Author Response

Reviewer #1 (Public Review):

HCN channels are atypically opened by the downward movement of gating charges during hyperpolarisation and have such weak coupling between the VSD and pore domain, and in the absence of an open state structure, extracting mechanistic information has been difficult. This manuscript is a continuation of a previous study on HCN channel gating that revealed how hyperpolarisation causes a downward movement of the VSD's S4, with breakage into two helices. The authors explore gating motions and the coupling between VSD and the pore domain using atomistic simulations. This includes microsecond MD with and without very strong -1V applied potentials to try to drive VSD-TMD changes to open the channel. In the end, however, the authors used a biased simulation approach (adiabatic bias) to enforce conformational change from resting to an open homology model of HCN based on hERG/rEAG. This microsecond simulation followed three interaction distances that were suggested to change between resting and open states based on free MD. This simulation caused pore opening and allowed a description of changes that may occur during gating, including a competition of S5-S6 and S6-S6 contacts and lipid binding locations, which may suggest lipid-dependent function and explain an unexpected closed structure at 0mV in micelles. While I feel the manuscript is written for the HCN expert audience, the mechanistic information in terms of hyperpolarisation-induced voltage gating makes it of much interest. The manuscript is presented at a high level, though there are a couple of points to address, including reproducibility of simulations and potential for more relation to experimental findings.

We appreciate the comments, thank you, please find a detailed answer below.

The authors carried out 1μs-MD simulations of the resting, activated, and a Y289D mutant at 0 mV, and then tried to drive the conformational change with a very large -1V voltage (double that studied previously). In 1 us MD, is the membrane stable with such a big voltage, as it would likely not be experimentally? Even with a volt applied, there was incomplete activation of the voltage sensors, despite timescales approaching that of activation.

This reviewer is correct in cautioning against membrane rupturing effects in simulations with a voltage of this magnitude. We have indeed checked that the membrane and the protein remains intact under these conditions and can confirm that no poration occurs. As membrane poration is stochastic, it could indeed occur over microsecond timescales under 1V, but the probability remains low, and we were lucky to not face this situation herein. Note that whereas potentials of this magnitude could not be applied in experiments, they are relatively routinely used in MD simulations to speed up processes that are driven by changes in transmembrane potentials.

Interestingly, other work from our lab (Rems et al. Biophysical Journal 119 (1) 190-205 (2020)) has shown that HCN1 voltage sensor domains are less prone to poration than those from other voltage sensor domains, for reasons that remain to be determined.

Author Response Figure 1. Final snapshots from the simulations of the resting (blue), intermediate (yellow) and activated (red) states. The representation of the solvent (water+ions) in cyan showed no membrane poration at the end of the 1us simulations.

For the pulling/ driving simulations (adiabatic bias MD) to change suspected interaction distances (V390-I302, N300-W281, and D290-K412), it seems to be just 1 simulation, without reproducibility. One has to wonder, if the simulation was redone from a very different initial conformation, would the results be the same (in addition to the distances themselves that were enforced by the ABMD). Moreover, the authors had to model the open state, such that the results depend on a homology model based on other CNBD channels, hERG / rEAG. Although the model stayed open for a microsecond, what other measures of accuracy of the homology model are there, such as preserved distances according to mutants/double mutants?

The ABMD simulations were repeated, please refer to the response to essential revisions point 1 for details.

For reasons mentioned by the reviewer as well as a reconsideration of our strategy to model channel opening, we have decided to omit homology models from the revised version of the paper.

The authors find that activation involves hydrophobic forces that strengthen the intra-subunit S4/S5/S6 interface, as well as lipid headgroups that make contact with hydrophilic residues at this interface, with lipid tails also contributing to hydrophobic contacts. The authors see bending and rotation of the lower S4 and a displacement of S1 away from S4 that exposes the VSD-pore interface to lipids, with increased lipid contacts at S4 and S5 during activation. This indicates lipid tails may play a role in coupling in HCN1 and may explain the closed state micelle structure at 0mV. Two sites of lipid contact are identified, one engaging VSD residues and the other polar or charged residues on S5 and S6. No experiments are presented or proposed to test the predicted lipid sites. e.g. Mutation of key residues, such as the arginine and histidine seen binding lipid headgroups could be tested as proof of their involvement, or perhaps experiments with varied phosphate moieties? In the absence of new experiments, is there existing data that could help validate the findings?

We thank this reviewer for this comment. As noted in the response to essential revisions point 3, such experiments are challenging, and have not been reported so far in HCN channels. We do agree that aspects of the mechanism we propose remain hypothetical awaiting further work, but are happy to report that importance of lipid interactions with the crucial salt bridge pair mentioned in the response to essential revisions point 3 has been completely independently validated, thus strengthening our mechanistic hypothesis substantially.

During free MD simulation, the authors see tilting of S5 caused by activation of the Y289D mutation that brings D290 and K412 positions into proximity. How do we know that the adjacent mutant of Y289 to aspartate has not caused this, or was this interaction also seen in wild-type simulation? Fig.3c might suggest the wt activated simulation may see such an interaction, but it is unclear given the large C_alpha distances, as opposed to H-bonding distances.

Indeed, Figure 3 appears to indicate that this interaction between D290 and K412 is present in the activated state when the mutation is reverted to the WT sequence. We have recalculated the interaction propensity using all atoms of the residues and present an updated Figure 3c in response.

The authors predict that a D290-K412 salt bridge may be important for gating and sought to experimentally validate the interaction in the activated-open state using cysteine cross-bridging. As this is the only experimental backing in the paper, it is important to be able to judge its ability to report on the D290-K412 salt bridge. A comparison experiment demonstrating other crosslinks that do not favour the open state would have been helpful in this regard e.g. if crossbridging at similar locations (but not predicted to change interaction during gating) had little effect on I/Imax, then the result may be bolstered. Are there existing mutagenesis experiments that may suggest the importance of these residues (as well as for other key interaction distances identified)?

Negative results in cross bridging and cysteine accessibility studies in general are difficult to interpret as the lack of a cadmium-specific effect may be due to inaccessibility of the site to cadmium, pairwise distance too far to bridge by cadmium, or bridging or the specified site without a functional effect. However, as reviewer 2 pointed out below, the Yellen group has performed extensive cross bridging experiments in the S4-S5 to Clinker region in spHCN and in most of these positions, the pairs favoring the open state are closer together in our models than pairs favoring the closed state or those without functional effect. We have added Videos 1-6 to highlight this comparison on our open state models and describe in our updated discussion section.

Rotation of the V390 side chain from a position facing the pore lumen to a position facing I302 on S5 is coupled to an increase of the pore radius at V390, an increased hydration of the pore intracellular gate, and K+ ion movement. Perhaps 5 or 6 ions cross in that single simulation. As K channel ion permeation can depend critically on starting ion configs (as well as the model/force field), reproducibility of this finding is important but does not appear to have been tested. How can we be sure that periods of permeation or no permeation in individual simulations are reliable?

As mentioned in our response to essential revisions point 1, we have modified the collective variable set used in ABMD, and repeated the simulations in 4 replicates. Whereas the number of permeation events is low in each simulation (Figure 4 S1), the consistency across repeats indicates that these open pore models indeed represent conductive states. Given how short the simulations are, however, it appears unreasonable to infer conductance values from these observations.

