the pipeline is similar to many currently available frameworks. The paper claims the following novelties over current framework, but more efforts are needed to be done to make it convincing.

1) Obtain stable estimate from multiple types of data:<br /> It turns out the stable estimates are just repeatedly use the same approaches to different time series (Figure 3A middle). From the wording I think there should be some methods to combine these time series to have a single estimate of Rt. Overall, the Rt and the time series of infection should be unique. It would be suboptimal, for example if there are big difference in the results from death time series and reported cases time series, which one should I trust?

2) Adequate representation of uncertainty:<br /> This is the result in Figure 2, suggesting the CI from EpiEstim is too narrow. This would be expected given that EpiEstim assumed the input infection time series is observed and fixed. It would be expected that the proposed approach would provide wider CI and hence the proportion covered would be more. However, I think to validate the wider CI is the correct one, simulation studies are required. I think the most related one would be Figure 1B. The results suggested that the approach works when the Rt is not rapid changing. However, I have concern on the methods for simulation (details below).

3) Real-time of the Rt<br /> There is no simulation about the real-time property of the Rt. The most related one is still Figure 1B. However, looks at the right-tail of the figure (the real-time performance), the proportion covered the true value is decreasing and more efforts are needed to support the framework can be accurate in real-time. For example, how is the real-time performance when Rt is increasing, or Rt decrease sharply due to lock down?

4) simulation methods to estimate Rt<br /> Both 2) and 3) needs simulation to support the results, and hence the simulation approach would be critical. The first part based on Poisson distribution to generate an infection time series, which is OK. However, the issue is the secondary part about how the authors obtained the time series for death/hospitalization/reported cases. To me, after generating the infection time series, based on the delay distribution from infection to death/hospitalization/reported, we could obtain those time series. I am not clear and sure if the authors approach is correct by using smoothing and fitting ARIMA to get those time series.

Minor comments:<br /> 1) What is near real-time mean? The estimates of Rt are delay for a few days like other approach?<br /> 2) For the results in Table 1, I think if there are some results suggesting that other approaches (like EpiEstim) perform worse than the proposed approach, it would be better to illustrate the value of the proposed approach.<br /> 3) I think more discussions are needed for the similarity and differences for current approach. For example, Abbott et al (https://wellcomeopenresearch.org/articles/5-112) used a similar pipeline.<br /> 4) Figure S11 is about accounting for known imports. While if the local cases are dominate and hence imported cases would not have a big impact on estimates of Rt. The impact of imported cases on estimates of Rt could be complicated, as suggested that in Tsang et al. (https://pubmed.ncbi.nlm.nih.gov/34086944/). In addition to assume imported cases and 'exported' cases could be canceled, it is also assumed that the imported cases had similar transmissibility to the local cases, which may not be true if there is border control.

Author Response

Reviewer #1 (Public Review):

Xiong and colleagues use an elegant combination of theory development, simulations, and empirical population genomics to interrogate a largely unexplored phenomenon in speciation/ hybridization genomics: the consequences and implications of admixture between species with differing substitution rates. The work presented in this well-written manuscript is thorough, thought provoking, and represents an important advancement for the field. However, there are a few instances where I feel the strength of the conclusions drawn is not fully supported.

Thank you for the positive comments!

The authors begin by presenting evidence based on whole genome sequencing that the two focal species, P. syfanius and P. maackii, are highly diverged despite ongoing hybridization. Though the discussion of remarkable mitochondrial sequence similarity is underdeveloped. I do not understand how such a pattern is not most likely the result of introgression from one species to the other given the relatively high FST across much of the nuclear genome coupled with the generally higher mitochondrial mutation rate in animals.

That’s a very good point. We have included this likely explanation of mitochondrial genome similarity in Line 84-86.

Next, they posit that barrier loci are likely to exist. To support this assertion, the authors use a combination of parental population genetic diversity and divergence comparisons and ancestry pattern analysis in hybrid populations. They show that there is a strong correlation between divergence across pure species and within species diversity across the autosomes. Then using four hybrid individuals they show that low ancestry randomness, as quantified estimates of between group and within group entropy, is associated with genomic region of reduced within group diversity and elevated between group divergence. The use of entropy estimates as a stand-in for admixture proportions and ancestry block analysis when sample size is severely limited is particularly clever. Though I must admit, I do not fully understand the derivations of the two entropy measures, it seems to me that relatedness might have a strong effect on the interpretability of between individual entropy estimates (Sb). With very small population sizes this may be a real issue.

Yes, genetic relatedness will play a big role in between-individual entropy (Sb). A group of highly correlated individuals will produce highly predictable ancestry (knowing one individual’s local ancestry gives much information on the local ancestries of others), and Sb will be small because entropy is a measure of uncertainty. If inbreeding is very severe, Sb will no longer be a useful measure because it will be too small across the entire genome. In our hybrid samples, although some genomic regions imply the possibility of inbreeding (see local ancestry of Z chromosomes in Figure 3–Figure supplement 1), there is still considerable variation of Sb across the genome which allows us to test for its correlation with DXY and π.

A brief discussion of potential caveats in using the new method developed here seems warranted given its potential usefulness to the population genomics field more broadly. One plausible but less likely alternative interpretation of these patterns is briefly discussed.

We have now devoted the first subsection of Discussion to the caveats and various motivation for entropy metrics. The appendix also contains further explanation of our intuition (section “Appendix-The entropy of ancestry”).

The authors then move on to evidence for divergent substitution rates. Analysis of both D3 and D4 statistics using several different outgroups and a series of progressively stringent FST thresholds shows that site patterns between the two species are highly asymmetrical with P. maackii lineage harboring more substitutions than P. syfanius. The authors offer two possible explanations for this finding and then test both hypotheses. First, they use a comparative tree-based method to show that there is little phylogenetic evidence for lineage biased hybridization from outgroups into either of the focal lineages. Further, the range overlaps of the study species do not correspond with the inferred direction of allele sharing from the Dstat analysis. This is a good argument against contemporary gene flow between the outgroups and P. syfanius, but I am not convinced that ancient gene flow that could have occurred when, say, species distributions may have been different, can be ruled out using this analysis.

Yes, we also felt that our original wording was overly strong. Now we say that our argument is based on current geographic distributions, but that archaic gene flow cannot be totally ruled out. However, we also point out that archaic gene flow with outgroups should still leave some detectable fractions of paraphyletic local gene trees after phylogenetic reconstruction. (Line 192-194).

To test whether this asymmetry can be explained by a difference in substitution rate between the two species the authors show that observed D3 increases and D4 decreases with increasingly divergent outgroups as predicted by theory developed here. The authors take this as evidence supporting the divergent substitution rates. Though they claim only that existence such rate divergence is likely. The unfortunately limited samples sizes seem to preclude attaining more certainty than this. Interestingly, as a byproduct of using D4 as an extended measure of site pattern asymmetry the authors highlight one way in which the ABBA-BABA test can give false positives for introgression. This is an important contribution to the field.

We agree with the reviewer that, for our data type – a handful of unphased genomes, it will be difficult to obtain more direct evidence for substitution rate differences. In line 182-187, we show using maximum-likelihood gene tree reconstruction that P. maackii samples often inherit more derived mutations than P. syfanius. This could be viewed as a separate test utilizing more accurate substitution models in phylogenetic software, while our theoretical calculation provides a coarse but testable signature of D3 and D4.

To provide more direct evidence, we believe one ought to measure spontaneous mutation rates in both species under their native habitats, and obtain better knowledge of generation times and population sizes. The limitation of sampling and rearing these rare species are major barriers for incorporating this kind of evidence into this study.

Finally, the authors observe a monotonic relationship substitution rate ratio and relative genetic divergence across the genome which is in line with their theoretical predictions for differential substitution rates in the face of gene flow. From this they infer an 80% increase in substitution rate from P. syfanius to P. maackii. It is remarkable to be able to extract these substitution rates from genomic regions with the least gene flow. However the veracity of these estimates relies on the assumptions I have highlighted above and should be presented with appropriate caution.

We have included the limitations of our conclusions in the final subsection of the Discussion. Because high FST regions are relatively rare, estimates of observed rate ratio “r” have larger errors in those regions. This problem is partially resolved by using the entire monotonic relationship between r and FST to estimate the true rate ratio, so we rely not only on regions with the least gene flow but the full dataset.

However, we do agree with the reviewer that ours is still a coarse theoretical framework since we do not impose a realistic substitution model (e.g., we don’t allow reverse mutations). We have now emphasized this weakness in the Discussion (Line 348-350).

Reviewer #2 (Public Review):

In their manuscript ("Admixture of evolutionary rates across a hybrid zone"), Xiong et al. use whole genome resequencing data to assess rates of genome evolution between two species of butterflies and determine whether putative barrier loci between the species are also those that evolve at asymmetric rates between them. This work presents a novel hypothesis and rigorously tests these ideas using a combination of empirical and theoretical work. I think the authors could more formally link loci that are evolving at highly asymmetric rates with those that are most likely to be barrier loci by evaluating the relationship between ancestry entropy and ratios of substitution rates between species. Additionally, clarifying the relationship between barrier loci and asymmetric evolution would be beneficial (i.e. are loci that we typically envision to be barrier loci, such as loci involved in reproductive isolation, evolving at asymmetric rates or do asymmetrically evolving loci represent a new type of barrier loci?).

Many thanks for these comments! For the second point (clarifying the relationship between barrier loci and asymmetric evolution), we specifically mean that barrier loci (which specifically are of interest to those who study speciation) cause asymmetric rates of evolution to be preserved between hybridizing species. Asymmetric rates themselves are caused by other factors (spontaneous mutation rate differences, generation times, environmental effects) specific to each species, and barrier loci merely prevent the mixing of asymmetric rates. For the first point (evaluating the relationship between entropy and ratios of substitution rates).

never ending is the ending

being comfortable with the unknown

Frank Herbert Dune

Author Response

Reviewer #1 (Public Review):

Redman and colleagues employed microprisms and two-photon optical imaging to track separately the structure of dorsal CA1 pyramidal neurons or the activity patterns of dorsal Dentate Gyrus, CA3, CA2 and CA1 pyramidal neurons, longitudinally in live mice. First, they carried out a characterization of the optical properties of their system. Second, they performed an example tracking of dendritic spines in the apical aspect of dorsal CA1 pyramidal neurons. Finally, they characterized differences in spatial coding along the tri-synaptic pathway, in the same animals. The main focus of the manuscript is technological and the authors show interesting data to support their technique, which I believe will be of relevance to neuroscientists interested in the hippocampal formation.

Strengths.

While using microprisms to achieve a "side" view of neurons in specific brain areas is not new per se [see Chia et al., J. Neurophysiol. (2009), Andermann et al., Neuron (2013), Low et al., PNAS (2014) etc.] the authors were able to visualize activity of a large neuronal circuit such as the hippocampal trisynaptic pathway - for the first time - in the same animal exploring an environment. This is not only a technical feat but it opens new scientific avenues to study how information is transformed at different stages within the hippocampus, as such I think this will be of broad interest for people in the field. In addition, the authors demonstrated imaging of dendritic spines in the apical aspect of pyramidal neurons but limited to dorsal CA1 due to the labelling density of the transgenic mouse line they decided to use. Despite the fact that imaging apical dendritic spines in dorsal CA1 has been shown earlier [see Schmid et al., Neuron (2016) and Ulivi et al., JoVE (2019)], the use of the micro periscope greatly increases the flexibility of these sort of experiments by enabling tracking of large portion (both apically and basally) of the dendritic arbors of dorsal CA1 pyramidal neurons.

Thank you for the positive comments. We have clarified that apical CA1 dendrites have been imaged in previous work as you point out, just not along the somatodendritic axis (lines 127-130). We have also clarified that we were able to image CA2 and CA3 spines as well (only DG exhibited the increased labeling density in Thy1-GFP-M mice; lines 130-132).

Weaknesses.

While the data are sufficient to demonstrate the technique, the conceptual advance of the paper is very narrow. The findings on spatial coding differences in different hippocampal subregions - namely a nonuniform distribution of spatial information in the different hippocampal subregions - do not add new knowledge but largely confirm the literature. The results on the dynamics of apical dendritic spines of pyramidal neurons in dorsal CA1 seem to confirm previous work, but the interpretation of these results differs fundamentally. In fact both papers cited by the authors (Attardo et al., and Pfeiffer et al.,) come to the conclusion that dendritic spines on basal dendrites of CA1 pyramidal neurons are highly unstable, at least by comparison to other neocortical areas. The authors seem to ignore this discrepancy. However, this discrepancy has importance also to the characterization of the technique the authors developed. In fact, the optical resolution of the system strongly affects the ability to resolve neighboring spines - especially at the high density of dorsal CA1 - and thus it has a direct effect on the measures of synaptic stability [Attardo et al., Nature, (2015)]. The authors duly report lateral and axial resolutions for their micro periscopes and both are lower than the ones of Attardo and Pfeiffer, thus the authors should consider the effects of this difference on the interpretation of their data.

We agree that the advance described in this manuscript is more methodological than conceptual. We do have other studies in progress that will be of greater conceptual interest. However, we believe the technique is of sufficient interest to the field that it is worth publishing the methodological approach and characterization as soon as possible.

We have also addressed the comparison with Attardo et al. and Pfeiffer et al. mentioned by the reviewer. We actually agree with the previous work that dendritic spines in CA1 show a high degree of instability compared to cortex, finding ~15% spine addition and ~13% spine subtraction between consecutive days (Fig. 3H, I), similar to single-day turnover rates observed in Attardo et al. and other papers. Despite the high turnover rate, the fraction of experimentally observed spines that persist across 8-10 days plateaus around 75-80%, indicating that there is a substantial fraction of apical spines that remain stable in the face of ongoing daily turnover. This was also observed in basal dendrites by Attardo et al. (with similar survival fractions) and Pfeiffer et al. (albeit with lower survival fractions), so we would not necessarily characterize this as a discrepancy. We have clarified these points in the manuscript (lines 157, 162-168, 331-332).

The reviewer pointed out that some previous studies used super-resolution microscopy to detect smaller structures and reduce optical merging. This would be an excellent extension of our work, as in principle super-resolution microscopy could be used with the implanted microperiscopes. Although the survival fractions we observed were similar to Attardo et al., they were higher than Pfeiffer et al., possibly due to the predicted effects of optical merging. We have updated the text to note that our results may inflate the degree of stability due to resolution limitations (lines 165-68, 335-340).

Reviewer #2 (Public Review):

Strengths

The Hippocampus is a key brain region for episodic and spatial memory. The major Hippocampal subregions: Dentate Gyrus (DG), CA3, and CA1 have predominantly been investigated independently due to technical limitations that only allow one subregion to be recorded from at a time. In this paper the authors developed a new method that allows DG, CA3, and CA1 to be imaged simultaneously in the same mouse during behavior with a 2-photon microscope. This method will allow investigation of the interactions between Hippocampal subregions during memory processes - a critical yet unexplored area of Hippocampal research. This method therefore provides a new tool that will help provide insight into the complex functions of the Hippocampus during behavior.

This method also provides high resolution optical access to deep dendritic structures that have been out of reach with existing methods. The authors demonstrate they can measure the structure of single spines on distal apical dendrites of CA1 cells. They track populations of spines and quantify spine changes, spines loss, and spine appearance. Spine turnover is thought to be a key process in how the Hippocampus encodes and consolidates memories, and this method provides a means to quantify spine dynamics over very long time periods (months) and can be used to study spine dynamics in CA3 and DG.

We appreciate the comments.

Weaknesses

This method requires the implantation of a relatively large glass microperiscope that cuts through part of the Septal end of the Hippocampus. This is a necessary step to image transversally and observe all the major subregions simultaneously. This is an unfortunate limitation as it damages the very circuits being investigated. The authors attempt to address this by measuring the functional properties of Hippocampal cells, such as their place field features, and claim they are similar to those measured with other methods that do not damage the Hippocampus. However, it is very likely the implant-induced damage is affecting the imaged cells in some way, so caution should be taken when using this method. The authors are very aware of this and briefly discuss the issue. In addition, the authors observe damaged adjacent to face of the glass microperiscope that extends to ~300 um from the face. This area should therefore be avoided when imaging the Hippocampus through the microperiscope.

We agree. This will be important for the interpretation of experiments using the microperisope approach. For many experiments, electrophysiology or traditional CA1 imaging approaches might be preferable to avoid damage to the hippocampal structure. We have tried to be straightforward about these caveats in our discussion. However, we believe the capability of imaging the transverse hippocampal circuit will allow a number of experiments that are currently intractable, and that the benefits will outweigh the caveats in these cases.

Reviewer #3 (Public Review):

Redman et al. describe a novel approach for long-term cellular and sub-cellular resolution functional and structural imaging of the transverse hippocampal circuit in mice. The authors discuss their procedure for implanting a glass microperiscope and show data that clearly support their ability to simultaneously record from neurons within the DG, CA3, and CA1 subregions of the hippocampus. They offer optical characterization demonstrating sufficient resolution to image at the cellular and subcellular level, which is further supported by experimental data characterizing changes in morphology of CA1 apical dendritic spines. Finally, neurons are recorded from as mice engage in navigation behavior, allowing authors to characterize spatial properties of hippocampal cells and relate findings to prior work in the field.

The ability to image from multiple hippocampal subregions simultaneously is a great technical achievement, sure to advance study of the hippocampal circuit. In particular, this approach will likely have tremendous application for addressing the question of how neural representations dynamically change across the hippocampal subfields during initial encoding of novel contexts or later during retrieval of familiar. While the feasibility and utility of this preparation is supported by the data, further characterization of recorded cells will aid the comparison of data collected using this imaging approach to data previously collected with other methodologies.

Thank you for the comments, we have addressed the specific concerns below.

1) Further measures could be taken to more thoroughly evaluate the impact of the implant on cell health. While authors evaluate glial markers, it is not obvious how long after implant these measurements were taken. Additionally, authors could characterize cell responses of neurons recorded proximal to and more distal to their implant to further evaluate implant effect on cell health.

Good points. We have added the date post implantation for the histology samples (Figure 1F caption). To address the second point, we added additional experiments characterizing functional response properties as a function of depth (Figure S7). We did not find systematic changes in place field width or place cell spatial information, as a function of imaging depth (lines 220-224; Figure S7A, B). We did however find a significant relationship between the decay constant for the fitted transients and depth, with cells close ( 130 um) to the surface of the microperiscope face exhibiting slower decay (Figure S7C). This appeared to be due to a small fraction of cells exhibiting longer decay times closer to the microperiscope face. As a result, we advise only imaging neurons >150 um from the microperiscope face (lines 224-226).

2) More in-depth analysis of place cells will aid the comparison of data collected using this novel approach to previously published data. For instance, trial-by-trial data and clearer descriptions of inclusion criteria will allow readers a more detailed understanding of observed place cells.

We have included example place cells with individual trial data (Figure 5C) and have added additional discussion and detail on our selection process for identifying place cells (lines 207-209, 663-666, 674676). In the revised manuscript, we further increased the stringency of our place cell criteria so that none of the cells with time shuffled responses pass the criteria. It should be noted that our place cells were not as reliable as those recorded in the presence of reward (Go et al, 2021). We chose to forgo reward to help ensure that the neurons were responding to spatial location and not to other task variables, but this likely reduced response reliability (see Krishnan et al, bioRxiv; Pettit et al, 2022). We have added discussion of this issue to the manuscript (lines 307-318).

Author Response

Reviewer #1 (Public Review):

The goal of the work was to test for direct and indirect fitness costs associated with specific types of constructs that could be used for gene drive. The authors conclude that there are no direct fitness costs associated with the presence and expression of either Cas9 or the guide RNAs but that the Cas9 is causing off-target cuts that result in loss of fitness. They also conclude that a newer form of CAS doesn't cause these off-target cuts. While the goal of this study is important, there are many caveats associated with the work as reported, and these limit interpretation of the results, Many of the caveats are pointed out in the discussion.

1.a) I am specifically concerned by the fact that from what I read, a company made the transgenic lines and that there was only one transgenic line per treatment. Unless the fly line used for the insertion was completely homozygous for the chromosome where the insertion was made, the lines could have differed in fitness, due to somewhat deleterious reccessives captured in one G1 but not another. This cost could have persisted for a number of generations after the crosses were made, especially in the high frequency "releases". This may not have been a real problem, but without any replication it is difficult to know.

We apologize that this was unclear in our initial submission. We did in fact generate several transgenic lines of each construct and used independently obtained lines for each of our population cages, except for the Cas9_gRNAs construct, where four lines were used in seven population cages (replicates 1 to 4 were founded with the same line). All of these were also crossed to w1118 flies before we obtained homozygous lines, so the impact of deleterious alleles would have been minimized. We have edited the section “Generation of transgenic lines” in the Methods to clarify this.

We also examined the possibility of fitness effects being caused by such alleles in our maximum likelihood analysis (assuming they are unlinked from the construct — otherwise they should have appeared as direct fitness effects). This model was not a good match for the data, nor was the model with direct fitness effects. Based on these results, we consider it unlikely that such deleterious alleles had a major impact on the observed frequency trajectories in our cage populations.

1.b) My concern is reinforced by the fact that the no-Cas9, no-gRNA line goes up in frequency for the first 5 generations and then becomes stable in frequency. The loss of the fitness advantage is consistent with a fitness effect partially linked to the insertion site in that one cross but not others.