Reviewer #3 (Public Review):

In this work, Elbahnsi and colleagues use enhanced sampling MD simulation, to recapitulate step by step, the electromechanical coupling between VSD and the pore in HCN1 channels. Building on the available cryoEM structures of HCN1 with the VSD in resting and active state, the authors characterize by MD a subset of interactions that seemingly stabilize the open channel. This subset is, in turn, used in enhanced-sampling simulations to guide channel opening. The main findings are that S4 movement induces a rearrangement of the hydrophobic interaction at the level of S1- S4- and S5 interfaces. Occupancy of lipids seems therefore statedependent and highlights their regulatory role in HCN gating.

The approach is rather innovative, and it apparently allows the reconstruction of the whole mechanism of gating, pushing the predictive power of MD simulation well beyond its actual temporal limitations. At the same time, the initial choice of interactions is crucial for this approach, because the result cannot differ from the inputs. And reading the paper it does not emerge clearly how the correctness of the reconstructed gating pathway can be verified, if not by functional validation.

We thank the reviewer for this thoughtful review. It has pushed us to reconsider our approach to enhance the sampling of channel activation and gating. Please refer to the detailed response below as well as the response in particular to essential revisions point 1.

Here are my comments on the main interactions that were used to feed the final MD simulation:

1) W281-N300: this interaction, previously identified and studied in SpH channels (Ramentol et al, 2020; Wu et al, 2021), has been elegantly confirmed in this paper. Its inclusion in the initial subset seems appropriate. In the other two cases, the choice of interactions requires further explanations and experimental validation.

2) D290 and K412: the validation of this interaction shown in Figure 3 and suppl Figure 1 is missing a control, i.e., the effect of the addition of Cd++ on the wt channel. Please add.

We have performed the control suggested. Please also refer to the answer to essential revisions point 2.

3) Modelling the open state of HCN1 pore (page 18), is done on the structure of the distantly related hERG rather than on the available open pore structure of HCN4. This choice is justified as follows by the authors:

a) "Available structures in the CNBD channel family for which representative structures have been solved in closed and open states".

b) "The structural mechanism of pore gating (i.e. the ⍺ to 𝜋 helix occurring at the glycine657 hinge in hERG) observed in rEAG/hERG may be a conserved gating transition in the CNBD family of channels"

I encourage the authors to consider the following:

a) The structure of hERG channel is not available in the closed/open configuration, indeed the comparison must be done with the closed configuration of the related channel rEAG. On the contrary, HCN4 is available in the closed/open configurations. Moreover, one of the open pore structures shows S4-S5-S6 in a very similar conformation to the lock open mutant (F186C/S264C) of HCN1 (Saponaro et al, 2021). With an available HCN4 open structure, forcing HCN1 to the open pore structure of hERG channel (which opens in depolarization and is not regulated by cAMP) seems not necessary.

In response to this point, we reconsidered our approach and chose to instead use a biasing distance that is consistently increased in CNBD channels of resolved structures, that between neighboring and cross-subunits V390. We have detailed our rationale in the response to essential revisions point 1.

To my knowledge, hERG is the only channel of the CNBD family for which the transition ⍺ to 𝜋 helix reported by the Authors, occurs in S6. It is not reported for other CNBD family members, in particular for the CNG channels mentioned by the Authors (Zheng et al., 2020; Xue et al., 2021, 2022). Task 4 (Zheng et al) does not show it. Its pore opens by a right-handed twist of S6 at glycine 399, a conserved glycine in all CNG. Human CNGA1 too, opens the pore by a rotational movement of S6 hinged at the equivalent glycine (glycine 385) (Xue et al, 2021). And the same occurs in the non-symmetrical channel CNGA1/B1 (Xue te al, 2022). So, it seems that CNG channels do not show the ⍺ to 𝜋 helix transition in the open pore. Moreover, hERG excluded, all other members of the CNBD family, CNG, EAG, and HCN4 included, do not bend at the hinge glycine 657 of hERG, but at another glycine (gly 648 in hERG numbering) located upstream. Further, their opening is due to a rotation of S6 associated with an outward movement, rather than to the lifting of the lower part of S6, as in hERG.

After considering this reviewer’s comment, we were surprised to see that HCN1 is apparently prone to secondary structure deformation in S6, even when biasing the aforementioned distances, and thus enforcing no rotation at all in S6. We are intrigued by this observation and eagerly await experimental validation or disproval.<br /> In the meantime, we have made clear in the text that this hypothesis remains based exclusively on modeling work.

4) V390-I302: this interaction is predicted to stabilize the open pore configuration and was included in the subset. The contact between V390 on S6 and I302 on S5 is observed in the homology model discussed above when the S6 is twisted at the glycine hinge, rotating the preceding residue (V390) out of its pore-lining position and is. Again, I can only disagree with this hypothesis because it has been experimentally demonstrated (Cheng et al, J Pharmacol Exp Ther. 2007 Sep;322(3):931-9) that the side chain of Valine390 is inside the cavity of the open pore of HCN1 channels as it controls the affinity for the pore blocker ZD7288.

In accordance with other comments above, we have eliminated the bias applied to the V390I302 distance. However, the new ABMD simulations with bias applied to encourage dilation at position 390 still involve rotation of V390 away from the central pore axis, albeit with bending of S6 at the upper glycine mentioned by this reviewer. The degree of rotation is lower than in our previous simulations so that V390 still lines the inner vestibule in the open state, consistent with the observation that this position influences the apparent affinity of open pore blockers.

In conclusion, modelling the open state pore of HCN1 on hERG rather than on that of HCN4 seems not justified based on accumulated evidence in the published literature. Therefore, the choice of the authors to use it as the open pore model of HCN1 channels needs to be experimentally validated. One possibility is to mutate the glycine hinge, gly391 in HCN1, into an Alanine in order to remove the flexible hinge. If this mutation alters pore gating, it will support the choice of the Authors.

Once more, we thank the reviewer for the comments, which have led us to reconsider a larg part of our modeling work.

Author Response

Reviewer #2 (Public Review):

There is emerging evidence that connexin43 hemichannels localized to mitochondria can influence their function. Here the authors demonstrated using an osteocyte cell model that connexin43 is localized to mitochondria and that this is enhanced in response to oxidative stress. Several lines of evidence were presented showing that mitochondrial connexin43 forms functional hemichannels and that connexin43 is required for optimal mitochondrial respiration and ATP generation. These aspects were major strengths of the study.

The authors also show that connexin43 is recruited to mitochondria in response to oxidant stress, as a cell protective mechanism. This was primarily done using hydrogen peroxide to generate oxidant stress; primary osteocytes from Csf-1+/- mice, which are prone to Nox4 induced oxidant stress, also show enhanced mitochondrial connexin43 when compared with wild type osteocytes.

Several approaches were used to demonstrate that connexin43 interacts with the ATP synthase subunit, ATP5J2, suggesting a direct role for connexin43 in the control of ATP synthesis by mediating mitochondrial ion homeostasis. Several experiments were done using a series of pHluorin fusion protein constructs as a proton sensor, these experiments hint at a potential role for connexin43 in regulating H+ permeability to support ATP production. However, the effects of inhibiting connexin43 on pH were modest, suggesting that additional roles for mitochondrial connexin43 in ATP generation should be considered.

Thank you for your positive and thoughtful comments. We agree that additional roles for mitochondrial Cx43 may be possible. As an example, we consider that there may be a change in the stability of ATP synthase that occurs after mtCx43 deficiency. This and other possible roles of mtCx43 ought to be investigated in the future.