Both of these cages were made with independent lines. We agree with the reviewer that the increase in frequency of the no-Cas9_no-gRNAs construct at the beginning of the experiment seems surprising at first. However, if an initial fitness advantage was truly driving the dynamics of this construct, we would expect that the “initial off-target model” (where fitness costs originated before the experiment) should have yielded the highest model quality in our maximum likelihood analysis, since we also allowed advantageous cut off-target alleles (i.e., fitness estimates > 1) in this model. While the maximum likelihood fitness estimate in the “initial off-target model” indeed exceeded the reference value of 1, its 95% confidence interval still included a fitness value of 1, and a neutral model actually yielded the lowest AICc value (i.e., best model quality, Table 3). We think that one possible explanation for this apparent initial frequency increase is that population cages tend to undergo larger than average fluctuations in the first one or two generations due to the smaller initial population size and potential health differences between founding fly lines (which can persist for a generation or two). We briefly note this in the manuscript methods section.

1.c) It is important to note that the starting points are cages with separate vials of the control and experimental strain. Even a small difference in development time of the two strains in the first generation could lead to an excess of homozygotes in the next generation.

We agree. In our maximum likelihood framework, such differences in development time should show up as a viability difference (fraction of offspring that made it to adulthood in the time window of our experiment). We now note in our revised manuscript that fitness differences between genotypes could be due to longer development time rather than an increase in the juvenile death rate in Cas9_gRNAs carriers. In the “Phenotypic fitness assays” section of our revised manuscript, we additionally state that “longer development time of individuals carrying the Cas9_gRNAs construct would also have appeared as a viability cost in our cage study but not in these fitness assays.”

1.d) I am also concerned by the fact that the main conclusion is that the decline in frequency in the Cas9-gRNA line is due to off-target cuts, but there was no sequencing to back up that conclusion. In the discussion, this problem is mentioned but dismissed. I don't see how it can be dismissed when this is a major conclusion that remains based on very indirect evidence.

We thank the reviewer for raising this important concern, which touches on the issue of how our approach differs from previous approaches that sought to directly detect off-target cleavage through sequencing. Our approach, by contrast, seeks to provide a “direct” measurement of the fitness of an allele. While this allows us to avoid the challenging task of detecting off-target mutations in vivo through whole-genome, population-level sequencing (and then predicting their potential effects), it comes at the price that inferences about the molecular nature of these fitness effects will rely on indirect evidence. However, we want to point out that our conclusion of these fitness effects being primarily due to off-target cleavage is based on three independent lines of evidence: (i) The maximum likelihood analysis of the frequency trajectory of the Cas9_gRNAs construct, where statistical model comparison ranked the off-target effect model higher than the direct fitness costs model; (ii) The fact that we inferred fitness costs only for the Cas9_gRNAs construct but not the construct in which Cas9 was replaced with the high-fidelity Cas9HF1 endonuclease (which should have similar expression and thus, similar direct fitness costs); and (iii) The heterogeneity we observed in the frequency trajectories of the Cas9_gRNAs construct in our cages, which is consistent with a model where off-target sites accumulate over the course of the experiment yet more difficult to reconcile with a model of direct fitness costs.

Inspired by the reviewer’s recommendation, we wondered whether we may in fact be able to directly detect cuts at a few computationally predicted off-target sites. To this end, we performed Sanger sequencing at six sites that were computationally predicted for our Cas9_gRNAs construct by CRISPR Optimal Target Finder, which unfortunately revealed only wild-type sequences (this analysis is described in the new section “Evaluation of computationally predicted off-target sites”). However, we believe that this does not rule out off-target cutting as the primary driver of fitness costs for the Cas9_gRNAs construct due to the following arguments we state in the discussion section of our revised manuscript:

“For example, our sequencing approach would not have allowed us to detect larger insertion/deletion events, which are frequently observed at on-target sites (48, 49). More likely though, we suspect that cleavage events occurred at other sites than the six computationally predicted ones. Indeed, the predictions by CRISPR Optimal Target Finder are based on cleavage specificity in cell lines, where off-target cutting is known to occur more frequently than in animals (47). All but one of the predicted off-target sites carry combinations of single nucleotide mismatches in the PAM-proximal and the distal region, which could make in-vivo cleavage less likely at these sites. Generally, our results are consistent with other studies that found off-target cleavage to frequently occur at sites which would have been difficult to predict computationally (50).”

In a sense, our inability to detect any mutated alleles at this small set of computationally predicted off-target sites might actually highlight a key benefit of our approach: It can estimate the potential fitness costs of a construct without having to rely on accurate computational predictions of putative off-target sites or requiring the very costly approach of whole-genome, population-scale sequencing.

Additionally, we would like to point out that while we found off-target effects to explain the empirical data best, we would probably consider our estimation of the overall magnitude of the fitness costs of the Cas9_gRNAs construct as one of the main conclusions of our manuscript, together with the fact that these were avoided when using the high-fidelity Cas9HF1 endonuclease instead. Thus, even if some readers may remain skeptical about the role of off-target cleavage (and we made sure to qualify our claims on this in the Discussion section accordingly), our systematic analysis of the overall fitness effects is more robust and should be of broad interest.

1.e) When releasing homing gene drives, the initial frequency of the transgenic line is very low, and as in the Garrood et al paper cited, it is possible for the gene drive to outpace the non-target cutting. The modeling does not address what the impact of the presumed fitness costs in this experiment would be for a replacement/suppression drive released at low frequency.

We thank the reviewer for raising this point. It has led us to add a completely new analysis on the “Effect of off-target fitness costs on gene drive performance”, in which we now show simulation results to illustrate the effect of direct and off-target fitness effects on both modification and suppression homing drives. We have also added more discussion on how these different types of fitness costs may affect other frequency-dependent CRISPR based gene drives.

Reviewer #2 (Public Review):

This paper reports a set of Drosophila population cage experiments aimed at quantifying fitness effects associated with the expression of Cas9 gene drive constructs in the absence of homing. The study attempts to deconvolve fitness effects due to the presence of the active nuclease at a genomic location from those that arise from off-target effects elsewhere in the genome: an important issue when considering gene drive strategies in the wild. To distinguish effects due to cleavage at the target site from activity elsewhere in the genome, a construct where Cas9 was replaced with a high fidelity nuclease (Cas9HF1) was employed. The experimental design compares the active nuclease-gRNA constructs targeting a site on another chromosome with no gRNA and reporter only controls, all inserted in the same locus. The Cas9 construct was assayed in 7 replicates with Cas9HF1 and controls assessed as duplicates with cages running for between 8 and 19 generations.

2.a) There is a lack of clarity in terms of the cage set up design, the description in the supplementary methods could clarify if all the replicates came from a single founder and the difference in set-ups that necessitated ignoring some 1st generations.

Thank you for pointing this out. We have thoroughly revised and extended our Methods section on “Generation of transgenic lines” to clarify this point. We now explicitly mention that we generated several transgenic lines of each construct and used independently obtained lines for each of our population cages, except for the Cas9_gRNAs construct, where we used four lines in seven population cages (replicates 1 to 4 were founded with the same line).

For the cage start conditions, we now note that “To avoid potentially confounding maternal fitness effects on the construct frequency dynamics (which could arise based on minor differences in health or age between the initial batches of flies mixed together), we excluded the first generation of five cage populations…” In general, it is quite common for this to happen in insect population cage studies (please see some examples below) and is always a very short-term effect.

2.b) The main finding reported from this part of the work is that with the control populations the frequency of the construct remained fairly constant across the generations, but the active nuclease tended to decline. I am somewhat confused by some of the claims here. First, the authors report a "bottoming out" effect where construct frequency declines then levels off: I am not entirely convinced that Figure 2 shows this. For example, comparing replicates 4 and 5 (8 and 16 generations respectively), it looks to me that there is a steady decline at the same rate with no evidence for a plateau. Perhaps replicates 2 and 3 show "some" evidence of leveling. In addition, replicates 4, 5, 6 and 7 have similar construct starting frequencies (particularly 5 and 7, which are only a few % different) yet the former show a steady decline whereas the latter maintain the construct at a steady level. This does not appear to be consistent with the author's explanation of higher off-target effects in populations carrying high frequencies of the construct. It would be helpful if the authors could more clearly explain the trajectories presented in Figure 2.

We agree with the reviewer that our initial description of the raw construct frequency dynamics solely based on visual clues was making too strong claims (e.g., “different frequency dynamics between single replicates”) without providing more quantitative statistical support. This was originally intended as some basic introduction, with our maximum likelihood analysis then providing a more rigorous assessment in the next section. To improve clarity, we have completely restructured this in our revised manuscript. We removed the comparison of Cas9_gRNAs replicates solely based on visual clues, highlighted the general heterogeneity in trajectories among replicates (without making any specific claims), and instead of the vaguely defined “bottoming out” interpretation, we now only mention the average construct frequency change for the Cas9_gRNAs construct. In addition, we now present our more rigorous maximum likelihood analysis of the construct frequency trajectories and statistical model comparison earlier on in the Results section, so that all of our conclusions are now based on this statistical analysis, rather than an initial visual inspection of the curves. Please see also our comments to point 3.a) below, as reviewer 3 made very similar comments and suggestions.

2.c) Utilising the allele frequencies obtained from the cages, 2 locus ML models were applied with the construct insertion site and an idealised off target site. They argue, correctly in my view, that fitness effects can be attributed to off target activity and not cleavage at the 3L target since the Cas9HF1 construct shows no substantive effect. In the models they assume that the presence of Cas9 in the germline (or maternally contributed) will invariably lead to cleavage at the idealised site. The model indicates that the construct insertion per se has no direct fitness costs but that off-target effects may have fitness consequences of approximately 30%, and seek to support this conclusion with simulations. I found this section difficult to follow but I feel that the conclusions are supported.

We agree with the reviewer that the “Maximum likelihood analysis” section was too dense and therefore challenging to follow, especially for non-expert readers who may not be very familiar with such methods. We have revised and extended this section. In particular, we now also provide a brief summary of the modeling approach at the beginning of the section and have added subsection titles aiming to better guide the reader through the various steps of the analysis. Furthermore, we added a table with an overview of all tested models and highlighted the best-fitting models in tables 2 and 3. We hope that this has improved the clarity of our revised manuscript.

2.d) Direct phenotypic assays with the active Cas9 nuclease were performed, looking at viability, mating preference and fecundity. Relegating these data to the supplements is not useful. While significant effects are attributed to the Cas9-gRNA construct, the authors cannot rule out a DsRed effect and it is a shame they did not assay at least one of the control constructs. In addition, in their modelling they assume that Cas9 activity will always cleave but see no evidence for this in the heterozygote viability assay. Whether this is due to the difference in rearing conditions that the authors claim is debatable.

We thank the reviewer for this valuable feedback. As suggested, we have moved the phenotypic assays (Methods & Results) of the Cas9_gRNAs construct to the main part of the revised manuscript. We decided to conduct phenotypic assays only for the Cas9_gRNAs construct, because it was the only one that displayed some fitness costs in our maximum likelihood analysis (in particular, the DsRed construct did not display any fitness costs in the cages). However, given more time and capacity, we agree that additional phenotypic assays would have been desirable (e.g., a larger sample size per construct and additional constructs). Regarding our choice of model for the maximum likelihood analysis, we used a highly simplified off-target approach, which was necessary given the available information.

2.e) Finally, since the initial cage experiments suggest that the Cas9HF1 enzyme reduces off-target effects they assay this enzyme in a model homing drive, indicating that this enzyme performs as well as the regular Cas9. Again, relegation of these data to supplementary datasets is unhelpful and it would improve the manuscript if these results could be simply summarised in a figure.

We added an additional figure at the end of the “Cas9HF1 homing drive” section in the Results showing the gene drive inheritance rate and resistance allele formation rate in early embryos for the Cas9HF1 and Cas9 homing drive respectively. The gene drive inheritance rate is the percentage of offspring with DsRed fluorescence when crossing individual gene drive heterozygotes with “wildtype” homozygotes (i.e., not carrying any gene drive allele) and is used to calculate the gene drive conversion rate (i.e., the rate at which wildtype alleles are converted to drive alleles) mentioned in the main text. We hope that this has improved the clarity of our revised manuscript.

2.f) Taken together, I think this is a useful study but is presented in a way that is at times impenetrable to the non expert. More clarity in presenting the cage and modelling data, as well as promotion of figures from supplementary material to the main manuscript would considerably aid the non expert and provide greater confidence in the interpretations. If these issue could be clarified I feel the work provides a useful addition to the gene drive field and will help those thinking about developing such strategies, particularly relevant are the findings related to the Cas9HF1 enzyme.

We thank the reviewer for the valuable feedback. We have significantly revised the Results as well as the Discussion, provided additional information on the modeling approach, and shifted supplementary material to the main text of the manuscript. We hope this has improved the overall clarity of the manuscript.

Reviewer #3 (Public Review):

The manuscript by Langmuller, Champer and colleagues reports a set of experiments and models investigating the fitness effects of transgenes in Drosophila melanogaster carrying CRISPR components to determine how useful such transgenes may be for population control. This study benefits from well-designed transgene constructs that allow the investigators to distinguish the effects of on-target and off-target Cas9 endonuclease activity, and a sophisticated maximum likelihood modeling framework that allows estimation of the fitness effects of the transgene constructs. The manuscript's major shortcoming is the absence of statistical analysis of the allele frequency data and some potentially unrealistic assumptions that went into the model.

3.a) My first recommendation is that a statistical analysis of the allele frequency data should be included in the manuscript, rather than inferring patterns solely from visual inspection of the data. Specifically, the manuscript claims that (lines 176-180): "We found Cas9_gRNAs to be the only construct that systematically decreased in frequency across all replicate cages (Figure 2). Interestingly, the allele frequency change was not consistent with fixed direct fitness costs. Instead, the construct frequency "bottomed out" in most replicates, and this occurred more quickly when the starting frequency was higher (Figure 2)." These conclusions regarding allele frequency changes should be supported by statistical analyses. What is the uncertainty surrounding the allele frequency estimates? Some indication of this uncertainty (such as error bars) could be added to Figure 2. Which of the trajectories in Figure 2 show a statistically significant change in allele frequency over the course of the experiment? Is the increase in the frequency of the no-Cas9_no-gRNA replicates significant? What support is there for the claim that the allele frequency changes "bottomed out"? Does a non-linear model fit these data significantly better than a linear trend? What is the evidence that allele frequency decreases slowed earlier "when the starting frequency was higher"? What is the evidence that "replicates 3 and 4 ... had very different frequency dynamics"? While they started at different frequencies, the slope of those two trajectories could be statistically indistinguishable. What is the authors' interpretation of the Cas9_gRNAs replicates 6 & 7 whose trajectories did not decrease?

We thank the reviewer for this detailed recommendation. We agree that our description of construct frequency dynamics solely from visual clues was indeed making too strong claims (e.g., regarding “different frequency dynamics”) without providing enough statistical support for these specific statements. We had originally thought that some readers would prefer we first provide such a qualitative description of the allele frequency trajectories, prior to going into the mathematically more rigorous (but therefore also more complicated) maximum likelihood inference of fitness costs and statistical model comparison of different selection scenarios (“full inference model” vs. “construct model” vs. “off-target model”, etc.)

In response to the reviewer’s comments, we decided to completely restructure this first part of the Results section. Specifically, we have removed our comparison of Cas9_gRNAs replicates solely based on visual clues, and also any mention of the admittedly vaguely defined “bottoming out” behavior. Instead, we now only mention the average frequency change for the Cas9_gRNAs construct across all replicates, while highlighting the heterogeneity among replicates. The maximum likelihood analysis is now introduced right after this and has also been revised extensively to improve clarity. We believe that this analysis provides a very powerful framework for the systematic inference of fitness costs and for assessing which of the different selection scenarios best explains our empirical data. This is because it combines the data from all replicates while fully accounting for the heterogeneity among them. For example, it could well be that construct frequency trajectories in individual replicates may not be statistically distinguishable from neutral evolution, yet in aggregate, an inferred fitness cost of the construct becomes highly significant. Note that the maximum likelihood framework also provides confidence intervals for its estimates, based on the entirety of the data. So the question of whether a departure from a neutral model is significant comes down to whether the 95% confidence interval surrounding the fitness estimate of the given construct still includes a value of 1 (which it does for the “direct fitness” estimate of the full model, but not for the “off-target fitness” estimate, see Table 2).

Regarding the comment about error bars for the allele frequency trajectories in Figure 2, we want to point out that our construct frequency estimates are actually based on the genotype counts of all adult flies present in the given cage experiment at the specific time point. We therefore did not include uncertainty estimates in Figure 2, nor did we include sampling noise in the maximum likelihood analysis. We have now clarified this in the caption of Figure 2 and in the Methods section (“Maximum Likelihood framework for fitness cost estimation”). We also acknowledge that we still cannot rule out sampling noise completely (for example through escaped flies, phenotyping errors, or loss of frozen flies due to destruction or other issues). However, we expect that the relative contribution of these errors should be negligible compared to drift.

The reviewer raises an interesting question: Why did the Cas9_gRNAs construct frequency not decrease in the two replicates with the highest construct starting frequency (replicate 6 and 7)? A possible explanation could be that — given a limited set of off-target sites — cut off-target alleles that impose a fitness cost will accumulate and start to independently segregate from the construct alleles very quickly in populations where the construct has a high starting frequency (and thus a higher overall rate of cleavage events). We now state this possible explanation in the section on “Construct frequency dynamics suggest moderate off-target fitness costs” of our revised manuscript.

3.b) My second recommendation involves the assumptions that went into the maximum likelihood modeling. In particular, it strikes me as unrealistic to assume that 1) the genome contains only a single off-target site that is entirely responsible for the decrease in fitness due to Cas9 activity; and 2) that the rate of off-target mutation is as high as it is assumed to be ("In individuals that carry a construct, all uncut off-target alleles are assumed to be cut in the germline, which are then passed on to offspring that could suffer negative fitness consequences."). Regarding point 1), isn't a more realistic scenario that there are multiple off-target sites, each with a potentially different fitness consequence resulting from Cas9-induced mutations? If so, doesn't the likelihood that all off-target sites have been cut depend on the number of such sites, as multiple off-target sites should reduce the mutation rate at any single site. This possibility also suggests that there may be multiple loci with potentially deleterious Cas9-induced alleles segregating within the experimental populations. Regarding point 2), even assuming only a few potential off-target sites per genome, it seems like the rate of off-target cutting would have to be unrealistically high to approach mutating all off-target sites in the population. The conversion efficiency of the constructs used here is reported as ~80% and 60% in females and males, respectively; it seems likely that the rate of Cas9 mutation at off-target sites is lower than this efficiency for the target site. These assumptions should be justified or relaxed before claiming that mutational saturation of off-target sites is responsible for a decreasing fitness loss over the course of the experiments (after confirming that there is statistical support for the claim that the allele frequency trajectories bottom out).

The reviewer raises a very important point: modeling only one off-target site that represents the net fitness effect of Cas9 cleavage outside the target region as well as a cut rate of 100 % (i.e., the off-target site is always cut in the presence of Cas9) is highly idealized.

(1) We agree with the reviewer that in reality, the experimental populations might have a polygenic off-target landscape, where the fitness of cleavage alleles could differ vastly within as well as between loci. However, given the limited number of data points (e.g., n=87 generation transitions for experimental populations with the Cas9_gRNAs construct), it would be extremely difficult if not impossible to disentangle the numerous parameters that would be necessary to describe such a more complex off-target scenario with our modeling approach. We have now highlighted our model choices, potential caveats, and resulting limitations in both the Discussion section and also the section “Construct frequency dynamics suggest moderate off-target fitness costs” in the Results.

(2) Similar to the single off-target locus, our cut rate of 100 % is an idealized assumption that was chosen with the aim to reduce model complexity. As outlined above, it would be extremely hard to disentangle the cut rate from other parameters (such as the number of target sites if fitness effects are multiplicative across loci). Additionally, we would like to point out that the reported conversion efficiencies (~80 % in males, ~60% in females) are not the conversion efficiencies of the constructs in the experimental populations shown in Figure 2, but of separate homing drives with a single gRNA. All constructs in the experimental populations are designed in a way that no homing can occur, and they have four gRNAs if any. We apologize for the confusion. Our revised manuscript contains now a paragraph in the “Cas9HF1 homing drive” section in the Results that highlights the differences between the constructs in the cage populations and the homing drives assessed in this study. Furthermore, we have added an additional figure that displays the individual results of the homing drive (Figure 5) — we hope this improves clarity.

3.c) My third suggestion involves the correspondence between the results of the likelihood modeling and the phenotypic assays. The best fit model inferred a viability loss of 26% and no detectable effects on female choice (or male attractiveness) or fecundity. In contrast, the phenotypic assays inferred no detectable effect on viability, but a 50% reduction in male attractiveness and 25% reduction in female fecundity. I think that the authors' conclusion that "[t]hese assays broadly confirmed our previous findings" needs some context or explanation as to how these numerically discrepant findings are broadly confirming, beyond the speculation that the discrepancy in viability may be due to rearing in vials vs. population cages.