Reviewer #3 (Public Review):

This manuscript should be of broad interest to readers not only in the field of gap junction (GJ) mediated cell-to-cell communication but also to scientists and clinicians working on the function of mitochondria and metabolism. Their data elucidates a new function of Cx43 in regulating the energy (ATP) generation of mitochondria, e.g., under oxidative stress.

The canonical function of gap junctions is in direct cell-to-cell communication by forming plasma membrane traversing channels that electrically and chemically connect the cytoplasms of adjacent cells. These channels are assembled from connexin proteins, connexin 43 (Cx43). However, more recently new, non-canonical cellular locations and functions of Cx43 have been discovered, e.g. mitochondrial Cx43 (mtCx43). However, very little is known about where Cx43 transported into mitochondria is derived from, how Cx43 is transported into mitochondria, where it is located in mitochondria, in which form Cx43 is present in mitochondria, (polypeptides, hemi-channels (HCs), complete GJ channels), and what the function of mtCx43 is. The authors addressed the latter question. The authors provide convincing evidence that mtCx43 modulates mitochondrial homeostasis and function in bone osteocytes under oxidative stress. Together, their study suggests that mtCx43 hemi-channels regulate mitochondrial ATP generation by mediating K+, H+, and ATP transfer across the mitochondrial inner membrane by directly interacting with mitochondrial ATP synthase (ATP5J2), leading to an enhanced protection of osteocytes against oxidative insult. These findings provide important information of a role of Cx43 functioning directly in mitochondria and not at the canonical location in the plasma membrane. While most of the functional assays presented in Figures 2-8 appear solid, the mitochondrial localization of Cx43, its translocation into mitochondria under oxidative stress, and its configuration as hemi-channels (Figure 1) is less convincing. I have five general comments that should be addressed:

1) This study was performed in MLO-Y4 osteocyte cells. Is the H2O2 induced increase of mitochondrial Cx43 MLO-Y4 cell type or osteocyte specific, or is Cx43 playing a more general role in mitochondrial function, e.g. under oxidative stress? Osteoblasts such as MC3T3-E1 and MG63, and many other cell types endogenously express Cx43, and oxidative stress is a general physiological stressor, not only for osteocytes and bone cells. Attending to this question would address the generality of the findings for mitochondrial function.

We thank the reviewer for bringing up these valid points; seeing the phenotype displayed in secondary cell types, such as osteoblasts, would be of great relevance and interest. To address this, we conducted new experiments on MC3T3-E1 cells (Figure 1-figure supplement 2). After 2 hrs of H2O2 treatment, Cx43 accumulated on the mitochondria, marked by Mitotracker. Statistical analysis also showed a significant increase of the localization between Cx43 and Mitotracker (Figure 1-figure supplement 2B). The colocalization coefficient is higher in the Ctrl group in MC3T3-E1 cells when compared with the MLO-Y4 Ctrl group, indicating a different response level in other cell lines. Osteoblasts seemed to be more sensitive to redox interference. Overall, proving the point that under oxidative stress, mtCx43 may display a similar phenotype, across multiple cell lines, although the degree of sensitivity may differ.

2) The images of MLO-Y4 cells (Figure 1A) and the primary osteocytes isolated from Csf-1+/- and control mice (Figure 8) do not show visible gap junctions. I guess this is due to the fact that slides were stained with the Cx43(E2) antibody. I feel, staining of these cells in addition with the Cx43(CT) antibody would be helpful to get a better understanding on the distribution of Cx43 in gap junctions and undocked/un-oligomerized Cx43 in these cells.

Thank you for the suggestion. To get a better understanding of the distribution of Cx43, either in GJ or HC form, we performed additional experiments in MLO-Y4 cells using the Cx43(CT) antibody and data are shown below. With Cx43(CT) staining, we observed more signals in the cells and on the plasma membrane. After H2O2 treatment, we observed increased and stronger signals localized on the mitochondria compared with the untreated control group. Stronger signals observed in the plasma membrane indicate the gap junction stained by Cx43(CT) antibody.

3) The images of cells presented in Figure 1A are quite fussy. No mitochondria are visible, and the Cx43 staining is hazy and does not localize to any subcellular structures. Also, it is not clear if the higher resolution image presented in Figure 1C actually represents a mitochondrion. A good DIC image, or co-staining with another mitochondrial marker such as MitoTracker (as shown in Figure 4-S1) would make the localization and translocation of Cx43 into mitochondria upon oxidative stress more convincing. This is especially important as the translocation, although statistically significant, increases only by about 10% or less (Figure 1B). Such a small difference (also represented in the Western analyses presented in Figure 1D) could easily be artefactual, depending on how the correlation coefficient was generated. Of note in this respect is that control cells in Figure 1A appear larger (compare the size of the nuclei) and are spread out more than the H2O2 treated cells. Better, more clear images would make the mitochondrial localization/translocation more convincing.

The reviewer made great points. To improve the image clarity, we redid the staining/imaging and determined the colocalization of SDHA and MitoTracker Deepred. The result (shown below) suggested that under normal conditions without H2O2 treatment, SDHA and MitoTracker merged perfectly, while after H2O2 treatment for 2 hrs, mitochondria became fragmented and the SDHA signal exhibited a more dotted pattern compared to the MitoTracker. Overall, we feel that MitoTracker represents the distribution of mitochondria better. SDHA is a subunit of mitochondrial complex II, and the images we presented in Figure 1C were captured from isolated mitochondria under a confocal microscope with SDHA and Cx43(CT) co-staining. Considering the specificity of SDHA (see images below), we believe the Cx43 signal we captured demonstrates the mitochondrial localization/translocation. After using MitoTracker as a mitochondrial marker and higher magnificent images, the correlation coefficient increased from 0.35 to 0.47, a 32% increment with statistical significance. As to the nuclei size, some cells indeed have smaller sizes, which may be affected by varied local cell density. The new images represented in Figure 1A are much more consistent in the nuclei size.

4) How pure are the mitochondria that were probed for Cx43 by Western shown in Figure 1D? The preparation method described is relatively simple, collecting the 10,000xg supernatant (here 9,000xg supernatant) as mitochondrial fraction. Is it possible that the Cx43 signal, at least in part, is derived from other, contaminating membranes, such as PM, Golgi, or ER? Testing the mitochondrial preparation by Western with marker proteins specific for these compartments would strengthen the author's results.

The reviewer made a great suggestion. To address this, we did a western blot to test the mitochondrial purity. Indeed, this method using centrifugation is simple, and as expected there were some contamination of ER (marked by PDI) and Golgi (marked by STX6). However, to further confirm the purity of the mitochondrial fraction, fluorescent dyes for mitochondria (MitoTracker Deepred), ER (ER-Tracker Blue-White), and nuclei (Hochest) were used. The organelle-specific dyes indicated most parts of the fraction were mitochondria. There were some contaminations with ER fragments and minimal nuclear contamination. Combining our western blot and immunofluorescence data, it can be concluded that our Cx43 signal is primarily derived from mitochondria.