We thank the reviewer for pointing this out. We removed the claim that the phenotypic assays “broadly confirmed our previous findings” and highlight now the differences in estimated fitness costs for male and females in the phenotypic assays as well as the discrepancy to our maximum likelihood estimates. Furthermore, we provide now additional explanations for what might be causing this phenomenon (i.e., single crosses vs. large populations, vial vs. cage, interactions between individual genotypes and the environment, delayed development of construct homozygotes being interpreted as reduced viability in the maximum likelihood analysis). We also point towards the discrepancies in the Discussion of our revised manuscript and recap potential explanations.

3.d) My fourth suggestion involves the comparison between the Cas9_gRNAs and Cas9HF1_gRNAs transgenes. The inference that off-target cuts are the major source of fitness loss for the Cas9_gRNAs construct relies heavily on the observation that there was no decrease in allele frequency for the two Cas9HF1_gRNAs replicates. It therefore seems critical to be confident in this observation, and to rule out alternative explanations as much as possible. For example, did the authors confirm that the Cas9HF1_gRNAs construct has on-target Cas9 activity levels as high as the Cas9_gRNAs construct? Although I am not certain about this (see comments in the next paragraph on this point), I think the transgene constructs used to estimate drive conversion rates are different from the constructs used for the population cage experiments; if this is correct, I think it would be helpful to provide the on-target mutation rates for the actual constructs used in the population cages.

The reviewer is correct: The constructs in the population cages are different to the homing gene drives for which we estimated the gene drive conversion rates. However, we were able to confirm at least one mutated gRNA target site in every PCR-based genotyped offspring of individuals carrying either the Cas9_gRNAs or the Cas9HF1_gRNAs construct (this is now specified in the manuscript). Thus, we did not expect a systematic difference in on-target mutation rates for Cas9_gRNAs, and Cas9HF1_gRNAs constructs respectively. We acknowledge in the Discussion that construct performance might substantially vary with genomic sites and even organisms.

3.e) Relatedly, I was confused about the portion of the manuscript that reports the drive conversion efficiency. The manuscript states, "As a proof-of-principle that Cas9HF1 is indeed a feasible alternative, we designed a homing drive that is identical to a previous drive (45), except that it uses Cas9HF1 instead of standard Cas9. This drive targets an artificial EGFP target locus with a single gRNA (see Methods)." Given that the rate of drive conversion was estimated by the loss of GFP, these homing drive constructs must be different from the constructs used in the population cage experiments, as those constructs targeted a site on chromosome 3L which does not contain GFP. I could not find a description of these homing constructs in the Methods - while a reader might be able to puzzle this out by reading reference #45, I think it would be helpful to explicitly describe these details in this manuscript.

We apologize for the confusion. We have highlighted the similarities (e.g., nanos promoter, DsRed) as well as the differences (e.g., number of gRNAs) between the homing drives and the constructs in the cage populations at the beginning of the section “Cas9HF1 homing drive” in the Results. We hope this makes it more clear.

Reviewer #3 (Public Review):

The manuscript by Langmuller, Champer and colleagues reports a set of experiments and models investigating the fitness effects of transgenes in Drosophila melanogaster carrying CRISPR components to determine how useful such transgenes may be for population control. This study benefits from well-designed transgene constructs that allow the investigators to distinguish the effects of on-target and off-target Cas9 endonuclease activity, and a sophisticated maximum likelihood modeling framework that allows estimation of the fitness effects of the transgene constructs. The manuscript's major shortcoming is the absence of statistical analysis of the allele frequency data and some potentially unrealistic assumptions that went into the model.

My first recommendation is that a statistical analysis of the allele frequency data should be included in the manuscript, rather than inferring patterns solely from visual inspection of the data. Specifically, the manuscript claims that (lines 176-180): "We found Cas9_gRNAs to be the only construct that systematically decreased in frequency across all replicate cages (Figure 2). Interestingly, the allele frequency change was not consistent with fixed direct fitness costs. Instead, the construct frequency "bottomed out" in most replicates, and this occurred more quickly when the starting frequency was higher (Figure 2)." These conclusions regarding allele frequency changes should be supported by statistical analyses. What is the uncertainty surrounding the allele frequency estimates? Some indication of this uncertainty (such as error bars) could be added to Figure 2. Which of the trajectories in Figure 2 show a statistically significant change in allele frequency over the course of the experiment? Is the *increase* in the frequency of the no-Cas9_no-gRNA replicates significant? What support is there for the claim that the allele frequency changes "bottomed out"? Does a non-linear model fit these data significantly better than a linear trend? What is the evidence that allele frequency decreases slowed earlier "when the starting frequency was higher"? What is the evidence that "replicates 3 and 4 ... had very different frequency dynamics"? While they started at different frequencies, the slope of those two trajectories could be statistically indistinguishable. What is the authors' interpretation of the Cas9_gRNAs replicates 6 & 7 whose trajectories did not decrease?

My second recommendation involves the assumptions that went into the maximum likelihood modeling. In particular, it strikes me as unrealistic to assume that 1) the genome contains only a single off-target site that is entirely responsible for the decrease in fitness due to Cas9 activity; and 2) that the rate of off-target mutation is as high as it is assumed to be ("In individuals that carry a construct, all uncut off-target alleles are assumed to be cut in the germline, which are then passed on to offspring that could suffer negative fitness consequences."). Regarding point 1), isn't a more realistic scenario that there are multiple off-target sites, each with a potentially different fitness consequence resulting from Cas9-induced mutations? If so, doesn't the likelihood that all off-target sites have been cut depend on the number of such sites, as multiple off-target sites should reduce the mutation rate at any single site. This possibility also suggests that there may be multiple loci with potentially deleterious Cas9-induced alleles segregating within the experimental populations. Regarding point 2), even assuming only a few potential off-target sites per genome, it seems like the rate of off-target cutting would have to be unrealistically high to approach mutating all off-target sites in the population. The conversion efficiency of the constructs used here is reported as ~80% and 60% in females and males, respectively; it seems likely that the rate of Cas9 mutation at off-target sites is lower than this efficiency for the target site. These assumptions should be justified or relaxed before claiming that mutational saturation of off-target sites is responsible for a decreasing fitness loss over the course of the experiments (after confirming that there is statistical support for the claim that the allele frequency trajectories bottom out).

My third suggestion involves the correspondence between the results of the likelihood modeling and the phenotypic assays. The best fit model inferred a viability loss of 26% and no detectable effects on female choice (or male attractiveness) or fecundity. In contrast, the phenotypic assays inferred no detectable effect on viability, but a 50% reduction in male attractiveness and 25% reduction in female fecundity. I think that the authors' conclusion that "[t]hese assays broadly confirmed our previous findings" needs some context or explanation as to how these numerically discrepant findings are broadly confirming, beyond the speculation that the discrepancy in viability may be due to rearing in vials vs. population cages.

My fourth suggestion involves the comparison between the Cas9_gRNAs and Cas9HF1_gRNAs transgenes. The inference that off-target cuts are the major source of fitness loss for the Cas9_gRNAs construct relies heavily on the observation that there was no decrease in allele frequency for the two Cas9HF1_gRNAs replicates. It therefore seems critical to be confident in this observation, and to rule out alternative explanations as much as possible. For example, did the authors confirm that the Cas9HF1_gRNAs construct has on-target Cas9 activity levels as high as the Cas9_gRNAs construct? Although I am not certain about this (see comments in the next paragraph on this point), I think the transgene constructs used to estimate drive conversion rates are different from the constructs used for the population cage experiments; if this is correct, I think it would be helpful to provide the on-target mutation rates for the actual constructs used in the population cages.

Relatedly, I was confused about the portion of the manuscript that reports the drive conversion efficiency. The manuscript states, "As a proof-of-principle that Cas9HF1 is indeed a feasible alternative, we designed a homing drive that is identical to a previous drive (45), except that it uses Cas9HF1 instead of standard Cas9. This drive targets an artificial EGFP target locus with a single gRNA (see Methods)." Given that the rate of drive conversion was estimated by the loss of GFP, these homing drive constructs must be different from the constructs used in the population cage experiments, as those constructs targeted a site on chromosome 3L which does not contain GFP. I could not find a description of these homing constructs in the Methods - while a reader might be able to puzzle this out by reading reference #45, I think it would be helpful to explicitly describe these details in this manuscript.

Author Response

Reviewer #3 (Public Review):

The primary strength of this study is in establishing the N999S heterozygous mouse as a useful model system for debilitating paroxysmal non-kinesigenic dyskinesia (PKND), with or without epilepsy. This outcome was hard-won following a comprehensive analysis of biophysical, neurophysiological, and behavioral tests. Ultimately the convincing evidence was demonstrated through a clever application of a stress-related behavioral test (quite in alignment with triggers in patients) to elicit the hypo-motility associated with PKND. Like patients who exhibit variable penetrance, even highly inbred mice exhibit much variability, and uncovering a robust phenotype took a nuanced approach and perseverance.

To reach this point, several experiments provided mechanistic insights into the mutant channel behavior. First, whole-cell patch clamp experiments revealed shifts in the G-V consistent with gain-of-function behavior previously characterized using the N999S and D434G mutants expressed heterologously. Novel observations of H444Q revealed a loss-of-function (LOF) behavior with the G-V shifted to positive potentials but to a lesser degree. These electrophysiological phenotypes establish the rank of predicted severity as N999S>D434G>H444Q.

This prediction was tested in brain slices of heterozygous animals where the mutant channels would be normally spliced and associate with WT subunits and other components such as beta subunits. The investigators evaluated BK currents by patch clamp from hippocampal neurons where BK channels are known to play key functional roles. Both N999S and D434G showed the predicted increase in current magnitude, though interestingly the differences between them apparent in heterologous expression were lost in the native setting. Curiously, no differences in BK current magnitude were observed in neurons of heterozygotes carrying the putatively LOF mutation H444Q.

In terms of seizure susceptibility, D434G mutants different from WT and less severe than N999S mutants with respect to time to evoked seizure, although differences in "EEG power" were not statistically significant between D434G and WT. These observations support the conclusion that D434G represents an intermediate disease phenotype.

The behavioral studies were the most effective in revealing differences among the variants and in defining GOF N999S heterozygotes as a compelling animal model for PKND and providing evidence that the LOF mutation conferred the opposite effect of hyperkinetic mobility. The findings provide the new insight that KCNMA is the target of heritable, monogenic disease, a conclusion that was previously not forthcoming because known human mutations have arisen de novo. The dyskinetic phenotypes in response to stress induction are wholly consistent with patient symptoms.

With respect to rigor and reproducibility, it is commendable that the investigators were blinded to genotype during data collection and analysis. Moreover, the study provides an important confirmation of previous findings from another lab regarding the cellular phenotype of the N999S mutant. WT controls were compared to transgenic littermates within individual transgenic lines. In some cases, the sample sizes were rather low (see below), but otherwise the study seems rigorous.

The strengths of the manuscript far outweighed the weaknesses. The experiments interpreted to suggest a gene dosage effect with D434G were not compelling to this reviewer and might be better documented in the supplement with the conclusion that further work is required.

Due to pandemic-related animal and lab issues, we were unable to generate and surgically implant full Kcnma1D434G/D434G homozygous cohorts for the EEG/seizure portion of the study. We focused instead on using the limited mice of this genotype for the novel PNKD3 assays (n=7), leaving the seizure dataset at n=3.

To address the concern, the Kcnma1D434G/D434G data was removed from Figure 4 to avoid overinterpretation of a gene dosage effect. However, we did retain the individual measurements within the Results text (lines 383 and 385), on the basis of facilitating direct comparisons between our study and other D434G studies. For example, even with only three measurements, the trend toward the shortest seizure latencies in Kcnma1D434G/D434G mice is similar to the result obtained with an independently generated D434G mouse model (Dong et al, 2022). Yet seizure power and the presence of spontaneous seizures do not show a similar trend, suggesting our results differ from theirs in these important aspects. This is now stated more clearly in the revised conclusion for that paragraph, ‘While not conclusive and requiring substantiation in a larger cohort, the Kcnma1D434G/D434G seizure data raise the possibility of a gene dosage effect with D434G that qualitatively differs from an independently-generated D434G mouse model (Dong et al., 2022),’ (lines 388-390).

In contrast to the seizure part of the study, the increased severity of Kcnma1D434G/D434G PNKD-immobility is fully supported by the data with sufficient statistical power (Figure 5D). However, the idea that the increased severity with homozygous D434G in PNKD-immobility was consistent with gene dosage observations for seizure was removed for consistency (lines 549-550).

As a side note, we also added additional clinical descriptors (akinesia) and colloquial descriptions for PNKD3 (‘drop attack’) to disambiguate how a PNKD3 episode appears different from other types of motor dysfunction. This was to facilitate comparison with the two other KCNMA1-D434G models (mouse and fly; Dong et al, 2022; Kratschmer et al., 2021), which report aspects of dyskinesia in the setting of baseline locomotor dysfunction. To our knowledge, these models have not been evaluated for the striking ‘drop attack’ immobility presenting in patients (lines 84-85).

The consequences of the altered BK current levels were assessed on the voltage dependence of firing frequency in the hippocampal neurons, but it was not very clear how increased BK current would enhance neuronal excitability. Also, how might it lead to the PKND phenotype? A paragraph even speculating on these mechanistic links in the Discussion would be welcome.

The mechanism for how BK currents increase action potential firing are not fully identified in this study (see also response to reviewer #2). In the Results, a new paragraph was added at the end of action potential section to summarize the AHP changes in more detail and speculate an indirect mechanism of action for the increase in BK current, predicted from a similar ‘GOF’ BK current type, where β4 regulation of BK channels is lost (lines 294-304). Additional details have also been added to the Discussion regarding the factors contributing to lower seizure threshold (lines 675-680).

Additional re-organization of Discussion text addresses the basis for PNKD. A direct statement that it is not clear yet which neurons/circuits are the most critical for PNKD-like symptomology was added, and which of these express BK channels (lines 680-700). We follow with a succinct summary of phenotypically-relevant PNKD models. While there is a lot to unpack with respect to similarities and differences between different paroxysmal dyskinesia models in the literature, they ultimately shed little light the question of KCNMA1 PNKD3-related dysfunction. With the addition of the d-amp rescue control, we focus mainly on the amphetamine response predicting a CNS locus (lines 692-693). The d-amp response may even suggest dopaminergic pathways (some of which express BK channels) as a plausible to investigate in future studies, but due to the complex interplay of d-amp dosage and the novel motor assay, we don’t think speculating on a specific circuit is supported with enough actual data to add in the Discussion.

Author Response

Reviewer #1 (Public Review):

The 2019, Johnson et al., Science study (referred to as "2019 study" or "prior study" in the rest of the comments) measured mutational robustness in F1 segregants derived from a yeast cross between a laboratory and a wine strain, which differ at >35,000 loci. To realize this, the authors developed a pipeline 1) to create the same set of transposon insertion mutations in each yeast strain via transformation; and 2) to measure the fitness effects of these specific insertion mutations.

In this manuscript, the authors applied the same pipeline to laboratory evolved yeast strains that differ in only tens or hundreds of loci and thus are much less divergent than those used in the prior study. Both studies aim to characterize how the fitness of the sets of insertion mutations (mostly deleterious) vary depending on the existing mutations (mostly beneficial) in those yeast strains. However, the current manuscript, especially when compared to the prior study, suffers from several major weaknesses.

First, only 91 genes out of >6,000 genes in the yeast genome are perturbed in the manuscript. The small set of disruption mutations is unlikely to faithfully capture the pattern of epistasis in the selected clones. By comparison, >1,000 insertion mutations were evaluated in the 2019 study. Because the majority of the >1,000 tested mutations were neutral, the authors focused on 91 insertions that had significant fitness effects. The same 91 insertion mutations are used in the current study. However, as evident in both studies, epistasis plays an important role in how insertion mutations interact with different genetic backgrounds. Considering the vastly different genetic backgrounds between clones used in the prior and current studies, the insertion mutations of interest in the current study is unlikely to be the same as those in the prior study. The large-scale genetic insertion used in the prior study is suggested to be conducted in the current study.

This concern is summarized in Essential Revision 1 above; see our comments there for our detailed response. Briefly, we have added an additional Figure Supplement (Fig. 1 – Supplement 8; see above) demonstrating that the 91 insertion mutants have a similar range of effects in this study as in the previous one (which may be expected since the genetic backgrounds here are as closely related to those in the 2019 study as the backgrounds in the 2019 study are to each other).

Second, the statistical power in the current manuscript is insufficient to support the conclusions. Fitness errors were not considered when several main conclusions were drawn (fitness errors on the y-axis of Figure 1B are not available; fitness errors on the x-axis of Figure 2 are not available). The current conclusions are invalid without knowing the magnitude of fitness error. Fitness of each clone should be measured in at least two replicates in order to infer errors of fitness measurements. Additionally, the authors isolated two clones from the same timepoint of each population and treated them as biological replicates based on the fitness correlation between the two clones. However, this practice can be problematic because the extent of fitness correlation varies across populations and it is less likely to capture the patterns of epistasis when clones are isolated from more heterogeneous populations. Similarly, the authors could avoid this bias by measuring the fitness of each clone in multiple replicates and treat the two clones from the same timepoint/population separately.

We agree that details about statistical methods, most of which are taken from Johnson et al. (2019), were not clear in our text. As we also describe in our response to the Essential Revisions above, we have rewritten a large part of the methods text to provide more details about statistical methods and have calculated and reported errors more broadly:

Errors on fitness effects: We have expanded our methods text describing how the fitness effect of a mutation is determined for a single clone / condition. This text now emphasizes the internal replication provided by redundant barcodes, which allows us to calculate a standard error for the effect of a mutation in a single clone / condition. These errors are shown in Figure 1 – Figure Supplements 1-3. We have also added details on how errors are calculated for a mutation for a population-timepoint, and these errors are now included in Figure 2.

Errors on the DFE mean: We discuss this below.

Considering clones separately: As we also describe in the essential revisions above, Johnson et al. (2021) shows that the mutational dynamics in these evolving populations are dominated by successive selective sweeps, so we expect clones isolated from the same population-timepoint to rarely differ by many mutations. However, we agree that there are likely some cases in which the two clones have important genetic differences. To address this concern, we have reanalyzed our data as you suggest, considering each clone separately. The results of this analysis are included for every main text figure in the form of figure supplements (Figure 1 - figure supplement 7, Figure 2 - figure supplement 5, Figure 3 - Figure supplement 5, and Figure 4 - figure supplement 1), which show that our qualitative conclusions are unchanged.

Reviewer #2 (Public Review):

Johnson and Desai have developed a yeast experimental-evolution system where they can insert barcoded disruptive mutations into the genome and measure their individual effect on fitness. In 2019 they published a study in Science where they did this in a set of yeast variants derived by crossing two highly diverged yeast. They found a pattern that they termed "increasing cost epistasis": insertion mutations tended to have more deleterious effects on higher fitness backgrounds. The term "increasing cost epistasis" was coined to play off the converse pattern commonly observed in experimental evolution of "diminishing returns epistasis" wherein beneficial mutations tend to have smaller effects on more fit backgrounds. Another way to think about fitness effects is in terms of robustness: when mutations tend to have little effect on phenotype, the system is said to be robust. Thus, when increasing costs epistasis is observed, it suggests that higher fitness backgrounds are less robust.

In this paper, Johnson and Desai use this same barcoded-insertions system in yeast, but here the backgrounds receiving insertions are adapting populations. More specifically, they took 6 replicate populations that evolved for 8-10k generations and inserted a panel of 91 mutations at 6 timepoints along the evolutions. They then did this entire experiment in two different environments: one in rich media at permissive temperature (YPD 30) and one in a defined media at high temperature (SC 37). Importantly, the mutations accumulating in a population over time here are driven by selection-and thus the patterns of epistasis observed here are probably more relevant to "real" evolution than the backgrounds from the 2019 paper. The overarching question, then, is whether similar patterns of epistasis is found in these long-term adaptations and across conditions as was previously observed.

The first major finding in this work is that at YPD 30 (where the yeast are presumably "happy"), the mean fitness effect does decline in most (but not all) populations as they adapt. Since the population is becoming more fit over time (relative to a constant reference type), this is consistent with the previously observed pattern of increasing cost epistasis. The strength of the effect is, however, weaker than in that previous work. The authors speculate that this may reflect the fact that far few mutations are involved here than in the previous study-giving far fewer opportunities for (mostly negative) epistatic effects. I find this explanation likely correct, although speculative.

The second major, and far more surprising, result is that in the other condition (SC 37), the insertion mutations mutations do not show a consistent trend: mean fitness effect of the insertion mutations does not change as adaptation proceeds. This is despite the fact that fitness increases in these population over time just as it did in the YPD populations. Toward the end of the paper, the authors speculate as to why this is the case. They argue that in the YPD 30 environment, selection is mainly on pure growth rate. They suggest that the growth rate depends on different components such as DNA synthesis, production of translation machinery, and cell wall synthesis. Critically, these components are non-redundant and can't "fill in" for each other. So, for example, rapid DNA synthesis is of little value if cell-wall synthesis is slow. As adaptation fixes mutations that increase the function of one of these growth components, they shift the "control coefficient" to other components. This, they argue, may be the major explanation behind increasing cost epistasis. I find the logic of their argument compelling and potentially providing great insight into developing a richer view of epistasis. Future experiments will be needed to test how well the hypothesis holds up. They then flip the argument around and suggest that in the SC 37 environment, the targets of selection are fundamentally different from those in growth-centric YPD 30 conditions. Instead, they argue, there is likely more redundancy in the components that mutations are affecting. I again find their arguments compelling.

After establishing these observed patterns for mean effects, they examine individual mutations and look at the relationship of fitness effects as a function of background fitness. The upshot of this analysis is that there are more negative correlations than positive ones (especially in the YPD 30 conditions), but also that there is a lot of variation: there are many mutations that show no correlation and a small number with a positive correlation. This casts substantial doubt on the simplistic view that for the vast majority of mutations, fitness itself causes mutations to have greater costs.

We thank the reviewer for these positive comments and the nice summary of our work.

As a minor point of criticism, a lot of statistical test are being done here and there is no attempt to address the issue of multiple testing. I would like the authors to address this. I say minor because I don't think the overarching patterns are being affected by a few false positive tests.

Related points were also raised by the other reviewer. To address this, we have added multiple-hypothesis-corrected p-values for these least-squares Wald Tests (using the Benjamini-Hochberg method) to our dataset (Supplementary File 1). As you suggest, for this particular analysis in which we compare the overall number of mutations following each pattern, we are willing to accept the possibility of false positives, so we still use the original p-values to categorize the mutations in Figure 2. We address this point in the main text and provide the numbers of mutations falling in each category after we perform this correction:

“Because we are primarily focused on comparing the frequency of each pattern across environments, we report these values before multiple-hypothesis-testing correction here and in Figure 2; after a Benjamini Hochberg multiple-hypothesis correction these values fall to 24/77 (~31%), 15/74 (~20%), 9/77 (~12%), and 11/74 (~15%), respectively.”

From here the authors turn to using a formal modeling to understand epistasis better. For each mutation, they fit the fitness data to three models: fitness-mediated model = fitness effects are explained by background fitness, idiosyncratic model = fitness effects can change at any point in an evolution when a new mutation fixes, and full model = fitness effects depend on both fitness and idiosyncratic effects.

My major criticism of the work lies here: the authors don't explain how the models work carefully and thoroughly, leaving the reader to question downstream conclusions. Typically, when models are nested (as the fitness-mediated and idiosyncratic models appear to be nested within the full model), the full model will, by definition, fit the data better than the nested models. But that is not the case here: for many mutations the idiosyncratic model explains more of the variance than the full model (e.g. Figure 3A). (Note, the fitness-mediated model never fits better than the full model). Further, when dealing with nested models in general, one should ask whether the more complex model fits the data enough better to justify accepting it over simpler model(s). There are clearly details and constraints in the models used here (and likely in the fitting process) that matter, but these are not discussed in any detail. Another frustrating part of the model fitting is that each model is fit to each mutation individually, but there is no attempt to justify this approach over one where each model is expected to explain all mutations. I'm not saying I think the authors have chosen a poor strategy in what they have done, but they have made a set of decisions about how to model the problem that carries consequences for interpretation, and they don't justify or discuss those decisions. I think this needs to be added to the paper. I think this should include both a high level, philosophy-of-our-approach section and, probably elsewhere, the details.

The reason this matters is because the authors move on to use the fitted models and the estimated coefficients from the models in discussing and interpreting the structure of epistasis. For example, they say "We find that the fitness model often explains a large amount of variance, in agreement with our earlier analysis, but the idiosyncratic model and the full model usually offer more explanatory power." Looking at Figure 3A, this certainly appears to be the case, yet that type of statement is squarely in the domain of model comparison/selection-but as explained above, this issue is not addressed. Relatedly, the authors go on to argue that "Positive and negative coefficients in the idiosyncratic model represent positive and negative epistasis between mutations that fix during evolution and our insertion mutations." I'm left wondering whether the details of the model fitting process matter. I am left asking how the idiosyncratic model would perform on data that arose, for example, under the fitness-mediated model? Or how it would perform on data originating under the full model? Is it true that when data arises under a different model (say the full model) but is fit under the idiosyncratic model, negative coefficients always represent negative epistasis and positive coefficients will always represent positive epistasis and that model misspecification does not introduce any bias? Another thing I am left wondering about concerns the number of observed coefficients in the idiosyncratic model: if one mutation shows similar effects across backgrounds, it might generate one coefficient during model fitting, while another mutation that has different effects on different backgrounds could give rise to several coefficients-is there some type of weighting that addresses the fact that individual mutations can generate different numbers of coefficients? One can imagine bias arising here if this isn't treated carefully.

One of the main conclusion that the authors reach is that the pattern of increasing cost epistasis (observed previously and here in the YPD 30 environment) may not arise from the effect of background fitness itself, but instead arise because epistatic effects tend to be negative-and the more interactions there are (with mutations accumulating over time), the more they tend to have a negative cumulative effect. I find it very likely that the authors have this major conclusion correct. By contrast, they find that at SC 37, the distribution of fitness effects is less negatively skewed-with a considerable number of coefficients estimated to be > 0. They close with a really interesting discussion exploring how these patterns likely arise from underlying biology of the cell, metabolic flux, redundancy, and selection for loss-of-function vs gain-of-function. I find a lot of this interesting and insightful. But because some of their conclusions rest squarely on the modeling, I encourage the authors to be more thorough and convincing in how they execute this aspect of the work.

Thanks for these detailed comments about the modeling approach and analysis, which raise points that were also described in the Essential Revisions and by Reviewer 1. We agree that these details were not presented sufficiently clearly in the original manuscript. In the revised manuscript, we have added a much more in-depth section on the details of the modeling procedures in the Materials and Methods, including formulas for each model and a discussion of how noise could affect our modeling results (see responses to essential revisions and reviewer 1 above for more information). This includes an analysis of shuffled and simulated datasets, which will give readers a better sense of how to interpret these modeling results. We have also included a new paragraph in the results that compares the models for each mutation and for the entire dataset using the Bayesian Information Criteria (BIC):

“We can also ask which model best explains the data using the BIC, which penalizes models based on the number of parameters. The small squares below the bars in Figure 3A indicate which model has the lowest BIC for each mutation. In YPD 30°C, the full model has the lowest BIC for 40/77 (~52%) mutations and the idiosyncratic model has the lowest BIC for 37/77 (~48%). In SC 37°C, the full model has the lowest BIC for 49/73 (~67%) mutations and the idiosyncratic model has the lowest BIC for 24/73 (~33%). When we assess how well each model fits the entire dataset in each environment, the full model has a lower BIC than the idiosyncratic model in both environments.”

We also appreciate the suggestion to look at how coefficients are spread among mutations. We have made a new supplemental figure (Figure 3 - Figure supplement 3) that clearly shows the coefficients broken down by mutation for each condition. This figure shows that coefficients are often clustered for one mutation. That is, multiple populations often have similar coefficients / patterns of epistasis for a particular mutation. We don’t view this as a source of bias in our data, but as an indication that the mutations fixing in these populations sometimes exhibit similar patterns of epistasis with these insertion mutations. We now reference this supplemental figure in the main text (“see Figure 3 – figure supplement 3 for a breakdown of coefficients by individual mutations”) as a better representation of the coefficients that result from our modeling.

Reviewer #2 (Public Review):

Johnson and Desai have developed a yeast experimental-evolution system where they can insert barcoded disruptive mutations into the genome and measure their individual effect on fitness. In 2019 they published a study in Science where they did this in a set of yeast variants derived by crossing two highly diverged yeast. They found a pattern that they termed "increasing cost epistasis": insertion mutations tended to have more deleterious effects on higher fitness backgrounds. The term "increasing cost epistasis" was coined to play off the converse pattern commonly observed in experimental evolution of "diminishing returns epistasis" wherein beneficial mutations tend to have smaller effects on more fit backgrounds. Another way to think about fitness effects is in terms of robustness: when mutations tend to have little effect on phenotype, the system is said to be robust. Thus, when increasing costs epistasis is observed, it suggests that higher fitness backgrounds are less robust.

In this paper, Johnson and Desai use this same barcoded-insertions system in yeast, but here the backgrounds receiving insertions are adapting populations. More specifically, they took 6 replicate populations that evolved for 8-10k generations and inserted a panel of 91 mutations at 6 timepoints along the evolutions. They then did this entire experiment in two different environments: one in rich media at permissive temperature (YPD 30) and one in a defined media at high temperature (SC 37). Importantly, the mutations accumulating in a population over time here are driven by selection-and thus the patterns of epistasis observed here are probably more relevant to "real" evolution than the backgrounds from the 2019 paper. The overarching question, then, is whether similar patterns of epistasis is found in these long-term adaptations and across conditions as was previously observed.

The first major finding in this work is that at YPD 30 (where the yeast are presumably "happy"), the mean fitness effect does decline in most (but not all) populations as they adapt. Since the population is becoming more fit over time (relative to a constant reference type), this is consistent with the previously observed pattern of increasing cost epistasis. The strength of the effect is, however, weaker than in that previous work. The authors speculate that this may reflect the fact that far few mutations are involved here than in the previous study-giving far fewer opportunities for (mostly negative) epistatic effects. I find this explanation likely correct, although speculative.

The second major, and far more surprising, result is that in the other condition (SC 37), the insertion mutations mutations do not show a consistent trend: mean fitness effect of the insertion mutations does not change as adaptation proceeds. This is despite the fact that fitness increases in these population over time just as it did in the YPD populations. Toward the end of the paper, the authors speculate as to why this is the case. They argue that in the YPD 30 environment, selection is mainly on pure growth rate. They suggest that the growth rate depends on different components such as DNA synthesis, production of translation machinery, and cell wall synthesis. Critically, these components are non-redundant and can't "fill in" for each other. So, for example, rapid DNA synthesis is of little value if cell-wall synthesis is slow. As adaptation fixes mutations that increase the function of one of these growth components, they shift the "control coefficient" to other components. This, they argue, may be the major explanation behind increasing cost epistasis. I find the logic of their argument compelling and potentially providing great insight into developing a richer view of epistasis. Future experiments will be needed to test how well the hypothesis holds up. They then flip the argument around and suggest that in the SC 37 environment, the targets of selection are fundamentally different from those in growth-centric YPD 30 conditions. Instead, they argue, there is likely more redundancy in the components that mutations are affecting. I again find their arguments compelling.

After establishing these observed patterns for mean effects, they examine individual mutations and look at the relationship of fitness effects as a function of background fitness. The upshot of this analysis is that there are more negative correlations than positive ones (especially in the YPD 30 conditions), but also that there is a lot of variation: there are many mutations that show no correlation and a small number with a positive correlation. This casts substantial doubt on the simplistic view that for the vast majority of mutations, fitness itself causes mutations to have greater costs. As a minor point of criticism, a lot of statistical test are being done here and there is no attempt to address the issue of multiple testing. I would like the authors to address this. I say minor because I don't think the overarching patterns are being affected by a few false positive tests.

From here the authors turn to using a formal modeling to understand epistasis better. For each mutation, they fit the fitness data to three models: fitness-mediated model = fitness effects are explained by background fitness, idiosyncratic model = fitness effects can change at any point in an evolution when a new mutation fixes, and full model = fitness effects depend on both fitness and idiosyncratic effects.

My major criticism of the work lies here: the authors don't explain how the models work carefully and thoroughly, leaving the reader to question downstream conclusions. Typically, when models are nested (as the fitness-mediated and idiosyncratic models appear to be nested within the full model), the full model will, by definition, fit the data better than the nested models. But that is not the case here: for many mutations the idiosyncratic model explains more of the variance than the full model (e.g. Figure 3A). (Note, the fitness-mediated model never fits better than the full model). Further, when dealing with nested models in general, one should ask whether the more complex model fits the data enough better to justify accepting it over simpler model(s). There are clearly details and constraints in the models used here (and likely in the fitting process) that matter, but these are not discussed in any detail. Another frustrating part of the model fitting is that each model is fit to each mutation individually, but there is no attempt to justify this approach over one where each model is expected to explain all mutations. I'm not saying I think the authors have chosen a poor strategy in what they have done, but they have made a set of decisions about how to model the problem that carries consequences for interpretation, and they don't justify or discuss those decisions. I think this needs to be added to the paper. I think this should include both a high level, philosophy-of-our-approach section and, probably elsewhere, the details.

The reason this matters is because the authors move on to use the fitted models and the estimated coefficients from the models in discussing and interpreting the structure of epistasis. For example, they say "We find that the fitness model often explains a large amount of variance, in agreement with our earlier analysis, but the idiosyncratic model and the full model usually offer more explanatory power." Looking at Figure 3A, this certainly appears to be the case, yet that type of statement is squarely in the domain of model comparison/selection-but as explained above, this issue is not addressed. Relatedly, the authors go on to argue that "Positive and negative coefficients in the idiosyncratic model represent positive and negative epistasis between mutations that fix during evolution and our insertion mutations." I'm left wondering whether the details of the model fitting process matter. I am left asking how the idiosyncratic model would perform on data that arose, for example, under the fitness-mediated model? Or how it would perform on data originating under the full model? Is it true that when data arises under a different model (say the full model) but is fit under the idiosyncratic model, negative coefficients always represent negative epistasis and positive coefficients will always represent positive epistasis and that model misspecification does not introduce any bias? Another thing I am left wondering about concerns the number of observed coefficients in the idiosyncratic model: if one mutation shows similar effects across backgrounds, it might generate one coefficient during model fitting, while another mutation that has different effects on different backgrounds could give rise to several coefficients-is there some type of weighting that addresses the fact that individual mutations can generate different numbers of coefficients? One can imagine bias arising here if this isn't treated carefully.

One of the main conclusion that the authors reach is that the pattern of increasing cost epistasis (observed previously and here in the YPD 30 environment) may not arise from the effect of background fitness itself, but instead arise because epistatic effects tend to be negative-and the more interactions there are (with mutations accumulating over time), the more they tend to have a negative cumulative effect. I find it very likely that the authors have this major conclusion correct. By contrast, they find that at SC 37, the distribution of fitness effects is less negatively skewed-with a considerable number of coefficients estimated to be > 0. They close with a really interesting discussion exploring how these patterns likely arise from underlying biology of the cell, metabolic flux, redundancy, and selection for loss-of-function vs gain-of-function. I find a lot of this interesting and insightful. But because some of their conclusions rest squarely on the modeling, I encourage the authors to be more thorough and convincing in how they execute this aspect of the work.

Reviewer #3 (Public Review):

Punishment is a key form of learning and behavior change, yet its core behavioural and brain mechanisms remain poorly understood and certainly less well understood than reward learning. This manuscript by Jacobs et al from the Moghaddam laboratory uses dual fibre photometry for calcium transients to make an important advance in understanding how punishment is learned by studying how punishment changes action and punisher coding in the PFC and VTA of rats. This work builds on the elegant single unit work from this group reported previously. The authors use a single action, probabilistic task whereby rats are first trained to nosepoke for sugar pellets on an FR1, with a 5 sec DS signalling reinforcement. Then, in blocks of 30 trials each, the nosepoke is punished on a probabilistic contingency of 0%, 6%, 10%. The authors used dual fibre photometry to concurrently record calcium transients in "dmPFC" and VTA, with a focus on transients related to action emission and punisher as well as reward delivery.

There are quite a few key findings here: 1) action transients in dmPFC change across punishment from modest inhibitory transients in 0% risk to no change (i.e possible loss of inhibitory transient in PFC) or modest positive transients (in VTA) as risk increased from 6-10%; 2) comparison with past single-unit data suggested similarity between photometry and single unit measures for the action but not DS; 3) there was no change in punisher transients in these regions; 4) diazepam which had modest behavioral effects to alleviate punishment had no effects on PFC transient to the action or punisher but did reveal peri-action ramping-like transients in VTA; 5) diazepam increased correlated activity between VTA and PFC at 0% and 6% risk

Overall, I enjoyed reading this manuscript and I learned much from it. The work builds neatly and clearly on the past work of this group in this task, providing new information on how punishment shapes action coding in the prefrontal cortex and VTA, how it shapes correlated activity between these regions, and how benzodiazepines may affect these to achieve their anxiolytic effects. The critical conclusions are that these regions are important for action, but not punisher, encoding, and that peri-action ramping in VTA neurons and VTA-PFC correlated activity contribute to the anxiolytic effects of benzodiazepines in this task.

Comments

1. I think it is worth drawing the distinction between punishment (i.e. learning and performance) versus the punisher (footshock). For example, the title (and across the manuscript) refers to "punishment coding" to mean transients to the punisher itself. I would suggest using "punisher" when referring to the outcome used (footshock) or its associated transients and "punishment" when referring to learning. So, learning punishment involves changes in action but not punisher encoding in these regions.

2. "dmPFC". Different researchers mean different things by this term. Would it be possible to state exactly where the fibres were instead (e.g., Laubach et al., eNeuro, 2018)?

3. I did struggle to understand the functional significance of the PFC transients. I am convinced they are real and robust because we see precisely the same in our own unpublished work. But, I am still puzzled as to what a loss of an 'inhibitory' transient around the punished action in PFC means? This is not really addressed but it is the main effect of punishment on action coding in the PFC and I think some readers would appreciate the author's interpretation of this.

4. Related to 3, it was also not clear why these PFC transients differed only at 6% risk and not also 10% risk. Again, I think this is worth discussing.

5. Re: analyses. I thought these were generally well done. There are two questions one might be interested in. The first is whether the transients are different from 0%. The second is whether transients differ across sessions. The figures do a good job at answering the second question (which to me is the most important question) by using coloured bars above transients to show when session differences are present as assessed by a robust analysis. However, I do think some readers would also appreciate knowing whether and when transients themselves were significantly < or > 0%. Perhaps these figures could be presented as supplementary data.

6. The comparison with previously published single-unit data was very interesting. Here I was persuaded that these correlations were meaningful because of the difference between these correlations for cue and action. I am not suggesting the authors do the following, I only offer it for their consideration in future work. Kriegeskorte has developed ways of assessing dissimilarity in different data types from the same behavioural designs that could prove very helpful and persuasive here (e.g., Front. Syst. Neurosci., 24 November 2008; https://doi.org/10.3389/neuro.06.004.2008).

7. The authors comment on the overgeneralisation of punishment learning. That is, in session 1 there is a broad suppression of behavior by punishment that was not obviously present in the remaining sessions. I am not sure overgeneralisation is the best term because this implies punishment learning generalised. More likely is that Pavlovian fear was present in session 1 to generally suppress nosepoking and this fear was reduced in the remaining sessions as the instrumental punishment contingency was learned. Bolles made this point some years ago and it may be worth citing Bolles et al. Learning and Motivation Volume 11, Issue 1, February 1980, Pages 78-96, on this point.

Author Response

Reviewer #2 (Public Review):

This manuscript from Shi, Ballesta, and Padoa-Schioppa examines the relationship between neural activity in the monkey orbitofrontal cortex (OFC) and various choice patterns that arise in sequential (versus simultaneous) choice. This approach addresses a central question in the study of decision-making: how can one identify value-dependent versus value-independent effects on choice behavior when value is defined from that behavior itself? Here, the authors document three behavioral differences in sequential choice: choosers are nosier, show an order bias, and show a preference bias. Leveraging a conceptual computational framework for OFC activity that the authors have developed over many years, the authors link reduced accuracy to changes in neural valuation in the OFC, order effects to post-valuation decision activity in the OFC, and preference effects to extra-OFC processes. For decision neuroscientists, these findings show specific differences between sequential and simultaneous choice, and suggest the integration of multiple stages (valuation, decision, and post-decision) in the selection process. More broadly, this work shows how an examination of neural activity can shed light on aspects of the decision process that cannot be distinguished by an examination of behavior alone.

Strengths:

Overall, this paper presents a novel and thoughtful task design that allows comparison of neural and behavioral value and choice effects. In concert with an established circuit-based framework for parsing different types of OFC response patterns, the authors test and validate a number of hypotheses on the link between neural activity and choice.

(1) Comparing sequential and simultaneous choice tasks in an interleaved manner is a clever approach to separate valuation and comparison processes in time. While not entirely novel (e.g. see work from the Hayden group), the combination of this approach with the OFC response pattern (offer value, chosen value, chosen juice) framework allows a distinction between valuation and comparison-related effects.

(2) This paper is the latest in a significant series of related papers on orbitofrontal activity from this group, and cleverly utilizes their expertise in characterizing, analyzing, and conceptualizing different patterns of OFC activity. In addition to the long-established offer value/chosen value/chosen juice categorization, recent papers from this group have established the causal contribution of OFC offer value activity to economic choice and established similar OFC neural contributions to sequential and simultaneous choice tasks.

(3) Apart from a causal test (e.g. cell type specific stimulation) of the contribution of different neural responses to different choice effects, the next strongest evidence is a demonstration of a consistent relationship across sessions. The authors show such a relationship between offer value coding strength and choice accuracy, between chosen value sequence effects and behavioral order bias, and between chosen juice inhibition and order bias. At the least, these relatively strong effects show a strong correlation between different OFC responses and behavior.

Thank you for emphasizing these points.

Weaknesses:

While the experimental approach and rigor of the analyses are strengths, there are issues of interpretation and generality of analytical approaches that should be clarified.