5) The authors rely on previous studies to postulate that Cx43 in mitochondria forms hemichannels in their system, is localized in the inner membrane, and is oriented with the Cx43 C-termini facing the inter-membrane space (as schemed in Figure 8C). The authors use lucifer yellow (LY) dye transfer and carbenoxolone, but both are not hemi-channel specific probes. They are transferred by, and block GJ channels as well. Experiments, using hemi-channel specific probes would be more convincing. This is important, as the information cited is based on only two references (Boengler et al., 2009; Miro-Casas et al., 2009), and it still is highly unclear how a membrane protein that is co-translationally inserted into the ER membrane, then traffics through the Golgi to be inserted into the plasma membrane is actually imported into mitochondria and in which state (monomeric, hexameric). Why the Cx43(CT) specific antibody traverses the outer mitochondrial membrane and reaches the Cx43CT while the Cx43(E2) specific antibody is not described and clear either. Where are these mitochondria permeabilized with Triton X-100 as described in M&M?

We edited the Methods section. We did not use Triton X-100 to permeate mitochondria. PMP appeared to preserve mitochondrial inner membrane integrity allowing us to assess the localization of Cx43(CT) antibody on mitochondria. We showed these new immunofluorescence images in Figure 5- figure supplement 2. PMP used as a plasma membrane permeabilizer has a 6x affinity with MOM compared with MIM. Meanwhile, no Cx43(E2) Ab signal was detected in mitochondria, suggesting the extracellular loop of Cx43 faces the matrix and cannot be accessed by Cx43(E2) antibody.

The translocation of Cx43 to mitochondria was reported to involve the chaperone Hsp90-dependent TOM complex pathway (Rodriguez-Sinovas et al., 2006). After the translocation, if mtCx43 forms gap junctions in mitochondria is unclear. Lucifer yellow is widely used in hemichannel-mediated dye uptake or gap junction-mediated dye transfer. In our case, considering the channel orientation, mtCx43 should form hemichannels, and Cx43(CT) Ab could be used as a specific Cx43 HCs blocker like the study reported in cardiomyocytes (Lillo et al., 2019).

Author Response

Reviewer #2 (Public Review):

In general, the study has several novel comments, the experimental design is appropriate and the manuscript is well written. While the manuscript contains a lot of data, still it is a bit descriptive. There are also some issues, which should be addressed.

1) In Figure 1E, the authors demonstrate a small but significant decrease in body weight of mutant mice. The difference is not so drastic. They also mentioned that some mice showed kyphosis. Please provide data on what percentage of mutant mice showed kyphosis. Please also provide individual hind limb muscle weight normalized with body weight.

Thank you for your suggestions. The kyphosis was observed in some (more than one third of) Dst-b mutant mice as shown in the author response image 1. MRI or CT imaging of the skeleton is necessary to accurately diagnose kyphosis, however, the imaging was not performed in this paper. Therefore, we would like not to provide data on what percentage of mutant mice showed kyphosis.

We weighed the soleus of hind limb and demonstrated the data (lines 132-135).

2) There is a lot of variability in the age of the mice employed for this study. For example, in Figure 3, the authors mentioned 23 months old mice (Fig. 3a) and over 20 months old and over 18 months old mice. What was the exact age of the mice? Why three different age mice were used for the same set of experiments? The authors should also comment on whether the onset of myopathy in skeletal and cardiac muscle occurs at the same or different age in mutant mice.

According to the comments, we described exact ages in each figure legends. The reason for the variability in age of mice is that we performed a lot of different kinds of experiment at different time points. We described the myopathy phenotypes occurred around 16 months of age and older (lines 128-129). As for cardiomyopathy, fibrosis was observed around 16 months of age and older (Figure 3D,E).

3) Authors have studied protein aggregation only in the soleus muscle of mutant mice. Do the same types of aggregates also form in cardiomyocytes? They write that desmin aggregates were observed in cardiomyocytes of mutant mice. Please show those results in a supplemental figure.

According to the suggestion, we presented the data on desmin aggregates in the cardiomyocytes of Dst-bE2610Ter/E2610Ter mice (Figure 4-figure supplement 1).

4) In Figure 5, the authors suggest that mutant mice have mitochondrial abnormalities. However, this analysis is quite abstract and inconclusive. Immunohistochemical images show higher levels of CytoC and Tom20 whereas QRT-PCR demonstrates a significant decrease in mRNA levels of some of the mitochondria-related molecules. Authors should perform additional experiments to determine whether there is any difference in mitochondrial content between WT and mutant mice. In addition, they should perform some functional assays (i.e. OCR, seahorse experiment etc.) to measure mitochondria oxidative phosphorylation capacity is affected in mutant mice.

Thank you very much for the comment. Mitochondrial accumulation was a characteristic phenotype in Dst-bE2610Ter/E2610Ter muscle and also in other types of MFM. We performed quantitative analyses and added the data (Figure 5B). Mitochondrial accumulation was observed even in young stage when protein aggregates were not observed (Figure 3-figure supplement 1A). As the reviewer pointed out, it is important to demonstrate changes in mitochondrial function, but at this moment, we do not have that assay system and would like to present it as data for a future paper, including analysis on mitophagy.

5) The morphology of the mitochondria in TEM images shows features that are commonly observed during oxidative damage. Is there any evidence of oxidative stress in skeletal and cardiac muscle of mutant mice?

Thank you very much for the insightful comment. Gene ontology and KEGG pathway analysis on RNA-seq data did not show alterations of oxidative stress in the heart. We performed q-PCR for genes associated with oxidative stress in soleus (Figure 1-figure supplement 3), which did not show alterations in oxidative stress. In the future, we would to investigate on this point.

Reviewer #3 (Public Review):

This manuscript by Yoshioka et al. provides an extensive analysis of cardiac and skeletal muscle in a mouse model of Dst-b mutation. The authors have generated the mutant mouse model to selectively mutate Dst-b isoform of Dystonin and show that such a mutation leads to cardiomyopathy and late-onset myofibrillar myopathy. This is a novel discovery which adds valuable information to the genetic basis and molecular mechanism of MFM mediated by Dst-b. However, the manuscript needs substantial revision and additional feasible experiments.

In Figure3A, the authors suggest that there are smaller myofibers in the mutated mice however they do not provide enough data to support that. Cross-sectional areas between the mutant and WT have to be counted and represented as bins. This can better show the presence of smaller myofibers and muscle degeneration in the mutant mice.

Thank you for the helpful comment. We quantified distribution of cross-sectional area (CSA) in the soleus and then the data was indicated in Figure 3C. It indicates that there are smaller myofibers in the mutant mice.

In Figure 3A-B, the authors show that mutant mice have significantly more myofibers with centrally located myonuclei indicating the constant degeneration and regeneration in the mutant mice. Another indicator of this is the number of activated muscle stem cells. Under homeostasis, authors can compare the number of quiescent muscle stem cells and activated muscle stem cells. If there is constant degeneration and regeneration in the mutant muscle, there will be more cycling muscle stem cells and that will further prove such phenotype in question. Alternatively, they can use EdU water and quantify the number of EdU+/Pax7+ cells between the mutant and WT.

Thank you very much for the interesting comment. We agree that the subject of muscle regeneration in Dst-b mutant mice to be interesting. The authors tried to address this issue by making ISH probes for Pax7 and Emerin, which label muscle stem cells (image below). However, we were unable to reach a conclusion at this time. We intend to address this issue in the future.

In figure 2F, the authors show behavioral tests on the mutant mice of age 1 year. They do not show any significant difference in muscle strength. However, most of the myopathic phenotypes they observe are at 23 months of age, these behavioral tests can be repeated at that age to see if there is more muscle weakness in the mutant mice compared to the WT. Also, are these behavioral test readouts affected by the cardiomyopathy independent of skeletal muscle strength?