(1) The abstract, introduction, and discussion touch on canonical behavioral economic choice effects as a prelude to the behavioral effects documented here, but it's not clear they are so closely related. [A] Many of the effects in the cited literature (framing effects in risky choice, preference reversals, etc.) are robust across different task paradigms, whereas the effects shown here arise specifically from a comparison of choice across different task paradigms (sequential vs. simultaneous). Furthermore, [B] it's not clear that the term "bias" adequately captures the array of effects in the behavioral economic literature (for that matter, [C] one of the main effects in this paper is reduced choice accuracy rather than a bias). [D] The paper would benefit from a clearer conceptual linkage between documented behavioral biases (particularly in humans) and the effects shown here.

[B] We beg to differ. In our reading of the literature, the term “bias” is very general and it is invoked practically every time choices present some effect that seems idiosyncratic or “irrational”. The list of documented biases is very long – a good reference is the Wikipedia page on cognitive biases (for more scholarly references, see (Gilovich et al., 2002; Kahneman et al., 1982)).

[A] As for whether biases documented in behavioral economics are robust across task paradigms, that’s really matter of perspectives. For example, we all understand the phenomenon of loss aversion (a.k.a. “status quo bias”) to be very robust and almost intuitive. But before the prospect theory paper of Kahneman and Tversky (1979), that was not at all the case. In the 15 years following that paper, much of what Kahneman and Tversky did was to show how loss aversion affected choices in different domains (Kahneman and Tversky, 2000). Other biases are much less reliable. For example, there is an extensive literature on decoy effects – i.e., violations of the axiom of “independence of irrelevant alternatives”. However, it turns out that the strength and even the direction of decoy effects depend on seemingly minor details (Spektor et al., 2021). In other words, decoy effects are not as robust as one might think. As for the biases dicussed here, our hunch is that the order bias is quite ubiquitous. Indeed, it was already documented using different tasks in different species (Krajbich et al., 2010; Rustichini et al., 2021). The preference bias might also be the manifestation of a rather general phenomenon. Afterall, there is a common intuition that when a decision is difficult we sometimes fail to finalize it, and eventually choose some default option. In conclusion, we think of the two biases discussed here as conceptually very comparable to biases described in behavioral economics.

[C] We agree that the drop in accuracy is (strictly speaking) not a choice bias, and we carefully chose the title and wrote the whole manuscript to keep that point clear. However, let us note that the drop in accuracy observed under sequential offers could easily be construed as a choice bias – specifically, a bias favoring in any situation the lesser option (lower value). As we conclude the present study, this phenomenon continues to fascinate us. Indeed, while it is clear that the behavioral effect arises at the valuation stage, we still don’t understand why the activity range of offer value cells is reduced under sequential offers. Naively, one might have guessed the opposite – i.e., that when only one offer is on display, the lack of competition translates to stronger offer value signals. We plan to give this issue more thought in the future. One possibility is that the system modulates the activity range of offer value cells depending on the task and/or the behavioral context. If so, differences in choice accuracy measured under sequential versus simultaneous offers would be a manifestation of a more general phenomenon. Of course, this matter remains open for future research.

[D] The link between the biases discussed here and other biases described in the literature is conceptual. The main point we want to make is this: Over the past 20 years, we have gained some understanding of the neural circuit and mechanisms underlying simple economic choices. While our understanding remains incomplete and object of ongoing research, notions acquired for simple choices can be used to make sense of a broader class of choices. Thus, in principle at least, it is possible to shed light on a variety of traits and biases by observing the activity of particular cell groups. The last paragraph of the ms conveys this point.

(2) The analyses rely on a particular quantification of choice behavior (probit regression), which interprets choice effects (e.g. relative valuation of the two juices, sigmoid steepness) via specific parameter combinations and relies on specific assumptions about the construction of choice (e.g. cumulative normal distribution, constant sigmoid slope across order effects). This method of quantifying choice behavior is well-documented in previous studies, allowing a comparison to past work. However, given the importance of this approach to both quantifying choice effects and comparing choice to OFC responses, the paper would benefit from directly addressing two issues: (1) how well does probit regression actually capture stochastic choice behavior (in both Task 1 and Task 2), and (2) do the findings rely on specific choice modeling assumptions? The second issue is most important for the order bias effects, which assume a constant sigmoid across conditions - do the authors reach similar conclusions if this assumption is relaxed?

Thanks for raising this question. We address it more thoroughly below (under “Recommendations for the authors”, point (2)). In a nutshell, when we designed the behavioral analysis, we chose the probit function and the log value ratio model (as opposed to the value difference model) based on general considerations and for consistency with our previous studies. We now conducted a series of control analyses using logit instead of probit and value difference instead of log value ratio. We also repeated all the analyses of neuronal activity using measures for relative value, choice accuracy and order bias derived from these behavioral models. The upshot is that all of our results hold true independently of the regression model used to analyze choices. Thus we kept the results as in the original ms, and we included a new section in the Methods to describe our control analyses (p.16-17).

(3) There are some issues with the strength and interpretation of the preference bias that need to be addressed. Re: strength and significance of the preference bias, the text seems to overemphasize the dependence of the effect on relative value (rotation of the rho-2 vs rho-1 ellipse) at the cost of the simple task difference (shift in the ellipse above the identity line). Conceptually, a preference bias (an shift in relative value towards the favored item) requires only the task difference, not the dependence on relative value. It would be clearer for example if the main text (pg. 6) presented the statistics (t-test, Wilcoxon) supporting the difference in relative values (rhos) between Tasks 1 and 2. Furthermore, the rotation does not seem as robust: the text states that the result is significant in both animals (p<0.04) but the ANCOVA results (Fig 3C and 3F) suggests that the effect is only significant in Monkey J. Is the preference effect significant only in one animal, and if so, is the effect significant across the combined data?

Let us refer to Fig.3C. There is no question that the separation between the red and blue lines is statistically significant (order bias). In addition, the two lines appear (a) displaced upwards and (b) rotated counterclockwise compared to the identity line. In our understanding, the question raised by R2 is whether the two effects – displacement (a) and rotation (b) – are both present and both necessary to define the preference bias. We actually gave this issue extensive thought early on, and we concluded that displacement and rotation are not easily dissociable, at least in our data set. The reason is simple: to dissociate them, we would have to make some assumption about the center of rotation. For example, if we assume that the center of rotation is [0, 0], then there clearly is a rotation but the displacement is close to zero. Conversely, if the center of rotation is [1, 1] (which, in some ways, is a more logical assumption), the rotation is still there but the displacement is >0. When we considered these elements, we realized that any choice of a center of rotation would be somewhat arbitrary. Further complicating things, once a center of rotation is chosen, rotation and displacement are non-commutative operations. Importantly, this issue only affects the displacement, meaning that the rotation angle (and its statistical significance) does not depend on choosing any particular center of rotation. In this light, we chose to define the preference bias in a way that is more tight to the rotation than to the displacement, while noting that the net effect of the phenomenon was to bias choices in favor of the preferred juice (hence, the phrase “preference bias”). The only problem with this definition is that it doesn’t do full justice to the phenomenon in monkey G (Fig.3F), where the displacement is more clearly evident than the rotation (indeed, the latter only trends towards statistical significance (p=0.07)). Still, we don’t see a better way to design our analyses. Thus we kept the ms unchanged in this respect.

(4) On a related note, the authors present and view the effects as detrimental for the animals, but I think they have to more explicitly state how they are defining outcomes. For example, the abstract states "By neuronal measures, each phenomenon reduced the value obtained on average in each trial and was thus costly to the monkey". Does this mean that outcomes are less valuable, with value defined by (offer value cell) firing rates? A clarification is particularly important for the preference bias, where animals show a stronger bias for the preferred option compared to simultaneous choice. At the behavioral level, this effect seems to only be a poorer outcome if one assumes that simultaneous choice demonstrates true values - can it not be assumed that sequential choice demonstrates true preference, and the preference bias reduces performance in simultaneous choice? The authors may have an explanation in mind based on OFC value coding, and it would be helpful to be explicit here.

Thank you for raising this question. The revised ms includes a new section (Discussion; ‘The cost of choice biases’; p.13) that discusses this important issue. In a nutshell, if in two conditions subjective values are the same but choices are different, in one or both conditions the subject fails to choose the higher value. In that sense, the choice bias is detrimental. Our analyses of neuronal activity indicated that subjective offer values were (a) the same in the two tasks and (b) independent of the presentation offer in Task 2. Hence, both the preference bias and the order bias were detrimental to the animal.

(5) Finally, at a broad level, the authors rigorously define and test hypotheses about how the different behavioral effects relate to OFC activity within the context of their neurocomputational framework (offer value, chosen value, chosen juice cells arranged in a competitive inhibition network; Fig. 1). However, it should be acknowledged that the primary conclusions - about how the different behavioral effects arise during valuation, comparison, or post-comparison - relies on the assumption that the different OFC response patterns reflect these specific circuit functions, and that OFC is causally related to choice. It would be more balanced if the authors could acknowledge this point in the discussion, and discuss any relevant potential alternative explanations for their findings.

This issue is addressed above (Essential revision, point 1). In essence, R2 is correct: all our analyses were designed, and all our results are interpreted, under a series of assumptions. Most of these are backed by empirical evidence (e.g., showing that the encoding of decision variables in OFC is categorical in nature). However, one assumption remains a working hypothesis. Specifically, we assume that the cell groups identified in OFC constitute the building blocks of a decision circuit. If so, the activity of different cell groups may be associated with different computational stages. We edited the Discussion to clarify this point (p.11-12). As for possible alternative explanations, we agree that it is a very reasonable question to ask, but we honestly are at a loss addressing it. Indeed, one would never conduct the analyses presented in this ms if not in the framework of Fig.1. Consequently, it is hard to come up with any interpretation for the results without embracing that computational framework. If R2 can propose some alternative interpretation for the results presented in the ms, we would be more than happy to think about it, and possibly revise our thinking.

Author Response

Reviewer #1 (Public Review):

Overall, this study is well designed with convincing experimental data. The following critiques should be considered:

1) It is important to examine whether the phenotype of METTL18 KO is mediated through change with RPL3 methylation. The functional link between METTL18 and RPL3 methylation on regulating translation elongation need to be examined in details.

We truly thank the reviewer for the suggestion. Accordingly, we set up experiments combined with hybrid in vitro translation (Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) and the Renilla–firefly luciferase fusion reporter system (Kisly et al. NAR 2021) (see Figure 5A).

To test the impact of RPL3 methylation on translation directly, we purified ribosomes from METTL18 KO cells or naïve HEK293T cells supplemented with ribosome-depleted rabbit reticulocyte lysate (RRL) and then conducted an in vitro translation assay (i.e., hybrid translation, Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) (see figure above and Figure 5A). Indeed, we observed that removal of the ribosomes from RRL decreased protein synthesis in vitro and that the addition of ribosomes from HEK293T cells efficiently recovered the activity (see Figure 5 — figure supplement 1A).

To test the effect on Tyr codon elongation, we harnessed the fusion of Renilla and firefly luciferases; this system allows us to detect the delay/promotion of downstream firefly luciferase synthesis compared to upstream Renilla luciferase and thus to focus on elongation affected by the sequence inserted between the two luciferases (Kisly et al. NAR 2021) (see figure above and Figure 5A). For better detection of the effects on Tyr codons, we used the repeat of the codon (×39, the number was due to cloning constraints in our hands). We note that the insertion of Tyr codon repeats reduced the elongation rate (or processivity), as we observed a reduced slope of downstream Fluc synthesis (see Figure 5 — figure supplement 1B).

Using this setup, we observed that, compared to ribosomes from naïve cells, RPL3 methylation-deficient ribosomes led to faster elongation at Tyr repeats (see Figure 5B). These data, which are directly reflected by the ribosomes possessing unmethylated RPL3, provided solid evidence of a link between RPL3 methylation and translation elongation at Tyr codons.

2) The obvious discrepancy between the recent NAR an this study lies in the ribosomal profiling results (such as Fig.S5). The cell line specific regulation between HAP1 (previously used in NAR) vs 293T cell used here ( in this study) needs to be explored. For example, would METLL18 KO in HAP1 cells cause polysome profiling difference in this study? Some of negative findings in this study (such as Fig.S3B, Fig.S5A) would need some kind of positive control to make sure that the assay condition would be working.

According to the reviewer’s suggestion, we conducted polysome profiling of the HAP1 cells with METTL18 knockout. For this assay, we used the same cell line (HAP1 METTL18 KO, 2-nt del.) as in the earlier NAR paper. As shown in Figure 9 — figure supplement 2A and 2B, we observed reduced polysomes in this cell line, as observed in the NAR paper.

We did not find the abundance of 40S and 60S by assessing the rRNAs and the complex mass in the sucrose gradient (see Figure 9 — figure supplement 2C-E) by METTL18 KO in HAP1 cells. This observation was again consistent with earlier reports.

Overall, our experiments in sucrose density gradient (polysome and 40S/60S ratio) were congruent with NAR paper. A difference from our finding in HEK293T cells was the limited effect on polysome formation by METTL18 deletion (Figure 4 — figure supplement 1A and 1B). To further provide a careful control for this observation, we induced a 60S biogenesis delay, as requested by the Reviewer. Here, we treated cells with siRNA targeting RPL17, which is needed for proper 60S assembly (Wang et al. RNA 2015). The quantification of SDG showed a reduction of 60S (see figure below and Figure 3 — figure supplement 1D-F) and polysomes (see Figure 4 — figure supplement 1C and 1D), highlighting the weaker effects of METTL18 depletion on 60S and polysome formation in HEK293T cells. We note that all the sucrose density gradient experiments were repeated 3 times, quantified, and statistically tested.

To further assess the difference between our data and those in the earlier NAR paper, we also performed ribosome profiling on 3 independent KO lines in HAP1 cells, including the one used in the NAR paper (METTL18 KO, 2-nt del.). Indeed, all METTL18 KO HAP1 cells showed a reduction in footprints on Tyr codons, as observed in HEK293 cells (see Figure 4H), and thus, there was a consistent effect of RPL3 methylation on elongation irrespective of the cell type. On the other hand, we could not find such a trend (see figure below) by reanalysis of the published data (Małecki et al. NAR 2021).

Thus far, we could not find the origin of the difference in ribosome profiling compared to the earlier paper. Culture conditions or other conditions may affect the data. Given that, we amended the discussion to cover the potential of context/situation-dependent effects on RPL3 methylation.

3) For loss-of-function studies of METLL18, it will be beneficial to have a second sgRNA to KO METLL18 to solidify the conclusion.

We thank the reviewer for the constructive suggestion. Instead of screening additional METTL18 KO in HEK293T cells, we conducted additional ribosome profiling experiments in HAP1 cells with 3 independent KO lines. In addition to ensuring reproducibility, these experiments should assess whether our results are specific to the HEK293T cells that we mainly used. As mentioned above, even in the different cell lines, we observed faster elongation of the Tyr codon by METTL18 deficiency.

4) In addition to loss-of-function studies for METLL18, gain-of-function studies for METLL18 would be helpful for making this study more convincing.

Again, we thank the reviewer for the constructive suggestion. To address this issue, we conducted RiboTag-IP and subsequent ribosome profiling. Here, we expressed Cterminal FLAG-tagged RPL3 of its WT and His245Ala mutant, in which METTL18 could not add methylation (Figure 2A), in HEK293T cells, treated the lysate with RNase, immunoprecipitated FLAG-tagged ribosomes, and then prepared a ribosome profiling library (see figure below, left). This experiment assessed the translation driven by the tagged ribosomes. Indeed, we observed that, compared to the difference in Tyr codon elongation in METTL18 KO vs. naïve cells, His245Ala provided weaker impacts (see figure below, right). Given that METTL18 KO provides unmodified His, the enhanced Tyr elongation may be mediated by the bare His but not by Ala in that position. Since this point may be beyond the scope of this study, we omitted it from the manuscript. However, we are happy to add the data to the supplementary figures if requested.

Reviewer #3 (Public Review):

In this article, Matsuura-Suzuki et al provided strong evidence that the mammalian protein METTL18 methylates a histidine residue in the ribosomal protein RPL3 using a combination of Click chemistry, quantitative mass spectrometry, and in vitro methylation assays. They showed that METTL18 was associated with early sucrose gradient fractions prior to the 40S peak on a polysome profile and interpreted that as evidence that RPL3 is modified early in the 60S subunit biogenesis pathway. They performed cryo-EM of ribosomes from a METTL18-knockout strain, and show that the methyl group on the histidine present in published cryo-EM data was missing in their new cryo-EM structure. The missing methyl group gave minor changes in the residue conformation, in keeping with the minor effects observed on translation. They performed ribosome profiling to determine what is being translated efficiently in cells with and without METTL18, and found decreased enrichment of Tyrosine codons in the A site of ribosomes from cells lacking METTL18. They further showed that longer ribosome footprints corresponding to sequences within ribosomes that have already bound to A-site tRNA contained less Tyrosine codons in the A site when lacking METTL18. This suggests methylation normally slows down elongation after tRNA loading but prior to EF-2 dissociation. They hypothesize that this decreased rate affects protein folding and follow up with fluorescence microscopy to show that EGFP aggregated more readily in cells lacking METTL18, suggesting that translation elongation slow down mediated by METTL18 leads to enhanced folding. Finally, they performed SILAC on aggregated proteins to confirm that more tyrosine was incorporated into protein aggregates from cells lacking METTL18.

The article is interesting and uses a large number of different techniques to present evidence that histidine methylation of RPL3 leads to decreased elongation rates at Tyrosine codons, allowing time for effective protein folding.

We thank the reviewer for the positive comments.

I agree with the interpretation of the results, although I do have minor concerns:

1) The magnitude of each effect observed by ribosome profiling is very small, which is not unusual for ribosome modifications or methylation. Methylation seems to occur on all ribosomes in the cell since the modification is present in several cryo-EM structures. The authors suggest that the modification occurs during biogenesis prior to folding and being inaccessible to METTL18, so it is unlikely to be removed. For that reason, I do not think it is warranted to claim that this is an example of a ribosome code, or translation tuning. Those terms would indicate regulated modifications that come on and off of proteins, but the authors have not presented evidence that the activity is regulated (and don't really need to for this paper to be impactful).

We thank the reviewer for making this point, and we agree that the nuance of the wording may not fit our results. We amended the corresponding sentences to avoid using the terms “ribosome code” and “translation tuning” throughout the manuscript.

2) In Figure 4-supplement 1, it appears there are slightly more 80S less 60S in the METTL18 knockout with no change in 40S. It might be normal variability in this cell type, but quantitation of the peaks from 2 or more experiments is needed to make the claim that ribosome biogenesis is unaffected by METTL18 deletion. Likewise, the authors need to quantitate the area under the curve for 40S and 60S levels from several replicates and show an average -/+ error for figure 3, supplement 1 because that result is essential to claim that ribosome biogenesis is unaffected.

Accordingly, we repeated all the sucrose density gradient experiments 3 times, quantified the data, and statistically tested the results. Even in the quantification, we could not find a significant change in either the 40S or 60S levels by METTL18 deletion in HEK293T cells (see Figure 3 — figure supplement 1B and 1C).

Moreover, for the positive control of 60S biogenesis delay, we treated cells with siRNA targeting RPL17, which is needed for proper 60S assembly (Wang et al. RNA 2015). The quantification of SDG showed a reduction in 60S (see figure below and Figure 3 — figure supplement 1D-F) and polysomes (see Figure 4 — figure supplement 1C and 1D), highlighting the weaker effects of METTL18 depletion on 60S and polysome formation.

3) The effect of methylation could be any step after accommodation of tRNA in the A site and before dissociation of EF-2, including peptidyl transfer. More evidence is needed for claiming strongly that methylation slows translocation specifically. This could be followed up in vitro in a new study.

We truly thank the reviewer for the suggestion. Accordingly, we set up experiments combined with hybrid in vitro translation (Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) and the Renilla–firefly luciferase fusion reporter system (Kisly et al. NAR 2021) (see Figure 5A).

To test the impact of RPL3 methylation on translation directly, we purified ribosomes from METTL18 KO cells or naïve HEK293T cells supplemented with ribosome-depleted rabbit reticulocyte lysate (RRL) and then conducted an in vitro translation assay (i.e., hybrid translation, Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) (see figure above and Figure 5A). Indeed, we observed that removal of the ribosomes from RRL decreased protein synthesis in vitro and that the addition of ribosomes from HEK293T cells efficiently recovered the activity (see Figure 5 — figure supplement 1A).

To test the effect on Tyr codon elongation, we harnessed the fusion of Renilla and firefly luciferases; this system allows us to detect the delay/promotion of downstream firefly luciferase synthesis compared to upstream Renilla luciferase and thus to focus on elongation affected by the sequence inserted between the two luciferases (Kisly et al. NAR 2021) (see figure above and Figure 5A). For better detection of the effects on Tyr codons, we used the repeat of the codon (×39, the number was due to cloning constraints in our hands). We note that the insertion of Tyr codon repeats reduced the elongation rate (or processivity), as we observed a reduced slope of downstream Fluc synthesis (see Figure 5 — figure supplement 1B).