We have used rotarod test and wire hang test to evaluate motor coordination and have reported impairment of motor performance in dt mice (Horie et al., 2020). The purpose of these behavior tests in the present study was to evaluate motor coordination of Dst-b mutant mice compared to dt mice, not to address the skeletal muscle function. The text has been changed to clarify this point (lines 121-123).

Generally speaking, these behavioral tests, especially the rotarod test, may be affected by cardiac abnormalities. However, it is difficult to draw conclusions from the results of this study, since there were no significant differences in the behavioral experiments.

They show in Figure 3B that the number of CNF's are affected to a different extent in different muscles. These muscles have a different composition of myofibers, one consisting mostly of slow-type fibers while the other is mostly of fast-type. The question of whether Dst-b mutation effect of muscle fiber types is not clear. Is there a difference?

Thank you very much for insightful comment. We performed qPCR to evaluate whether Dst-b mutation affects the myofiber type of soleus muscle (Figure 1-figure supplement 3B). Expression levels of the genes did not change between WT and Dst-b mutant mice.

The cardiac myopathy phenotype that is clearly shown in figure 3 is shown in mice of 16 months of age whereas the skeletal muscle myopathy phenotype is shown in 23-month-old mice. The reason for the choice of the age of the mice should be discussed. Does the cardiac phenotype precede the skeletal muscle phenotype? Have they looked at the skeletal muscle phenotype at earlier ages? If so, that data should be provided as well and discussed.

Thank you for the comment. We analyzed myopathy and cardiomyopathy phenotypes in mice aged between 16-23 months and then have chosen histological photographs with the high quality. As shown in Figure 3B, CNFs increased in the soleus from all Dst-b mutant mice aged between 16-23 months. We added description that skeletal myopathy phenotypes occurred at 16-month-old mice.

The authors clearly show the formation of protein aggregates in the myofibers in the mutant mice. They further characterize the composition of these desmin aggregates by determining their co aggregates such as plectin and ab-Crystallin. Another component of the z-disk that has been shown to be involved in the aggregates in MFM is myotilin. The authors should also show the presence/ absence and co-aggregation of this protein with the desmin aggregates present in the mutant mice.

According with the suggestion, we performed immunohistochemistry of myotilin. Myotilin was abnormally accumulated in myofibers of the soleus from Dst-b mutant mice. We thank the nice comment and added the data in Figure 4-figure supplement 2.

The authors show abnormal accumulation of mitochondria through cyt c and Tom20 staining. The increased Tom20 levels in the mutant are shown in figure 5A which is from mice that are 23-month-old. However, in figure 3-figure supplement 1a they also show elevated Tom20 staining in the mutant mice that are only 1-2 months old. However, no other phenotype is observed at this age except for the disrupted mitochondria according to the data provided. This needs to be discussed and addressed.

We would like to correct that the data in figure 3-figure supplement 1a is 3-4 months old mutant mice. These data show that mitochondrial accumulation precedes CNF and desmin aggregation. We have described this point in the text (lines 206-209).

In Figure 5, the authors show changes in gene expression levels of genes involved in oxidative phosphorylation which supports the disrupted mitochondrial function. Additionally, ROS levels could be compared between the WT and mutant mice.

To address the involvement of oxidative stress, we performed q-PCR for genes associated with oxidative stress response in soleus (Figure 1-figure supplement 3C). qPCR data did not show alterations in such genes. In the future, we would like to investigate on this point.

In Figure 5 authors show disrupted oxidative phosphorylation in the mutant soleus muscle. Is this also associated with the fiber-type switch? Since mouse soleus muscle is a mix of fast and slow fiber types, they can look at differences in gene expression of key marker genes for slow and fast myofibers.

Thank you very much for the suggestion. We quantified expression levels of muscle fiber-type marker genes (Figure 1-figure supplement 3B). There is no data to suggest the fiber-type switch.

In figure 2, the authors show that mutant mice increase their body weight at a normal pace until 13 weeks of age after which the mutant mice become lighter than their WT counterparts. Is this suggestive of loss of muscle mass? If so, the authors show the muscle atrophy phenotype in 23-month-old mice with cross-sections. Does this mean muscle atrophy starts at an earlier age at 16 months in these mice? Please provide details on the age of the mice for each experiment. In addition, in the text (line 121) authors phrase that the mutant mice become leaner. Lean usually means a decrease in fat mass and an increase in muscle mass. Is this the case? If so, there is no data to support that and the phenotype in the mutant mice suggests there is muscle atrophy in these mice. Therefore, it would not be appropriate to suggest that these mice get lean. However, it is interesting that the bodyweight of the mutant mice gets significantly lighter after 13 weeks. EchoMRI analysis can be performed between these mice to see the total body composition to determine if there is a change in the different type of fat, lean or water composition.

Thank you for your comments. We provided exact ages in each figure legend. We described that skeletal myopathy phenotypes occur as early as 16-month-old mice, and CSA analysis showed that increased small caliber myofibers in the soleus of Dst-b mutant mice. However, muscle mass of the soleus normalized by body weight was not significantly different between control and Dst-bE2610Ter/E2610Ter mice. Therefore, muscle atrophy may be not significant enough to affect muscle weight.

Because we have not quantified the fat mass in Dst-b mutant mice, we changed the phrase from “the mutant mice become leaner” to “they become lower body weight compare with WT mice” (line 120).

Authors have performed RNA-Seq for the left ventricle from the mutant and the WT mice. Separate clustering of the WT and the mutant has to be shown at least through a PCA plot. Some IGV tracks to show the expression level changes in key genes between the mutant and WT should be shown as well. In addition, they could show how some of the genes involved in autophagy and protein degradation are affected since these are mainly the mechanism by which there is protein aggregation in MFM's.

Thank you for your helpful comment. We performed principal component analysis (PCA) and hierarchical clustering. The data showed that transcriptomic features of WT and Dst-b mutant hearts are separated (Figure 8-figure supplement 1A, B). To evaluate the change in expression level of genes, we also performed real time-PCR (Figure 8-figure supplement 1C). Our Gene ontology analysis and KEGG pathway analysis on RNA-seq data in the heart did not suggest the alterations in autophagy and protein degradation, while many genes responsible for unfolded protein response affected (Figure 8C, Figure 8-figure supplement 1C). Previous studies have reported that unfolded protein response is abnormal in several animal models for myofibrillar myopathy (Winter et al., 2014; Fang et al., J Clin Invest, 2017). We would like to investigate underlying mechanisms of protein aggregates in Dst-b mutant myofibers in the future.

Author response:

Reviewer #1 (Public Review):

This paper proposes a novel framework for explaining patterns of generalization of force field learning to novel limb configurations. The paper considers three potential coordinate systems: cartesian, joint-based, and object-based. The authors propose a model in which the forces predicted under these different coordinate frames are combined according to the expected variability of produced forces. The authors show, across a range of changes in arm configurations, that the generalization of a specific force field is quite well accounted for by the model.

The paper is well-written and the experimental data are very clear. The patterns of generalization exhibited by participants - the key aspect of the behavior that the model seeks to explain - are clear and consistent across participants. The paper clearly illustrates the importance of considering multiple coordinate frames for generalization, building on previous work by Berniker and colleagues (JNeurophys, 2014). The specific model proposed in this paper is parsimonious, but there remain a number of questions about its conceptual premises and the extent to which its predictions improve upon alternative models.

A major concern is with the model's premise. It is loosely inspired by cue integration theory but is really proposed in a fairly ad hoc manner, and not really concretely founded on firm underlying principles. It's by no means clear that the logic from cue integration can be extrapolated to the case of combining different possible patterns of generalization. I think there may in fact be a fundamental problem in treating this control problem as a cue-integration problem. In classic cue integration theory, the various cues are assumed to be independent observations of a single underlying variable. In this generalization setting, however, the different generalization patterns are NOT independent; if one is true, then the others must inevitably not be. For this reason, I don't believe that the proposed model can really be thought of as a normative or rational model (hence why I describe it as 'ad hoc'). That's not to say it may not ultimately be correct, but I think the conceptual justification for the model needs to be laid out much more clearly, rather than simply by alluding to cue-integration theory and using terms like 'reliability' throughout.

We thank the reviewer for bringing up this point. We see and treat this problem of finding the combination weights not as a cue integration problem but as an inverse optimal control problem. In this case, there can be several solutions to the same problem, i.e., what forces are expected in untrained areas, which can co-exist and give the motor system the option to switch or combine them. This is similar to other inverse optimal control problems, e.g. combining feedforward optimal control models to explain simple reaching. However, compared to these problems, which fit the weights between different models, we proposed an explanation for the underlying principle that sets these weights for the dynamics representation problem. We found that basing the combination on each motor plan's reliability can best explain the results. In this case, we refer to ‘reliability’ as execution reliability and not sensory reliability, which is common in cue integration theory. We have added further details explaining this in the manuscript.

“We hypothesize that this inconsistency in results can be explained using a framework inspired by an inverse optimal control framework. In this framework the motor system can switch or combine between different solutions. That is, the motor system assigns different weights to each solution and calculates a weighted sum of these solutions. Usually, to support such a framework, previous studies found the weights by fitting the weighed sum solution to behavioral data (Berret, Chiovetto et al. 2011). While we treat the problem in the same manner, we propose the Reliable Dynamics Representation (Re-Dyn) mechanism that determines the weights instead of fitting them. According to our framework, the weights are calculated by considering the reliability of each representation during dynamic generalization. That is, the motor system prefers certain representations if the execution of forces based on this representation is more robust to distortion arising from neural noise. In this process, the motor system estimates the difference between the desired generalized forces and generated generalized forces while taking into consideration noise added to the state variables that equivalently define the forces.”

A more rational model might be based on Bayesian decision theory. Under such a model, the motor system would select motor commands that minimize some expected loss, averaging over the various possible underlying 'true' coordinate systems in which to generalize. It's not entirely clear without developing the theory a bit exactly how the proposed noise-based theory might deviate from such a Bayesian model. But the paper should more clearly explain the principles/assumptions of the proposed noise-based model and should emphasize how the model parallels (or deviates from) Bayesian-decision-theory-type models.

As we understand the reviewer's suggestion, the idea is to estimate the weight of each coordinate system based on minimizing a loss function that considers the cost of each weight multiplied by a posterior probability that represents the uncertainty in this weight value. While this is an interesting idea, we believe that in the current problem, there are no ‘true’ weight values. That is, the motor system can use any combination of weights which will be true due to the ambiguous nature of the environment. Since the force field was presented in one area of the entire workspace, there is no observation that will allow us to update prior beliefs regarding the force nature of the environment. In such a case, the prior beliefs might play a role in the loss function, but in our opinion, there is no clear rationale for choosing unequal priors except guessing or fitting prior probabilities, which will resemble any other previous models that used fitting rather than predictions.

Another significant weakness is that it's not clear how closely the weighting of the different coordinate frames needs to match the model predictions in order to recover the observed generalization patterns. Given that the weighting for a given movement direction is over- parametrized (i.e. there are 3 variable weights (allowing for decay) predicting a single observed force level, it seems that a broad range of models could generate a reasonable prediction. It would be helpful to compare the predictions using the weighting suggested by the model with the predictions using alternative weightings, e.g. a uniform weighting, or the weighting for a different posture. In fact, Fig. 7 shows that uniform weighting accounts for the data just as well as the noise-based model in which the weighting varies substantially across directions. A more comprehensive analysis comparing the proposed noise-based weightings to alternative weightings would be helpful to more convincingly argue for the specificity of the noise-based predictions being necessary. The analysis in the appendix was not that clearly described, but seemed to compare various potential fitted mixtures of coordinate frames, but did not compare these to the noise-based model predictions.

We agree with the reviewer that fitted global weights, that is, an optimal weighted average of the three coordinate systems should outperform most of the models that are based on prediction instead of fitting the data. As we showed in Figure 7 of the submitted version of the manuscript, we used the optimal fitted model to show that our noise-based model is indeed not optimal but can predict the behavioral results and not fall too short of a fitted model. When trying to fit a model across all the reported experiments, we indeed found a set of values that gives equal weights for the joints and object coordinate systems (0.27 for both), and a lower value for the Cartesian coordinate system (0.12). Considering these values, we indeed see how the reviewer can suggest a model that is based on equal weights across all coordinate systems. While this model will not perform as well as the fitted model, it can still generate satisfactory results.

To better understand if a model based on global weights can explain the combination between coordinate systems, we perform an additional experiment. In this experiment, a model that is based on global fitted weights can only predict one out of two possible generalization patterns while models that are based on individual direction-predicted weights can predict a variety of generalization patterns. We show that global weights, although fitted to the data, cannot explain participants' behavior. We report these new results in Appendix 2.

“To better understand if a model based on global weights can explain the combination between coordinate systems, we perform an additional experiment. We used the idea of experiment 3 in which participants generalize learned dynamics using a tool. That is, the arm posture does not change between the training and test areas. In such a case, the Cartesian and joint coordinate systems do not predict a shift in generalized force pattern while the object coordinate system predicts a shift that depends on the orientation of the tool. In this additional experiment, we set a test workspace in which the orientation of the tool is 90° (Appendix 2- figure 1A). In this case, for the test workspace, the force compensation pattern of the object based coordinate system is in anti-phase with the Cartesian/joint generalization pattern. Any globally fitted weights (including equal weights) can produce either a non-shifted or 90° shifted force compensation pattern (Appendix 2- figure 1B). Participants in this experiment (n=7) showed similar MPE reduction as in all previous experiments when adapting to the trigonometric scaled force field (Appendix 2- figure 1C). When examining the generalized force compensation patterns, we observed a shift of the pattern in the test workspace of 14.6° (Appendix 2- figure 1D). This cannot be explained by the individual coordinate system force compensation patterns or any combination of them (which will always predict either a 0° or 90° shift, Appendix 2- figure 1E). However, calculating the prediction of the Re-Dyn model we found a predicted force compensation pattern with a shift of 6.4° (Appendix 2- figure 1F). The intermediate shift in the force compensation pattern suggests that any global based weights cannot explain the results.”

With regard to the suggestion that weighting is changed according to arm posture, two of our results lower the possibility that posture governs the weights:

(1) In experiment 3, we tested generalization while keeping the same arm posture between the training and test workspaces, and we observed different force compensation profiles across the movement directions. If arm posture in the test workspaces affected the weights, we would expect identical weights for both test workspaces. However, any set of weights that can explain the results observed for workspace 1 will fail to explain the results observed in workspace 2. To better understand this point we calculated the global weights for each test workspace for this experiment and we observed an increase in the weight for the object coordinates system (0.41 vs. 0.5) and a reduction in the weights for the Cartesian and joint coordinates systems (0.29 vs. 0.24). This suggests that the arm posture cannot explain the generalization pattern in this case.