Using this setup, we observed that, compared to ribosomes from naïve cells, RPL3 methylation-deficient ribosomes led to faster elongation at Tyr repeats (see Figure 5B). These data, which are directly reflected by the ribosomes possessing unmethylated RPL3, provided solid evidence of a link between RPL3 methylation and translation elongation at Tyr codons.

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Reply to the reviewers

General Statements [optional]

We are grateful for the very kind, thoughtful, and detailed comments of the reviewers, which we have strived to fully integrate into the revised manuscript.

Of note are the concerns with the data from stages S21 and S22, which we acknowledge do appear to be qualitatively and quantitatively distinct from the other samples. While we are unable to completely disambiguate meaningful biological variation from technical or experimental noise using our data, we hope a few additional analyses and visualization tools we have included can provide greater confidence in the reliability of our findings.

Additionally, while attempting to evaluate Reviewer #2’s suggestions about examining the distribution of intergenic peaks along the genome, we discovered an error in our code that resulted in the improper assignment of peak categories. The error resulted in the improper assignment of intronic and exonic peaks as intergenic peaks. While the largest group of peaks in our dataset remains distal intergenic peaks (30.2%), and distal intergenic peaks remain a larger proportion of our intergenic peaks than proximal intergenic peaks, many of the peaks originally assigned to the intergenic categories have been reclassified as exonic or intronic peaks. We have updated our code and figures upon reanalysis of our data and have revised our findings and discussion accordingly.

Description of the planned revisions

Reviewer #3, Comment #3 of 11_

“In general, I thought that the bioinformatic methods (i.e., the code or the options used for each program) would have been helpful for my understanding in some cases. The authors say that these will be published on an accompanying GitHub repository, which should be fine if this is sufficient for journal policy.”_

We are still at work compiling the code for our analyses into a more reader-friendly form and setting up a GitHub repository to enable easy access to more detailed methods for interested readers. Some of the most important settings have been included in the Methods and Supplementary Methods sections, but we hope to include more thorough detailing of our pipelines in the GitHub repository. The raw data for portions of the RNA-Seq and all of the ATAC-Seq data have been uploaded to the Sequence Read Archive, and we are finalizing additional raw data submission. We are also in the process of determining what data to include in our Gene Expression Omnibus submission, which we hope to include all pertinent final data analysis files as well as any intermediate or accompanying datasets which would facilitate downstream analyses. The large size and number of our final analysis files has resulted in some challenges with data transfer and storage, which has delayed the upload and submission process.

We are also collating several of the data visualization scripts built for this manuscript into a Jupyter notebook. This tool will enable the visualization of ImpulseDE2 models and peak classifications for arbitrary genes and genome regions of a user’s choice, alongside additional functions which are discussed in this revision plan.

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

We have addressed the following substantive concerns with the manuscript:

Reviewer #2, Comment #2 of 3:_

“Authors have repeatedly used S21 and S22 throughout the manuscript to support their claims with clustering etc. May authors shed some light on the differences in replicates for these timepoints. Furthermore, I could not find Fig 3J, perhaps author would like to point out Fig 3H.”_

Reviewer #3, Cross-comment #2 of 3:_

“Focus on stages S21/S22: This might indeed be somewhat problematic. The libraries from these two stages (particularly S21) seem to be very different from those from the other stages. In the PCA (Fig. 1C), S21 doesn't cluster well with anything, and the difference between the two replicates is massive compared to other stages. The accessibility pattern (Fig. 1D) also looks odd. The libraries also have the lowest scores for % of mapped reads (Fig. S2B), fragment size distribution (S2E), and Spearman correlation (S2I). All this could be biologically sound and be due to a major developmental transition at this point, but maybe it justifies revisiting the data and testing whether leaving out S21 (and/or S22) makes a big difference for the clustering analyses.”_

1. Reviewers #2 and #3 discussed concerns with the outlying nature of libraries S21 and S22. We had also previously held concerns about these samples and had performed some analyses to examine whether the global properties of our dataset are dramatically changed upon removing those samples. We did not observe dramatic changes to the structure of our data in the absence of the S21/S22 samples.

   • a. Samples S21 and S22 appear to be highly separated from the rest of our data using Principal Components Analysis. We had also previously believed that this suggested that these samples might be problematic. However, a colleague indicated to us that researchers in microbiome ecology had observed similar phenomena, often caused by strong single axes of variation (or “linear gradients”) in the datasets. In “Uncovering the Horseshoe Effect in Microbial Analyses” (mSystems, 2017) by Morton et al., the authors describe how a strong linear gradient can create a “horseshoe effect” or “Guttman effect”, where PCA results in the two ends of a linear gradient appearing to come together in ordinal space. The authors also describe a similar “arch effect” which strongly resembles the general shape of our PCA curve. We suggest that the strong apparent “outlier” appearance of S21 and S22 may be exaggerated or induced by the technical “arch effect” phenomenon, and may be caused by a strong single biological gradient – a developmental timecourse – which our data aimed to capture.
   • b. We also performed PCA on our dataset with the S21 and S22 time points removed prior to performing the analysis (see right panel, bottom). When we did so, we observed that the relative positions of the remaining libraries remains largely similar, with time points closer to the middle of development showing a positive loading in PC2, and time points closer to the beginning and end of development showing a negative loading. This suggests that the second major axis of variation in our dataset would remain a contrast between middle vs. terminal timepoints, even without the S21/S22 data, and that the relative positioning of the remaining data within PC-space is not entirely driven by S21/S22.
   • c. To further assess the degree of the S21/S22 samples’ outlying effects, we also performed ImpulseDE2 analysis to generate model fits without S21/S22 data. Doing so allowed us to determine to what degree the S21/S22 stages are necessary for driving the accessibility trajectory of individual peaks, and of the data more broadly. We performed IDE2 with either all data, or the S21/S22 data removed prior to input into IDE2. This generated two sets of model fits to the “cloud” of accessibility vs. time measurements: one that included the S21/S22 data, and one without. We evaluated, for each peak in our dataset, the time point at which the IDE2 model achieved maximum accessibility (the “IDE2 max fit”), and plotted both the “all” and “noS21S22” data as a histogram (see right panel, top graph). The presence of peaks that achieve predicted maximum accessibility in the S21/S22 stages in the “no S21/S22” data is a result of how we calculate “max fit”, which does not require that there is a known accessibility value at a given timepoint; only that the time point during which the model fit is maximum is closest to the timing of that developmental stage. Overall, we still observed early, middle, and late enrichment of IDE2 max fit even when the S21/S22 data are removed. We do see a rightward shift in the middle timepoint histogram in the direction of later stages, although this may be expected given the absence of concrete accessibility values at S21/S22 in the “no S21/S22” data. This indicates that our data globally retain the general trends of early, middle, and late enrichment of accessibility in the absence of the S21/S22 data. Moreover, this suggests that, even without the S21/S22 data, the remaining data from early and late stages result in a model fit that still predicts maximum accessibility at middle developmental stages for many peaks.
   • d. To further measure the influence of the S21/S22 data in IDE2 model fit, we also evaluated the degree of change in the global behavior of a peak when the S21/S22 stages were removed. This analysis aimed to assess whether removing S21/S22 data resulted in an IDE2 model with the same general trajectory as with all data, as opposed to the more stringent requirement of evaluating whether the exact developmental stage of the peak was changed. To perform this analysis, we grouped developmental stages into five quintiles, each representing three stages of development. We asked, for each peak in our dataset, whether that peak’s IDE2 max fit was “stable” when the S21/S22 data were removed; that is, if the quintile of the IDE2 max fit was altered when the S21/S22 data were removed (i.e. if a peak moved more than 3 developmental stages away from its original position), a peak was considered “unstable”. We observed that over 80% of peaks in each quintile remained “stable” after removing the S21/S22 data, suggesting that the vast majority peaks show the same general trajectory of accessibility even without the S21/S22 data. Peaks within the middle time points appeared to be more unstable than peaks at the terminal timepoints, which could be expected given that the S21/S22 timepoints constituted the middle-most timepoints in our dataset.

We acknowledge that the S21/S22 timepoints still appear to be qualitatively different in other ways. Moreover, we acknowledge that some of the peaks in our dataset are “dependent” on the S21/S22 stages, given that their accessibility trajectory changes when these stages are removed. It is difficult to determine whether a change in accessibility trajectory for a given peak caused by the removal of S21/S22 data is indicative of technical differences in sample preparation, such as batch effects; biological variation, such as a potentially unknown mutant or sick embryo; or due to genuine wildtype biological processes that occur at the S21/S22 stages.

These caveats acknowledged, a comparative analysis of the data in the absence of the S21/S22 stages suggests that much of the global picture of development remains the same. In the interest of providing the data we generated as a resource, we decided to include the S21/S22 data in the final manuscript we have prepared for submission.

We have included an additional supplementary figure (Supp. Fig. 2.2) highlighting these further analyses, which we hope future readers will consider when performing their own analyses with these timepoints, as well as a summary of the ways we evaluated this potential concern in the Supplementary Methods. To facilitate future users of this dataset, we will include the model parameters calculated from IDE2 using both the full dataset and the data with S21/S22 removed in the GEO accession data, as well as a Jupyter notebook (ParhyaleATACExplorer.ipynb) that allows users to plot the raw accessibility data and IDE2 model fits for individual peaks of interest (C, example on right panel), so that downstream experiments can consider the potential differences with the S21/S22 samples.

Reviewer #2, Comment #3:_

“The majority of ATAC-seq peaks in the distal intergenic regions is a very surprising result. Authors defend this result by suggesting that this organism has big genome. May author perform a short analysis that shows that these peaks are indeed represent nearby genes or may point towards 3D genome organisation. For example, I see that this genome might have regions in the genomes that are densely organised in gene clusters, in those cases does the pattern remains same i.e he majority of the genes are very distant from each other and hence use vital regulatory elements?”_

Reviewer #3, Cross-comment #3 of 3:_

Peaks in distal intergenic regions: I agree that this could be elaborated on. It might also be that >10 kb is not actually that distal for Parhyale. I would suggest to split the "distal peaks" further (e.g., in 10 kb or 2-log steps, or whatever makes most sense) and try to understand if >10 kb is mostly <20 kb, or if most of them are hundreds of kb from the nearest gene?_

1. Reviewers #2 and #3 expressed interest in understanding the absolute distribution of distal intergenic peak distances from nearby genes in our dataset. In generating the analyses to address this question, we stumbled upon an error in our code that reveals that the true number of intergenic peaks is much lower than we had originally reported. We discuss the nature of the error below. Moreover, we address the previous question using the new data, which overall still indicates that distal intergenic peaks remain a large portion of the Parhyale genome.
   • a. To address Reviewer #2’s comments with respect to the presence of potential clusters of intergenic regions, we built a Python tool (included in ParhyaleATACExplorer.ipynb) enabling the visualization of different cis-regulatory element categories along a genomic coordinate. Upon plotting our data with this tool, we observed problems with the categorization of the peaks – namely, that intronic and exonic peaks were erroneously classified as intergenic peaks (see right panel, top). We analyzed our script for classifying annotations more carefully and realized that we had erroneously used “bedtools closest” instead of “bedtools intersect” to try to identify all peaks overlapping with gene annotations in our genome. We corrected this error and observed the expected distribution and categories of peaks in our data (right panel, bottom).
   • b. The revised peak categories have been added to the updated manuscript in Fig. 3H and Fig. 5C. The categories of peaks we observed differ substantially from our previous results, in that we observe a much higher representation of exonic and intronic peaks in our dataset, with intronic peaks now representing 28.2% of all peaks (increased from <1%), and distal intergenic peaks representing 30.2% (decreased from 51.2%). While distal intergenic peaks remain the largest category over time, the proportion is relatively equal to the fraction of intronic peaks. Intergenic peaks (distal and proximal combined) now make up only a slightly larger fraction of peaks (37.2%) than gene body peaks (exon, intron; total 34.4%). This updated result is a significant departure from our previous report, and we have updated the text of the manuscript to correct this mistake.-
   • c. While intergenic and distal intergenic peaks constitute a much smaller portion of our data, we still wanted to address Reviewer #2 and #3’s questions about the distribution of distances between intergenic peaks and nearby genes. We generated a plot to illustrate the number of intergenic peaks at variable distances to the nearest gene (B, right panel). As illustrated in the plot, there are a very large number of distal intergenic peaks, including many peaks >100kb away from the nearest gene. The average distance of intergenic peaks from the nearest gene was 73,351bp. We neglected to mention in the original manuscript that one of the rationales for choosing a 10kb cutoff as “distal intergenic” was that peaks beyond this distance would be considerably more difficult to isolate as single fragments combined with a proximal promoter using PCR, agnostic of their orientation with respect to the promoter element. Such peaks could not have been easily identified using previous transgenic approaches, and are thus distinguished from “proximal” peaks by their necessary identification using techniques such as ATAC-Seq. We have updated the text to reflect this distinction.
   • d. Given that both intergenic and gene body peaks appeared to comprise large fractions of our revised data, we also examined the relative enrichment of intergenic and gene body peaks with respect to time (after normalizing for the fraction of “unknown” peaks, as suggested by Reviewer #3). We observed that the proportion of peaks belonging to intergenic and promoter regions declined slightly as development progressed, while the proportion of gene body peaks increased (E, below). There appeared to be slightly more intergenic peaks than gene body peaks at all developmental time points, and the ratio of intergenic peaks to gene body peaks declined very slightly over time (F, below). These data indicate that intergenic and gene body peaks have different enrichment trajectories over time. As development progresses, gene body peaks are increasingly enriched, and may have a greater impact on gene regulation. We have added these additional observations to the text and to a new Supplementary Figure 2.3.

We have also addressed the following textual and conceptual concerns with the manuscript:

Reviewer #3, Comment #1 of 11_

I felt that the first paragraph of the introduction is not necessary._

1. We believe the introductory paragraph helps frame the paper in the context of the broader scope of advances in technologies for emerging research organisms – currently, it has become straightforward to both generate a genome sequence and to identify and manipulate coding genes of interest across diverse taxa, but the identification of gene regulatory mechanisms remains more difficult. We have edited the introduction to better reflect this perspective and to link the first paragraph to the rest of the paper.

Reviewer #2, Comment #1 of 3_

“In Introductory paragraph 2, sentence one, authors suggest that gene regulation plays more important role in evolutionary process than genes. Although a significant amount of research has been dedicated to gene regulation based evolution still this field is in nascent form. For example evidence of inheritance of the gene regulation pattern across generation is scarce and requires more evidence. I suggest authors to modulate the claim that still gene based evolution is the main paradigm instead otherwise.”_

Reviewer #3, Cross-comment #1 of 3_

Evolution via gene regulation vs. coding sequence: While (to my understanding) it is largely accepted in the field that changes to the CDS will often have more deleterious effects than changes to the expression of a gene, I agree that this could be elaborated on a bit.

1. As requested by Reviewers #2 and #3, we have clarified the language surrounding the debate between gene functional and gene regulatory evolution to indicate that both mechanisms appear to be important for evolutionary processes, with the importance of the latter more recently revealed.

Reviewer #3, Comment #2 of 11_

Use of Genrich: I presume this was run on both duplicates simultaneously? This is not clear from the methods section. It might have implications for downstream analyses (e.g., differential accessibility between time points) because running on both sequencing library replicates simultaneously leads to a single "replicate" of peaks per time point, while running it individually leads to two. However, I have never tested if this actually does make a difference. Maybe the authors have and can comment on this?

1. In response to Reviewer #3’s inquiry about Genrich, we have added additional clarifying information into the Methods section. “Genrich analysis was run on both duplicate libraries simultaneously; Genrich performs peak calling on each peak individually, and then merges the p-values of the replicates using Fisher’s method to generate a q-value, obviating the need to calculate an Irreproducible Discovery Rate (IDR).” We did not test running Genrich on individual libraries, opting for the more conservative approach of using the combined q-value as a filtering score for peak quality. For further information, the reviewer can see the Genrich Github repository section here: < [https://github.com/jsh58/Genrich#multiple-replicates]

Reviewer #3, Comment #4 of 11_

The section on the IDE2 models (the paragraph at the end of page 4/beginning of page 5) was unclear to me but appears sound. (The only instance where I didn't quite understand what the program actually does.) Maybe this can be explained a bit easier?_

1. As requested by Reviewer #3, we have attempted to explain the methods and logic of using ImpulseDE2 a bit more clearly:

“To identify regions of dynamically accessible chromatin, we used the ImpulseDE2 (IDE2) pipeline (Fischer et al., 2018). IDE2 differs from other software for differential expression analysis in that it allows the investigation of trajectories of dynamic expression over large numbers of timepoints. It does so by modeling a gene expression trajectory as an “impulse” function that is the product of two sigmoid functions (Chechik and Koller, 2009; Yosef and Regev, 2011). This approach enables the modeling of a trajectory of gene expression in three parts: an initial value, a peak value, and a steady state value, thus summarizing an expression trajectory using a fixed number of parameters. With the ability to capture the differences between early, middle, and late expression values for each gene in a dataset, IDE2 also enables the detection of transient changes in gene expression or accessibility during a time course. Identifying differential expression over large numbers of timepoints is difficult for more categorical differential expression software such as edgeR and DESeq2, which generally use pairwise comparisons between timepoints to assess change over time (Love et al., 2014; Robinson et al., 2010).”

Reviewer #2, Comment #2 of 3_

2-2) Authors have repeatedly used S21 and S22 throughout the manuscript to support their claims with clustering etc. May authors shed some light on the differences in replicates for these timepoints. Furthermore, I could not find Fig 3J, perhaps author would like to point out Fig 3H.

Reviewer #3, Comment #5 of 11_

On page 7, Fig.3J needs changing to 3H. This figure should, in my opinion, also contain the absolute number of peaks for each time point to set the individual proportions into context.

1. As requested by Reviewer #3, we have added a bar charts representing the number of peaks found at each time point (Fig. 3H) and the number of peaks found in each cluster (Fig. 5C) to the peak type proportion plots. We have also fixed references to Fig. 3J to instead refer to Fig. 3H – we apologize for the confusion.

Reviewer #3, Comment #6 of 11_

Last paragraph of the "Improving the Parhyale genome annotation" section: I think this needs to focus on those regions of the genome for which the location is known - after all, the "unknown" regions" could all be "distal transgenic", which would significantly change the relative proportions._

1. We have revised our analysis of this topic with our updated peak type proportions, as described above in point 2d above under “substantive concerns”.

Reviewer #3, Comment #7 of 11_

“On page 9, t-SNE is mentioned but doesn't seem to be cited.”

1. As requested by Reviewer #3, we have added citations for the t-SNE method, as well as scikit-learn, the software we used for t-SNE visualization.

Reviewer #3, Comment #8 of 11_

“The third paragraph on page 9 ("We evaluated the differences...") should mention the fact that clusters 1 and 2 are the only ones with significant proportions of exonic and intronic peaks. In the accompanying figure (5C), the total number of peaks would again be helpful.”_

1. After identifying the error in our peak category classification pipeline, this observation was no longer true. However, upon examining the new distributions by cluster, we observed that in Clusters 3–7, for which we observed GO enrichment for developmental processes, there appeared to be slightly higher enrichment of intronic regulatory elements than distal intergenic regulatory elements. These results resemble the observation from recent work showing that tissue-specific enhancers are enriched in intronic regions in various human cell types (e.g. Borsari et al. 2021, Genome Research). We have noted this new observation in the text.

Reviewer #3, Comment #9 of 11_

In figure 5D, I can't quite make out at which stage the dip in the peak of Cluster 8 occurs. This is quite an unusual pattern of accessibility change, and I can't help but wonder if it has something to do with the quality of one of the libraries? Also, the fact that half of the peaks fall into unmapped regions of the genome is unusual, and I feel this deserves more discussion._

1. In Figure 5D, Reviewer #3 asks about a dip in accessibility for Cluster 8 peaks. The dip in accessibility was actually observed for Cluster 9 peaks and is marked by the asterisk in that panel. We have updated the figure legend to clarify the significance of the asterisk and have referred readers to examine Supp. Fig. 5.1B, where the IDE2 model fits more clearly show a collective dip in accessibility for Cluster 9 peaks. Upon examining the size distribution of the clusters, we have also noticed that Cluster 8 is the smallest cluster. We have noted the small cluster size and high “unknown” peak enrichment for Cluster 8 in the text.

Reviewer #3, Comment #10 of 11_

“On page 10, the abbreviation PFM appears, but it is only explained in the legend of Fig.4. This should appear in the text.”_

1. Reviewer #3 mentions that on page 10, we use the abbreviation for position frequency matrices (PFMs) without previous reference. We first introduce the abbreviation on page 8, but given the repeated use of “PFM” on page 10, we have added an additional explanation of the abbreviation on page 10, for ease of reading.

Reviewer #3, Comment #11 of 11_

“The section on "Concordant and discordant expression and accessibility" is the one I disagree most with. The authors seem to suggest that a repressive cis-regulatory module should become less accessible when the gene is activated. However, they leave trans-acting factors completely out of their conceptualisation here. It is in general likely the availability of transcription factors that leads to repression, while the "silencer" can be well accessible in all cells. Moreover, it has become clear in recent years that CRMs are not just repressors or enhancers per se but can act as either depending on the availability of transcription factors. I think these facts could partially explain the weak correlation and should be discussed.”_

1. We appreciate the comments from Reviewer #3, which alerted us to the more recent literature around the bifunctional potential of regulatory elements. We have revised our claims to clarify that concordance and discordance analysis cannot be used to directly assign “enhancer” or “silencer” identity to given regulatory elements. Instead, we suggest that evaluating concordance and discordance can be useful for downstream users of our data, such as those aiming to build reporter constructs for a given gene of interest. To facilitate such tool development, we have built additional functions into a Jupyter notebook to enable the visualization of accessibility, gene expression, fold change of accessibility and gene expression, significance of fold change, and concordance/discordance assignment for arbitrary peak-gene pairs. An example of this visualization is shown on the following page. Panel A shows the region around the Engrailed-1 and Engrailed-2 loci in Parhyale (text labels within the plot region were added manually in Illustrator). Panel B shows visualization of the En1 promoter peak alongside En1 expression. Significant log fold changes (DESeq2 padj < 0.05) are marked by asterisks in the bar plots, and concordance/discordance assignment at each time point is indicated by the color of the comparison text (red = concordant, blue = discordant). Panels C and D show accessibility and expression visualization for a single peak (En1 peak5) compared to two nearby genes (En1 and En2). We hope to include sufficient documentation in our GitHub repository such that using these tools is accessible for most researchers, even with limited programming knowledge.

Description of analyses that authors prefer not to carry out

We were unable to easily visualize the distribution of regulatory elements across the whole genome as suggested by Reviewer #2. One challenge of working with the Parhyale genome is the lack of complete chromosomes. The genome is distributed across ~290,000 contigs of variable size. We were unable to find any software that could be easily and quickly set up to visualize our data, although we will provide in a Jupyter notebook the tools for local visualization of peak types that we developed.

That is the key issue

I think everyone rushes to find out their purpose in life but I think it's fine not to know. You'll get there eventually in life. My purpose in life has always been to be a good person and I realized that purpose a long time ago while I was in a bad place in life. Your purpose doesn't have to be the same as anyone else's. It's simply yours and you choose what to make of it.

What I think may have been surprising here is that the captured text is not the same as what would be copied to the clipboard. When <mark>copying to the clipboard, <mark style="background-color: #8000314f">new lines in the source</mark> get <mark style="background-color:#00800030">replaced with spaces</mark>, and <br> tags get converted to new lines</mark>. </br> <mark>Browser specifications distinguish <mark style="background-color: #00800036">the original text content of HTML "in the source"</mark> as returned by <mark style="background-color: #00800036"/>element.textContent</mark> from <mark style="background-color: #ffa500a1">the text content "as rendered" returned by element.innerText.</mark></mark> Hypothesis has always captured quotes from and searched for quotes in the "source" text content rather than the "rendered" text.

Dispositivo avanzado para la época, pudo predecir de forma general el funcionamiento de la web hoy en día, aun así ni siquiera se ha igualado ese nivel de pensamiento, puesto que el Memex planteaba una forma de imitar procesos neuronales complejos de organización y asociación.

Herald: menelaus had disappeared don't make me taint good news with bad

         there was a storm and boats crashed but we were spared, they may be alive but they will think we are dead just as we think they are dead

          wait for Menelauss's return because Zeus favors him

.

we won, troys' triumphant and subdued are like oil and water the triumphant revel in it, the subdued weep and toil

if we don't desecrate troys' shrines we'll be fine but if our people do it'll be bad

we all have cause to celebrate

Summary of Tucker's televised evening talk show.

Author Response

Reviewer #3 (Public Review):

The import of soluble precursor proteins into the mitochondrial matrix is a complex process that involves two membranes, multiple protein interactions with the translocating substrate, and distinct forms of energetic input. The traditional approaches for in vitro measurement of protein translocation across membranes typically involve radiography or immunodetection-based assays. These end-point approaches, however, often lack optimal resolution to analyze the sequential processes of protein transport. Therefore, the development of techniques to dissect the kinetic steps of this process will be of great interest to the field of protein trafficking.

This study by Ford et al. employs a novel bioluminescence-based technique to analyze the import of presequence-containing precursors (PCPs) into the mitochondrial matrix in real time. As a follow-up study to previous work from the Collinson group (Pereira et al. 2019), this approach makes use of the split NanoLuc luciferase enzyme strategy, whereby mitochondria are isolated from yeast expressing matrix localized 'LgBiT' (encoded by the mt-S11 gene) and used for import experiments with purified PCPs containing 'SmBiT' (the 11-residue pep86 sequence). The light intensity that results from the high-affinity interaction of pep86 with mt-S11 is convincingly shown in this study to be a reliable reporter of protein import into the matrix space. Therefore, from a technical stance, this appears to be a very promising approach for making high-resolution measurements of the different kinetic steps of protein translocation.

The authors leverage this technology to seek insights into several features of mitochondrial protein import, with some observations challenging key longstanding paradigms in the field. Using series of PCP constructs differing in length and placement of the pep86 peptide, the authors perform luminescence-based import tests with varying protein concentration, energetic input, and presequence charge distribution. Fits to the time course data suggest two main kinetic steps that govern matrix-directed import: transit of the PCP across the TOM complex into the IMS and association of the PCP with the TIM23 motor complex. The results support some very interesting insights into TIM23-mediated protein import, including: that precursor accumulation is strongly dependent on length; that the kinetically limiting step of IM transport is engagement with the TIM23 complex, not transmembrane transport itself; and that presequence charge distribution differently affects import rate and matrix accumulation. The results of this study appear repeatable among samples and the mathematical fits to time courses are well explained. However, there remain some questions about the nature of the experimental approach and the interpretation of the kinetics data in terms of the underlying biological processes. These questions are as follows:

Major points

Overall system characterization and mathematical analysis

1) The Western-based characterization of the amount of matrix-localized 11S (shown in Figure 1 - figure supplement 1) shows that the concentration of 11S varies significantly (> twofold concentration difference, quantified as a ratio to Tom40) among yeast/mitochondria preps. Is there a particular reason for this large variability? Perhaps more significantly, the import efficiency (judged by luminescence amplitude) shows high batch variability as well (> twofold efficiency difference). While this series of experiments makes the case that the luminescence readout of import is not limited by matrix-localized 11S, it does raise a potential concern of batch-to-batch variation in import competence. Could this have any implications for the reproducibility of results by this assay, particularly regarding the kinetic parameters reported?

It is very difficult to know what causes this variability as it can be seen even between triplicate preparations carried out on the same day. It could be due to slight differences in the flasks used to grow cells (such as the size of the baffles). However, we have determined that the variability in 11S concentration does not correlate with import competence (Figure 1 – figure supplement 1C), and that the kinetics of import are not affected (Figure 1 – figure supplement 2C).

2) My understanding from the Pereira 2019 JMB paper is that the yeast expressing the matrix-targeted 11S were engineered so that the 11S construct contained a 35 residue presequence from ATP1. In Figure 1 - figure supplement 1, panel A, it looks like the mitochondria-derived 11S constructs are significantly larger than the purified 11S constructs used to calibrate concentration. If the added residues on the mitochondrial 11S constitute a presequence, then they should be cleaved up on import to yield the mature sized protein. Why are the mitochondrial 11S constructs so much larger than the purified ones? Explicit labeling of MW markers would be useful here.

We noted that it seemed likely that the presequence was not getting cleaved off. There may also be some kind of SDS-PAGE mobility issues for 11S (common for beta-barrels), such that the purified version has a different mobility to the matrix localised version. Therefore, the possibility remains that the MTS is cleaved off, but the mature product migrates anomalously on gels. For this reason we carried out experiments to show that 11S is matrix localised, which turned out to be the case (Figure 1 – figure supplement 1D). So irrespective non-MTS cleavage, or unexpected gel mobility of correctly processed 11S, the reporter is where it should be – in the matrix. These points are elaborated in the text.

Labels have been added to molecular weight markers, as requested.

3) From Figure 1D, given that the amplitude linearly increases with added Acp1pep86 up to ~45 nM, this suggests that matrix-localized 11S is in stoichiometric excess of imported peptide within this range of added substrate. Given a matrix [11S] of 2.8 uM, a stoichiometrically equivalent amount of Acp1-pep86 would be equivalent to an import of <0.5% of added substrate, and it is suggested that import efficiency is actually much lower than that. How can this very low import efficiency be explained?

Import is single turnover under our assay conditions and is therefore limited by the number of import sites rather than matrix [11S]. Under standard conditions, we intentionally add substrate in vast excess and only anticipate that a very small proportion will be imported.

4) Apropos of point #3 above: Given the low efficiency of import observed for the purified PCP substrates in this study, one wonders if this due to the formation of off-pathway (translocation incompetent) precursors established during the import reaction, before substrates have a chance to engage OM receptors (e.g., due to aggregation, etc.) In this case, the interpretation of single-turnover conditions may instead be caused by a vast majority of PCP losing translocation competence, rather than the requirement for energetic resetting that is suggested. Might this be a possibility?

We anticipate that some PCP will aggregate and add substrate in excess to allow for that. Our interpretation of the reaction as single turnover was drawn from a comparison of PCP-pep86-DHFR import amplitude in the presence versus absence of MTX, rather than amplitudes from absolute amounts of PCP. We cannot think of a reason why MTX would affect protein solubility.

5) Import time courses in many cases show a progressive drop in luminescence at later time points after a maximum value has been reached. This reduction in signal cannot be accounted for by the two rate constants in the equation used in two-step kinetic model. How were such luminescence deviations accounted for when fitting data to obtain these kinetics parameters? What might be the reason for this downward drift in signal once maximum amplitude has been reached?

We almost always see this gradual drop in luminescence in both the mitochondrial and bacterial systems. The data points acquired after the amplitude are excluded for the fitting. The assay is based on an enzymatic reaction and we think that the downward drift is due to a combination of substrate depletion and accumulation of reaction products.

Import kinetics: dependence on total protein size

6) In Figure 3 - figure supplement 1, some of the kinetic parameters from the PCP concentration-dependent responses are quite noisy. For instance, responses for the shortest constructs (L and DL) show a lot of variability in the k1 and k2 parameters. Is this (partly) due to difficulty in resolving these two parameters during the nonlinear least-squares fitting protocol for these particular constructs?

It is difficult to resolve k1 and k2 perfectly, so the numbers are only estimates.

7) The data in Figure 3, panels E and F (derived from Figure 3 - figure supplement 1) in some cases show non-linear dependence of kinetic parameters on the 'N to pep86 distance' for the length (panel E) and position (panel F) variants. For instance, from the length series, the k1 mean goes from 132 to 385 to 237 nM for the DL, DDL, and DDDL constructs, respectively. The variances suggest that these differences are real. Is there a reason that kinetic parameters would have such non-monotonic dependence on length?

We don’t know the reason for this variance, but it could be investigated in future studies.

Import kinetics: dependence on energetic input

8) The data of Figure 4A show the results of partial dissipation of the membrane potential by 10 nM valinomycin. Most studies designed to cause a gradual dissipation of membrane potential do so by protonophore (e.g., CCCP) titration. Given that matrix-directed import is completely blocked by low micromolar amounts of this potent ionophore, it would be useful to have an independent readout (e.g., TMRM measurements) of the residual membrane potential that exists upon treatment with the lower concentrations of valinomycin used here.

We have now included data that shows the partial effect of 10 nM valinomycin on membrane potential (TMRM measurements) and protein import (Figure 4 – figure supplement 1A-B).

9) The step associated with k1, designated as transport across the TOM complex, is suggested to go to completion before starting the step associated with k2, engagement of the TIM23 complex. The k1 step shows a strong dependence on membrane potential (Fig. 4A, middle), particularly for the length series. Why would this be, given that no part of translocation across the OM should be associated with a valinomycin-sensitive electric potential?

This effect is relatively small and mainly affects shorter PCPs. Our interpretation is that passage of the PCP through TOM is reversible, and committing PCP to import across the IMM (which requires ∆ψ) prevents this reversibility. However, it is also possible that transport through TOM and TIM23 are partially coupled. Both these possibilities are discussed in the discussion.

Working model

10) One of the most surprising outcomes of this study is that passive transport of substrates across the TOM complex and energy-coupled transport via the TIM23 complex are kinetically separable and independent events. As the authors note in the Discussion, the current paradigm of the field is that matrix-targeted substrates concurrently traverse the OM and IM via the TIM-TIM23 supercomplex, and this model is supported by quite a bit of experimental evidence. Even in this study, the fact that the PCP-pep86-DHFR construct exposes the pep86 sequence to the matrix in the presence of MTX (Figure 2) is evidence of a two membrane-spanning intermediate. Key mechanistic questions arise regarding the model proposed in this study. For example, if PCPs traverse the TOM complex as a stand-alone step, what is the driving force (e.g., a simple pathway of protein interactions with increasing affinity)? And would soluble, matrix-directed substrates be expected to accumulate in the very restricted space of the IMS? If so, how would TIM23directed membrane proteins keep from aggregating in the aqueous IMS? These questions would be worth addressing in the discussion of the model.

We have included a discussion of the experimental evidence for TOM-TIM23 supercomplexes. The acid chain hypothesis has been proposed as the driving force for PCP transport though TOM ‒ an interaction between positive charges of the presequence and negatively charged residues within the TOM40 channel. Proteins that are targeted to the IMS are imported through TOM without the participation of TIM23 and we think that matrix-targeted proteins can do the same. This could explain why TOM is in excess over TIM23. We also think that some matrix-targeted PCPs can accumulate in the IMS, although this may not be true of membrane proteins.

Import kinetics: dependence on MTS charge distribution

11) The fact that import rates are increased with a more electropositive presequence makes sense in terms of the electrophoretic pull exerted on the PCP (matrix, negative). However, the greater accumulation of precursors containing more electronegative presequences remains puzzling. In the manuscript, this is explained based on the concept that accumulation of positive charges will cause partial collapse the membrane potential. However, I am still uncertain about this explanation for a few reasons. First, for each PCP, the presequence will constitute just a small fraction of the total length of the precursor, and therefore contribute a small fraction of the total charge density of imported protein. Would such a small change in total PCP charge be expected to have the dramatic effect observed among samples?

The majority of the total PCP charge is from the mature region, and whilst the positive charges in the presequence undoubtedly deplete ∆ψ, the differences in extent of ∆ψ depletion that we see between PCPs that vary in charge, is due to the difference in charge of the mature regions (as their presequences are identical).

Second, given the small amount of protein imported under these conditions, would the total charge of imported PCPs be expected to affect transmembrane ion distribution so significantly? For instance, as I recall, it takes up to micromolar amounts of mitochondria-targeted lipophilic cations (e.g., TPP+) to cause a major change in the TMRM-detected membrane potential.

The effect was indeed unexpected. Despite the seemingly small number of PCPs that are imported, the total number of charged residues will be much greater.

Finally, I would expect isolated mitochondria to be capable of respiratory control. It is well known, for example, that isolated mitochondria can respond to temporary draw-down of the membrane potential (e.g., by ADP/Pi addition) by going into state 3 respiration and restoring membrane gradients. Why would that not be the case here (Figure 5D)?

The isolated mitochondria that we used for the import assays demonstrate increased O2 consumption in response to ADP addition, as expected (Figure 5 – figure supplement 1A-B). In addition to this new figure, we have now included TMRM data (Figure 6 – figure supplement 2B) that shows a depletion of ∆ψ in response to ADP addition, that is temporary and dependent on the amount of ADP added. We are therefore confident that our isolated mitochondria are capable of respiratory control as expected. We think that the lack of restoration of ∆ψ, following import-induced dissipation, is a consequence of the import process in vitro. Perhaps the import process compromises the channel resulting in concomitant ion/ charge dissipation during the active process. Moreover, this is likely to be exacerbated in vitro upon acute exposure to PCP, causing a sudden saturation of the import sites – thereby compromising the ∆ψ and the mitochondria’s ability to rapidly recover (this possibility has been noted in the MS).

General

12) Although the spectral approach in this study is developed as an alternative to the more traditional import assays, it would be useful to have some control import tests (done with Westerns or autoradiography) as complements to the luminescence-based imports. For example, control tests to accompany Figure 1 that show import efficiency or tests that accompany Figure 3 to show import of the different length and position series constructs. Perhaps this could be done with immunodetection of Acp1 or the pep86 epitope, showing protease-protected, processed import substrates that appear in a membrane potential/ATP-dependent manner. Even if the results from the more traditional techniques ran contrary to the results using the NanoLuc system, this would still allow the authors to compare which effects are consistent and which are dissimilar between different approaches.

We have now included a Western blot import assay for the PCP-pep86-DHFR substrate and show that import is ∆ψ-dependent (Figure 2 ‒ figure supplement 1).

13) The authors might also consider conducting imports with mitoplasts as a way to test the kinetic model that includes the TIM23-mediated step alone.

We conducted import assays with mitoplasts and have now included this as a main Figure 5.

14) It is difficult to follow the logic in the Discussion regarding the number of TIM23 sites limiting the number of 11S imported into mitochondria in live cells (page 15, lines 23-27). Are the authors suggesting that in vivo, one TIM23 complex serves to transport a single protein? This needs to be clarified.

This has been removed, and this section of the discussion has been clarified.

Author Response

Reviewer #1 (Public Review):

The paper is very well written, the question is interesting, and the analyses are innovative. However, I do have concerns about the overall approach. My main concern is about looking at asymmetries in the low dimensional representation of connectivity. A secondary concern has to do with looking at the parcellated connectome. I explain these concerns in succession below.

We thank the Reviewer for the appreciation of our work and the insightful comments, which we have addressed below. The page numbers are corresponding to the clean version of the manuscript.

The first concern is to me quite a fundamental issue: looking at connectivity in a low dimensional space, that of the laplacian eigenvectors. There are two issues with this. The first one, which is less important than the second, is that the authors have a reference embedding to which they align other embeddings using a procrustes method with no scaling. While the 3D embedding is still optimally representing the connectivity (because distances don't change under rotations), we can no longer look at one axis at a time, which is what the authors do when they look at G1. In this case, G1 is representative of the connectivity of the reference matrix (LL), but not the others.

But even if the authors only projected their matrices onto a single G1 dimension with no procrustes (and only sign flipping if necessary), there is still a major issue. One implicit assumption of this whole approach is that if there is a change in connectivity somewhere in the original matrix, the same "nodes" of the matrix will change in the embedding. This is not the case. Any change in the original matrix, even if it is a single edge, will affect the positions of all the nodes in the embedding. That is because the embedding optimises a global loss function, not a local one.

To make this point clear, consider the following toy example. Say we have 4 brain regions A,B,C,D. Let us say that we have the following connectivity:

In the Left Hemisphere: A-B-C-D

In the Right Hemisphere: A-B=C-D

So the connection between B and C is twice as strong in the right hemi, and everything else remains the same.

The low dimensional embedding of both will look like this:

Left: ... A ... B ....... C ... D ...

Right A... ... ... B ... C ... ... ... D

Note how B,C are closer to each other in the RIGHT, but also that A,D have moved away from each other because the eigenvector has to have norm 1.

So if we were to calculate an asymmetry index, we would say that:

A is higher on the LEFT

B is higher on the RIGHT

C is higher on the LEFT

D is higher on the RIGHT

So we have found asymmetry in all of our regions. But in fact the only thing that has changed is the connection between B and C.

This illustrates the danger of using a global optimisation procedure (like low-dim embedding) to analyse and interpret local changes. One has to be very careful.

We thank the Reviewer for the detailed description of the first concern. We agree that low-dimensional embeddings describe global embedding of local features, rather than local phenomena. Moreover, we indeed assume that the connectivity embedding of a given node gives us information about its position along ‘gradients’ relative to other nodes and their respective embedding. Thus, indeed, when a single node (node X) has a different connectivity profile in the right hemisphere relative to the left, this will also have some impact on the embeddings of all nodes showing a relevant (i.e., top 10%) connection to node X.

To evaluate whether asymmetry could be observed in average connectivity within functional networks, an alternative approach to measure asymmetry was taken by computing average connectivity within different functional networks. Following we compared the within-network connectivity between left and right. We have now added this conceptual analysis to our results robustness analysis section. In short, we observed that transmodal networks (DMN, FPN, and language network) showed higher connectivity in the left hemisphere but other networks showed higher connectivity in the right hemisphere. Thus, this indicates that observations made with respect to asymmetry of functional gradients are similar to those observed for within-network functional asymmetry between the left and right hemispheres. We have now detailed the outcome of this analysis in our Result section and Supplementary Materials.

Results, p.14.: “As low-dimensional embedding is a global approach to summarize functional connectivity we reiterated our analysis by evaluating asymmetry of within network functional connectivity in the current sample. Observations made with respect to asymmetry of functional gradients are similar to those observed for within-network functional asymmetry between the left and right hemispheres.”

“To further explore functional connectivity asymmetry between left and right hemispheres, we calculated the LL within network FC and RR within network FC (Figure 2-figure supplement 5). It showed that connections in the left hemisphere and right hemisphere were relatively equal in the global scale. However, for the local differences, networks showed significant subtle leftward or rightward asymmetry (vis1: t = -5.203, P < 0.001; vis2: t = -22.593, P < 0.001; SMN: t = -8.262, P < 0.001; CON: t = -32.715, P < 0.001; DAN: t = -11.272, P < 0.001; Lan.: t = 33.827, P < 0.001; FPN: t = 24.439, P < 0.001; Aud.: t = 0.191, P = 0.849; DMN: t = 11.303, P < 0.001; PMN: t = -35.719, P < 0.001; VMN: t = -11.056, P < 0.001; OAN: t = 0.311, P = 0.756).”