(2) In experiments 2 and 3, we used the same arm posture in the training workspace and either changed the arm posture (experiment 2) or did not change the arm posture (experiment 3) in the test workspaces. While the arm posture for the training workspace was the same, the force generalization patterns were different between the two experiments, suggesting that the arm posture during the training phase (adaptation) does not set the generalization weights.

Overall, this shows that it is not specifically the arm posture in either the test or the training workspaces that set the weights. Of course, all coordinate models, including our noise model, will consider posture in the determination of the weights.

Reviewer #2 (Public Review):

Leib & Franklin assessed how the adaptation of intersegmental dynamics of the arm generalizes to changes in different factors: areas of extrinsic space, limb configurations, and 'object-based' coordinates. Participants reached in many different directions around 360{degree sign}, adapting to velocity-dependent curl fields that varied depending on the reach angle. This learning was measured via the pattern of forces expressed in upon the channel wall of "error clamps" that were randomly sampled from each of these different directions. The authors employed a clever method to predict how this pattern of forces should change if the set of targets was moved around the workspace. Some sets of locations resulted in a large change in joint angles or object-based coordinates, but Cartesian coordinates were always the same. Across three separate experiments, the observed shifts in the generalized force pattern never corresponded to a change that was made relative to any one reference frame. Instead, the authors found that the observed pattern of forces could be explained by a weighted combination of the change in Cartesian, joint, and object-based coordinates across test and training contexts.

In general, I believe the authors make a good argument for this specific mixed weighting of different contexts. I have a few questions that I hope are easily addressed.

Movements show different biases relative to the reach direction. Although very similar across people, this function of biases shifts when the arm is moved around the workspace (Ghilardi, Gordon, and Ghez, 1995). The origin of these biases is thought to arise from several factors that would change across the different test and training workspaces employed here (Vindras & Viviani, 2005). My concern is that the baseline biases in these different contexts are different and that rather the observed change in the force pattern across contexts isn't a function of generalization, but a change in underlying biases. Baseline force channel measurements were taken in the different workspace locations and conditions, so these could be used to show whether such biases are meaningfully affecting the results.

We agree with the reviewer and we followed their suggested analysis. In the following figure (Author response image 1) we plotted the baseline force compensation profiles in each workspace for each of the four experiments. As can be seen in this figure, the baseline force compensation is very close to zero and differs significantly from the force compensation profiles after adaptation to the scaled force field.

Author response image 1.

Baseline force compensation levels for experiments 1-4. For each experiment, we plotted the force compensation for the training, test 1, and test 2 workspaces.

Experiment 3, Test 1 has data that seems the worst fit with the overall story. I thought this might be an issue, but this is also the test set for a potentially awkwardly long arm. My understanding of the object-based coordinate system is that it's primarily a function of the wrist angle, or perceived angle, so I am a little confused why the length of this stick is also different across the conditions instead of just a different angle. Could the length be why this data looks a little odd?

Usually, force generalization is tested by physically moving the hand in unexplored areas. In experiment 3 we tested generalization using a tool which, as far as we know, was not tested in the past in a similar way to the present experiment. Indeed, the results look odd compared to the results of the other experiments, which were based on the ‘classic’ generalization idea. While we have some ideas regarding possible reasons for the observed behavior, it is out of the scope of the current work and still needs further examination.

Based on the reviewer’s comment, we improved the explanation in the introduction regarding the idea behind the object based coordinate system

“we could represent the forces as belonging to the hand or a hand-held object using the orientation vector connecting the shoulder and the object or hand in space (Berniker, Franklin et al. 2014).” The reviewer is right in their observation that the predictions of the object-based reference frame will look the same if we change the length of the tool. The object-based generalized forces, specifically the shift in the force pattern, depend only on the object's orientation but not its length (equation 4).

The manuscript is written and organized in a way that focuses heavily on the noise element of the model. Other than it being reasonable to add noise to a model, it's not clear to me that the noise is adding anything specific. It seems like the model makes predictions based on how many specific components have been rotated in the different test conditions. I fear I'm just being dense, but it would be helpful to clarify whether the noise itself (and inverse variance estimation) are critical to why the model weights each reference frame how it does or whether this is just a method for scaling the weight by how much the joints or whatever have changed. It seems clear that this noise model is better than weighting by energy and smoothness.

We have now included further details of the noise model and added to Figure 1 to highlight how noise can affect the predicted weights. In short, we agree with the reviewer there are multiple ways to add noise to the generalized force patterns. We choose a simple option in which we simulate possible distortions to the state variables that set the direction of movement. Once we calculated the variance of the force profile due to this distortion, one possible way is to combine them using an inverse variance estimator. Note that it has been shown that an inverse variance estimator is an ideal way to combine signals (e.g., Shahar, D.J. (2017) https://doi.org/10.4236/ojs.2017.72017). However, as we suggest, we do not claim or try to provide evidence for this specific way of calculating the weights. Instead, we suggest that giving greater weight to the less variable force representation can predict both the current experimental results as well as past results.

Are there any force profiles for individual directions that are predicted to change shape substantially across some of these assorted changes in training and test locations (rather than merely being scaled)? If so, this might provide another test of the hypotheses.

In experiments 1-3, in which there is a large shift of the force compensation curve, we found directions in which the generalized force was flipped in direction. That is, clockwise force profiles in the training workspace could change into counter-clockwise profiles in the test workspace. For example, in experiment 2, for movement at 157.5° we can see that the force profile was clockwise for the training workspace (with a force compensation value of 0.43) and movement at the same direction was counterclockwise for test workspace 1 (force compensation equal to -0.48). Importantly, we found that the noise based model could predict this change.

Author response image 2.

Results of experiment 2. Force compensation profiles for the training workspace (grey solid line) and test workspace 1 (dark blue solid line). Examining the force nature for the 157.5° direction, we found a change in the applied force by the participants (change from clockwise to counterclockwise forces). This was supported by a change in force compensation value (0.43 vs. -0.48). The noise based model can predict this change as shown by the predicted force compensation profile (green dashed line).

I don't believe the decay factor that was used to scale the test functions was specified in the text, although I may have just missed this. It would be a good idea to state what this factor is where relevant in the text.

We added an equation describing the decay factor (new equation 7 in the Methods section) according to this suggestion and Reviewer 1 comment on the same issue.

Reviewer #3 (Public Review):

The author proposed the minimum variance principle in the memory representation in addition to two alternative theories of the minimum energy and the maximum smoothness. The strength of this paper is the matching between the prediction data computed from the explicit equation and the behavioral data taken in different conditions. The idea of the weighting of multiple coordinate systems is novel and is also able to reconcile a debate in previous literature.

The weakness is that although each model is based on an optimization principle, but the derivation process is not written in the method section. The authors did not write about how they can derive these weighting factors from these computational principles. Thus, it is not clear whether these weighting factors are relevant to these theories or just hacking methods. Suppose the author argues that this is the result of the minimum variance principle. In that case, the authors should show a process of how to derive these weighting factors as a result of the optimization process to minimize these cost functions.