Irrespectively, we have further highlighted that such a global interpretation for asymmetry of areas is still meaningful, given that a node is always placed in a global context. We have now further explained that our metrics give insights in local embedding of global phenomena in the introduction, p. 3.

Introduction, p. 3: “These low-dimensional gradient embeddings describe global embedding of local features, rather than local phenomena. Thus, interpretation for asymmetry of areas is under a global context.”

My second concern is about interpreting the brain asymmetry as differences in connectivity, as opposed to differences in other things like regional size. The authors use a parcellated approach, where presumably the parcels are left-right symmetric. If one area is actually larger in one hemisphere than in the other, the will manifest itself in the connectivity values. To mitigate this, it may be necessary to align the two hemispheres to each other (maybe using spherical registration) using connectivity prior to applying the parcellation.

Thanks for this nice idea. We have now computed the differences of the mean rsfMRI connectome along the first gradient at the vertex level using 100 random subjects, as we have the data mapped to a symmetric template (fs_LR_32k), indicating that each vertex has a symmetric counterpart in the right hemisphere. Our results show left-right asymmetry as language/default mode-visual-frontoparietal vertices, which is consistent with the main results of the parcel-based approach. We have also added this response to the Supplementary materials.

Though overall findings are consistent, spherical registration may also have new issues. Total anatomical spatial symmetry may not provide functional comparability at the vertex level between left and right hemisphere. For example, during language tasks in the current sample, the activated frontal region in the left hemisphere is larger than the activated contralateral region in the right hemisphere. In the current study, we aimed to evaluate asymmetry between functionally and structurally homologous regions, as described by the Glasser atlas. In case of the resting state fMRI data, we used the region-wise symmetric multimodal parcellation (Glasser et al., 2016). This parcellation ensures the functional contralateral regions in both hemispheres. A previous study (Williams et al., 2021) investigated the structural and functional asymmetry in newborn infants. They used spherical registration (make fs_LR symmetric) for structural asymmetry but not for functional asymmetry. As such spheric registration may hide functional information, we think spherical registration may be more suitable for structural studies.

To address the concern regarding the alignment of hemispheres, we used joint alignment for LL and RR to compare the results between this and the Procrustes alignment technique (Pearson r=0.930, P_spin<0.001), below is the figure of asymmetry along the principal gradient (upper: joint alignment, below: Procrustes alignment) indicating convergence between both approaches. We have reported this information in the Supplementary Materials.

Lastly, we do agree that parcel size might be an important issue influencing the asymmetry pattern. To test for such an effect, we performed the correlation between the rank of parcel size (left-right)/(left+right) and rank of asymmetry index. It suggests only a small insignificant correlation along G1 (Spearman r_intra=0.130, P_spin=0.105; Spearman r_inter=0.130, P_spin=0.084). Of note, there is a systematic difference in parcel size as a function of sensory-association hierarchy, indicating that the link between parcel-size and asymmetry may vary as a function of sensory vs associative regions.

Reviewer #2 (Public Review):

Using recently-developed functional gradient techniques, this study explored human brain hemispheric asymmetry. The functional gradient is a hot technique in recent years and has been applied to study brain asymmetries in two papers of 2021. Compared to previous studies, the current study further evaluated the degree of genetic control (heritability) and evolutionary conservation for such gradient asymmetries by using human twin data and monkey's fMRI data. These investigations are of value and do provide interesting data. However, it suffers from a lack of specific hypotheses/questions/motivations underlying all kinds of analyses, and the rich observational or correlational results seem not to offer significant improvement of theoretical understanding about brain asymmetries or functional gradient. In addition, given the limited number of twins in HCP project (for a heritability estimation), the limited number of monkeys (20 monkeys), and the relatively poor quality of monkeys' resting functional MRI data, the results and conclusion should be taken cautiously. Below are major concerns and suggestions.

We thank the Reviewer for the evaluation of our work and the helpful suggestions.

The gradient from resting-state functional connectome has been frequently used but mainly at the group level. The current study essentially applied the gradient comparison (i.e., gradient score) at the individual level. Biological interpretation for individual gradient score at the parcel level as well as its comparability between individuals and between hemispheres should be resolved. This is the fundamental rationale underlying the whole analyses.

We thank the Reviewer for this remark, and are happy to provide further rationale for using and comparing individual gradients scores to evaluate individual variation in asymmetry and associated heritability. Though gradients from resting-state functional connectivity have been frequently used at the group level, various studies have also studied individual differences. For example, using linear mixed models to compare gradient scores between left and right across subjects (Liang et al., 2021), applying the individual gradient scores to compare disease and controls (Dong et al., 2020, 2021; Hong et al., 2019; Park et al., 2021), and link individual hippocampal gradients to memory recollection (Przeździk et al., 2019). Together, these studies show individual variations of local gradients, indicating changes in node centrality and hubness (Hong et al., 2019), and connectivity profile distance (Y. Wang et al., 2021). Of note, low-dimensional embeddings describe global embedding of local features, rather than local phenomena. Thus, interpretation for asymmetry of areas is under a global context. The biological interpretation for individual gradients would be to what degree the system segregated and integrated has changed patterns of ongoing neural activity (Mckeown et al., 2020). It reflects that individuals have different functional boundaries between anatomical regions. Whereas, individual neurons are embedded under the global-local boundaries through a cortical wiring space consisting of intricate long- and short-range white matter fibers (Paquola et al., 2020).

Introduction, p. 4: “We applied the individual gradient scores to study the asymmetry, consistent with prior studies (Gonzalez Alam et al., 2021; Liang et al., 2021). Individual variation along the gradients reflects a global change across subjects in the functional connectome integration and segregation, and it is under genetic control (Valk et al., 2021). Moreover, to what degree the system segregated and integrated relates to patterns of ongoing neural activity (Mckeown et al., 2020), and different individuals have different functional boundaries between anatomical regions.”

Results, p. 5: “Next, individual gradients were computed for each subject and the four different FC modes and aligned to the template gradients with Procrustes rotation. It rotates a matrix to maximum similarity with a target matrix minimizing sum of squared differences. As noted, Procrustes matching was applied without a scaling factor so that the reference template only matters for matching the order and direction of the gradients. Therefore, it allows comparison between individuals and hemispheres. The individual mean gradients showed high correlation with the group gradients LL (all Pearson r > 0.97, P spin < 0.001).”

Only the first three gradients are used but why? What about the fourth gradient? Specific theoretical interpretation is needed. At the individual level, is it ensured that the first gradients of all individuals correspond to each other? In this study, it is unclear whether we should or should not care about the G2 and G3. The results of G2 and G3 showed up randomly to some degree.

In the current study we focused on the principal gradient in the main analysis, given its association with sensory-transmodal hierarchy, microstructure, and evolutionary alterations (Margulies et al., 2016; Paquola et al., 2019; Xu et al., 2020).

Conversely, gradient 2 reflects the dissociation between visual and sensory-motor networks and gradient 3 is linked to task-positive, control, versus ‘default’ and sensory-motor regions. We analyzed asymmetry and its heritability of the first three gradients (explaining respectively 23.3%, 18.1%, and 15.0% of the variance of the rsFC matrix). However, we extracted the first ten gradients to maximize the degree of fit (Margulies et al., 2016; Mckeown et al., 2020). We have now also shown G4-10 mean asymmetry results as a supplementary figure. To ensure correspondence of gradients across individuals, we aligned the individual gradients to the group level template with Procrustes rotation. Procrustes rotation rotates a matrix to maximum similarity with a target matrix minimizing sum of squared differences. The approach is typically used in comparison of ordination results and is particularly useful in comparing alternative solutions in multidimensional scaling. Figure S1 shows the mean gradients across subjects of each FC mode, which is close to the Figure 1D template gradient space.

Results, p. 5: “The current study analyzed asymmetry and its heritability of the first three gradients explaining most variance (Figure 1d). As they all have reasonably well described functional associations (G1: unimodal-transmodal gradient with 24.1%, G2: somatosensory-visual gradient with 18.4%, G3: multi-demand gradient with 15.1%). However, given we extracted ten gradients to maximize the degree of fit 26,52. We stated mean asymmetry of G4-10 in Figure 1-figure supplement 1.”

The intra-hemispheric gradient is institutive. However, it is hard to understand what the inter-hemispheric gradient means. From the data perspective, yes you can do such gradient comparison between the LR and RL connectome but what does this mean? Why should we care about such asymmetry? From the introduction to the discussion, the authors simply showed the data of inter-hemispheric gradients without useful explanation. This issue should be solved.

We are happy to further clarify. The LR and RL connectivity reflects cross-hemispheric functional signal interaction via corpus callosum, whose structural asymmetry is usually studied (Karolis et al., 2019). Such intra-hemispheric connections, compared to the inter-hemispheric connections, have been suggested to reflect the inhibition of corpus callosum, and underlie hemispheric specialization. Different information relies on hemispheric specialization (e.g., visual, motor, and crude information) and/or inter-hemispheric information transfer (e.g., language, reasoning, and attention) (Gazzaniga, 2000). To clarify and motivate the analysis of both intra- and inter-hemispheric asymmetry in functional gradients, we have now added further detail in the introduction, p. 5.

Here is text: Introduction, p. 4. “The full FC matrix contains both intra-hemispheric and inter-hemispheric connections. Intra-hemispheric connections, compared to the inter-hemispheric connections, have been suggested to reflect the inhibition of corpus callosum and may underlie hemispheric specializations involving language, reasoning, and attention. Conversely, inter-hemispheric connectivity may reflect information transfer between hemispheres, for example a wide range of modal and motor information, and crude information concerning spatial locations 48. Previous studies have reported intra-hemispheric FC to study gradient asymmetry 6,38. By having the callosum related to association white matter fibers, one hemisphere could develop for new functions while the other hemisphere could continue to perform the previous functions for both hemispheres 48. Therefore, in addition to the intra-hemispheric FC gradients, we depicted the inter-hemispheric FC, which is abnormal in patients with schizophrenia 23,49 and autism 24.”

as well as Discussion, p. 16 “Conversely, the transmodal frontoparietal network was located at the apex of rightward preference, possibly suggesting a right-ward lateralization of cortical regions associated with attention and control and ‘default’ internal cognition 62,63. The observed dissociation between language and control networks is also in line with previous work suggesting an inverse pattern of language and attention between hemispheres 3,64. Such patterns may be linked to inhibition of corpus callosum 65, promoting hemispheric specialization. It has been suggested that such inter-hemispheric connections set the stage for intra-hemispheric patterns related to association fibers 48. Future research may relate functional asymmetry directly to asymmetry in underlying structure to uncover how different white-matter tracts contribute to asymmetry of functional organization.”

and Discussion, p.18 “Though overall intra- and inter-hemispheric connectivity showed a strong spatial overlap in humans, we also observed marked differences between both metrics across our analysis. For example, although we found both intra- and inter-hemispheric differences in gradient organization to be heritable, only for intra-hemispheric asymmetry we found a correspondence between degree of asymmetry and degree of heritability. Similarly comparing asymmetry observed in human data to functional gradient asymmetry in macaques, we only observed spatial patterning of asymmetry was conserved for intra-hemispheric connections. Whereas intra-hemispheric asymmetry relates to association fibers, commissural fibers underlie inter-hemispheric connections 77 It has been suggested that there is a trade-off within and across mammals of inter- and intra-hemispheric connectivity patterns to conserve the balance between grey and white-matter 76. Consequently, differences in asymmetry of both ipsi- and contralateral functional connections may be reflective of adjustments in this balance within and across species. Secondly, previous research studying intra- and inter-hemispheric connectivity and associated asymmetry has indicated a developmental trajectory from inter- to intra-hemispheric organization of brain functional connectivity, varying from unimodal to transmodal areas 78,79. It is thus possible that a reduced correspondence of asymmetry and heritability in humans, as well as lack of spatial similarities between humans and macaques for inter-hemispheric connectivity may be due to the age of both samples (young adults in humans, adolescents in macaques). Further research may study inter- and intra-hemispheric asymmetry in functional organization as a function of development in both species to further disentangle heritability and cross-species conservation and adaptation.”

When aligning intra-hemispheric gradient, choosing averaged LL mode as the reference may introduce systematic bias towards left hemisphere. Such an issue also applies to LR-RL gradient alignment as well as cross-species gradient alignment. This methodological issue should be solved.

We thank the Reviewer for raising this point. Indeed, we also used RR as reference, the results were virtually identical. We have stated this in the Results, p. 13. Regarding the cross-species alignment, we averaged the left and right hemispheres to reduce the systematic bias. It showed that the correlation and comparison results remained robust. Now we have updated the method and corresponding results (p.10). Here is the text:

Results (p.15): “We also set the RR FC gradients as reference, the first three of which explained 22.8%, 18.8%, and 15.9% of total variance. We aligned each individual to this reference. It suggested all results were virtually identical (Pearson r > 0.9, P spin < 0.001).”

Results (p.10): “To reduce a possible systematic hemispheric bias during the cross-species alignment, we averaged the left and right hemisphere. We found that the macaque and macaque-aligned human AI maps of G1 were correlated positively for intra-hemispheric patterns (Pearson r = 0.345, P spin = 0.030). For inter-hemispheric patterns, we didn’t observe a significant association (Pearson r = -0.029, P spin = 0.858)”

The sample size of monkey (i.e., 20) is far less than human subjects (> 1000). Such limitation raises severe concern on the validity of the currently observed gradient asymmetry pattern in the monkey group, as well as the similarity results with human gradient asymmetry pattern. Despite the marginal significance of G1 inter-hemisphere gradient between humans and monkeys, I feel overall there is no convincingly meaningful similarity between these two species. However, the authors' discussion and conclusion are largely based on strong inter-species similarity in such asymmetry. The conclusion of evolutionary conservation for gradient asymmetry, therefore, is not well supported by the results.

We agree with your comments. Although it is a small sample compared to humans, in NHP studies, it is a relatively decent sample size (most of the studies have N<10). Of note, recent work suggested that the individual variation pattern can be captured using 4 subjects in both human and macaques (Ren et al., 2021).

To overcome potential overinterpretation of our findings, we have now changed the title to a more descriptive format: “Heritability and cross-species comparisons of asymmetry of human cortical functional organization”

And further detailed findings already in the Abstract; “These asymmetries were heritable in humans and, for intra-hemispheric asymmetry of functional connectivity, showed similar spatial distributions in humans and macaques, suggesting phylogenetic conservation.”

We have pointed out the small sample size in the limitation. Please find the text below: Discussion, p. 18: “Due to the small sample size of macaques, it is important to be careful when interpreting our observations regarding asymmetry in macaques, and its relation to asymmetry patterning observed in humans. Therefore, further study is needed to evaluate the asymmetry patterns in macaques using large datasets 53,79”

And nuanced the conclusion, p.19: “This asymmetry was heritable and, in the case of organization of intra-hemispheric connectivity, showed spatial correspondence between humans and macaques. At the same time, functional asymmetry was more pronounced in language networks in humans relative to macaques, suggesting adaptation.”

Author Response

Reviewer #2 (Public Review):

Weaknesses:

1) It is surprising that certain enzymes with established depalmitoylation activity were excluded from BrainPalmSeq data-base (e.g. ABHD4, ABHD11, ABHD12, ABHD6)

We have now included additional depalmitoylating enzymes in our database and manuscript.

2) Albeit not essential it will be of great interest to include in the established database enzymes necessary for synthesis of ACYL-CoA (e.g. ACSL enzymes). One improvement may include the ability of future researchers to add such curated analysis to the platform within future research studies.

We agree with the reviewer there are many expansions of our gene set that would be interesting to include. Given the size of the current manuscript however, for brevity we have decided at present to curate data for the core set of genes that directly regulate dynamic palmitoylation. We have also added a ‘Contact Us’ feature to the website, so that repeatedly requested genes or datasets can be added in future.

3) The experimental validation presented in figure 6 relies on over-expression of substrates and ZDHHC enzymes. This setup is known to often provide unspecific S-acylation events which result from excess enzyme or substrate availability. Hence, such validation would be greatly strengthened by loss of function experiments.

We have now done loss-of-function experiments and included results in major discussion point 1 above. If the editors/reviewers think it is appropriate to add to the manuscript, we will comply. However, as our negative data does not negate the fact that ZDHHC9 is able to palmitoylate the myelin proteins tested, but merely suggests it may not be necessary for protein palmitoylation in vivo, we do not think it strengthens the manuscript.

4) The authors relevantly use in-situ hybridization images from the Allen Brain atlas to validate their predictions. Although it is understandable that an extensive experimental validation of the predictions here established would be out of the scope of the current study, this work could be improved by validating the RNA expression at the protein level of certain abundant ZDHHC enzymes in available neuro-associated cell types.

We have now validated RNA expression at the protein level for a few palmitoylating and depalmitoylating enzymes.

5) It would be interesting if the authors would further compare the predicted association clusters (e.g. figure 1), substrates (figures 1 and 2), and S-acylation pairs (figure 4) here determine, with previous determined ZDHHC enzyme associations described in different cell types and biological systems. Alternatively, further relevant validation could include testing whether further established ZDHHC-ZDHHC cascades (e.g. ZDHHC3-7) can be also detected with specific cells or regions of the CNS.

On our website, all expression data can be downloaded below the heatmaps for each study, and the cell type expression relationships between any 2 genes can be plotted by the user to reveal cell types (if any) within which genes are co-expressed. In response to this comment and that of Reviewer 3 below, we have now performed such analysis on ZDHHC5/ZDHHC20 and ZDHHC6/ZDHHC16, which are to our knowledge the best established ZDHHC cascades. We have included these plots in new Figure 1 – figure supplement 2, along with discussion on line 172. Similar analysis has been performed on the known ZDHHC-accessory protein pairs (see below).

6) Figure 3B: it is not clear why the cluster of zdhhcs with high layer specific expression displayed at the top of the graph does not follow the low-to-high expression scale of the table.

The expression data in this figure is grouped by hierarchical clustering, rather than in order of low-to-high expression, in order to be consistent with Figure 2B. While we believe this is the better way to display the data, we are willing to modify if the editors/reviewers have a strong preference.

7) Figure 4D: the more relevant potential cooperative pairs (ZDHHCs-APTs) could be highlighted in more contrasted colours.

We thank the reviewer for this suggestion but at this stage would prefer to keep the color scheme as it is so that readers are better able to formulate their own hypotheses when observing these figures.

Reviewer #3 (Public Review):

Weaknesses:

1) There is a vast amount of data available and the description and discussion of this could be endless, but there are a few points that could be brought out in more detail. For example, the correlation (or lack of correlation) of expression of the proposed zDHHC-PAT accessory proteins with their cognate zDHHCs. The dominance of a relatively small number of zDHHC enzymes (20, 2, 17, 3, 21, 8) in the CNS also merits some discussion. Is the combination of a high-capacity, low-specificity enzyme (zDHHC3) with others that are regarded as more 'specific'? I believe none of these are ER-resident - they represent Golgi and PM?

The reviewer brings up many interesting questions. Indeed, we were hopeful that this type of mining of RNAseq data would bring to light many questions that can be followed up on in future publications.

We have addressed the correlation in expression of accessory proteins with their cognate ZDHHCs with new data.

We are unsure how to address the dominance of a relatively small number of ZDHHC enzymes (20, 2, 17, 3, 21, 8) in the CNS, beyond highlighting this expression pattern. We believe that interpretation of the expression of this in any way (e.g. co-expression of high-capacity, low-specificity enzymes (ZDHHC3) with more 'specific' ZDHHCs) would merely be speculative. However, we are open to adding further discussion with some guidance from the reviewer.

An early example of the verbification of Steven Pinker's name. Here it indicates the view of predominantly privileged men to argue that because the direction of history has been so positive, that those without power shouldn't complain.

I've also heard it used to generally mean a preponderance of evidence on a topic, as seen in Pinker's book The Better Angels of Our Nature, but still not necessarily convincingly prove one's thesis.

Aristotelian criticism is largely concerned with wondering how effective an artifact is in reaching its intended audience. In this case, Senator Smith never mentions Sen. McCarthy by name, but given the historical context, it is obvious she refers to him and his supporters in condemning "the Senate and its members". If one were to measure her success in doing so, as mentioned in Lorraine Boissoneault's Smithsonian article, stating , "The one person who didn’t forget Smith’s speech was McCarthy himself. 'Her support for the United Nations, New Deal programs, support for federal housing and social programs placed her high on the list of those against whom McCarthy and his supporters on local levels sought revenge,' writes Gregory Gallant in Hope and Fear in Margaret Chase Smith’s America. When McCarthy gained control of the Permanent Subcommittee on Investigations (which monitored government affairs), he took advantage of the position to remove Smith from the group, replacing her with acolyte Richard Nixon, then a senator from California." This may not have been an intended effect, but shows nonetheless the significance and degree to which Smith's speech was able to reach her audience. Unfortunately however, it's hard to say how effective entirely her speech would have been, as popularity of her speech waned as the Korean War broke out later the same month, inclining many to take a more right-wing, anti-communist approach favored by McCarthy and many other Republicans.