The reviewer brings up a very important point regarding the model. As shown below, it is not trivial to derive these weights using an analytical optimization process. We demonstrate one issue with this optimization process.

The force representation can be written as (similar to equation 6):

We formulated the problem as minimizing the variance of the force according to the weights w:

In this case, the variance of the force is the variance-covariance matrix which can be minimized by minimizing the matrix trace:

We will start by calculating the variance of the force representation in joints coordinate system:

Here, the force variance is a result of a complex function which include the joints angle as a random variable. Expending the last expression, although very complex, is still possible. In the resulted expression, some of the resulted terms include calculating the variance of nested trigonometric functions of the random joint angle variance, for example:

In the vast majority of these cases, analytical solutions do not exist. Similar issues can also raise for calculating the variance of complex multiplication of trigonometric functions such as in the case of multiplication of Jacobians (and inverse Jacobians)

To overcome this problem, we turned to numerical solutions which simulate the variance due to the different state variables.

In addition, I am concerned that the proposed model can cancel the property of the coordinate system by the predicted variance, and it can work for any coordinate system, even one that is not used in the human brain. When the applied force is given in Cartesian coordinates, the directionality in the generalization ability of the memory of the force field is characterized by the kinematic relationship (Jacobian) between the Cartesian coordinate and the coordinate of interest (Cartesian, joint, and object) as shown in Equation 3. At the same time, when a displacement (epsilon) is considered in a space and a corresponding displacement is linked with kinematic equations (e.g., joint displacement and hand displacement in 2 joint arms in this paper), the generated variances in different coordinate systems are linked with the kinematic equation each other (Jacobian). Thus, how a small noise in a certain coordinate system generates the hand force noise (sigma_x, sigma_j, sigma_o) is also characterized by the kinematics (Jacobian). Thus, when the predicted forcefield (F_c, F_j, F_o) was divided by the variance (F_c/sigma_c^2, F_j/sigma_j^2, F_o/sigma_o^2, ), the directionality of the generalization force which is characterized by the Jacobian is canceled by the directionality of the sigmas which is characterized by the Jacobian. Thus, as it has been read out from Fig*D and E top, the weight in E-top of each coordinate system is always the inverse of the shift of force from the test force by which the directionality of the generalization is always canceled.

Once this directionality is canceled, no matter how to compute the weighted sum, it can replicate the memorized force. Thus, this model always works to replicate the test force no matter which coordinate system is assumed. Thus, I am suspicious of the falsifiability of this computational model. This model is always true no matter which coordinate system is assumed. Even though they use, for instance, the robot coordinate system, which is directly linked to the participant's hand with the kinematic equation (Jacobian), they can replicate this result. But in this case, the model would be nonsense. The falsifiability of this model was not explicitly written.

As explained above, calculating the variability of the generalized forces given the random nature of the state variable is a complex function that is not summarized using a Jacobian. Importantly the model is unable to reproduce or replicate the test force arbitrarily. In fact, we have already shown this (see Appendix 1- figure 1), where when we only attempt to explain the data with either a single coordinate system (or a combination of two coordinate systems) we are completely unable to replicate the test data despite using this model. For example, in experiment 4, when we don’t use the joint based coordinate system, the model predicts zero shift of the force compensation pattern while the behavioral data show a shift due to the contribution of the joint coordinate system. Any arbitrary model (similar to the random model we tested, please see the response to Reviewer 1) would be completely unable to recreate the test data. Our model instead makes very specific predictions about the weighting between the three coordinate systems and therefore completely specified force predictions for every possible test posture. We added this point to the Discussion

“The results we present here support the idea that the motor system can use multiple representations during adaptation to novel dynamics. Specifically, we suggested that we combine three types of coordinate systems, where each is independent of the other (see Appendix 1- figure 1 for comparison with other combinations). Other combinations that include a single or two coordinate system can explain some of the results but not all of them, suggesting that force representation relies on all three with specific weights that change between generalization scenarios.”

Author Response:

Reviewer #1 (Public Review):

Jo et al. use a combination of micropatterned differentiation, single cell RNA sequencing and pharmacological treatments to study primordial germ cell (PGC) differentiation starting from human pluripotent stem cells. Geometrical confinement in conjunction with a pre-differentiation step allowed the authors to reach remarkable differentiation efficiencies. While Minn et al. already reported the presence of PGC-like cells in micropatterned differentiating human cultures by scRNA-Seq (as acknowledged by the authors), the careful characterization of the PGC-like population using immunostainings and scRNA-Seq is a strength of the manuscript. The attempt at mechanistically dissecting the signaling pathways required for PGC fate specification is somehow weaker. The authors do not present sufficient evidence supporting the ability to specify PGC fate in the absence of Wnt signaling and the importance of the relative signaling levels of BMP to Nodal pathways; the wording of the text should be amended to better reflect the presented evidence or the authors should perform additional experiments to support these claims.

We thank the reviewer for this comment. As described in more detail in the responses below, we have significantly strengthened the evidence for the rescue of Wnt inhibition by exogenous Activin treatment and have nuanced our interpretation. We believe that our data suggest low levels of Wnt may be required directly for PGC competence, while much higher levels are required indirectly to induce Nodal, with Nodal signaling being the limiting factor for PGC specification under the reference condition with BMP4 treatment only. We describe this in detail in the manuscript but summarize it here in a simplified diagram:

We have also carried out additional experiments that match model predictions demonstrating the importance of relative BMP and Nodal signaling levels and amended the text to reflect the evidence as suggested. More details are provided below.

The molecular characterization of why colonies confined to small areas differentiate much better would greatly increase the biological significance of the manuscript (the technical achievement of reaching such efficiency is impressive on its own).

We believe the mechanism by which cells confined to small colonies differentiate to PGCLCs more efficiently is explained by a larger fraction of the cells being exposed to the necessary levels of BMP and Nodal signaling. In large colonies BMP signaling was shown to be restricted to a distance of 50-100 um from the colony edge through receptor localization and secretion of inhibitors (Etoc et al, Dev Cell 2016). From this one would expect that BMP signaling extends a similar distance from the edge in small colonies, so that a larger fraction of cells are receiving the BMP signal needed to differentiate to PGCLCs. Because it was not previously shown that the length scale of BMP signaling and downstream signals are preserved as colony size is reduced, we have now included an analysis of BMP signaling (pSmad1 levels) and Nodal signaling (nuclear Smad2/3 levels) as a function of colony size (Figure 5i-k). This confirms our hypothesis and provides a potential mechanism.

The authors propose a mathematical model based on BMP and Nodal signaling that qualitatively recapitulate their experimental data. While the authors should be commended for providing examples of other simple models that do not fully recapitulate their data, it would have been nice to see an attempt at challenging quantitatively the model. In particular, the authors do not take advantage of the ability to explore in a more systematic manner the BMP/Nodal phase space with their system.

We thank the reviewer for this suggestion. Experimentally we have now tested the effect of 5x5 = 25 different combinations of BMP and Activin doses on PGCLC differentiation. We then challenged the mathematical model to predict the ‘phase diagram’ corresponding to this data with good agreement (Figure 6f). It is important to note here that the model was fit using only data with 50ng/ml of BMP, making this a true prediction. We also point out that the phase diagram predicted in this way is different from the one shown in Figure 6d, not only because of the lower resolution, but because Figure 6f shows the steady state after uniform stimulation in space and time (i.e. the response on the very edge), whereas the predicted phase diagram shows average expression at 42h in a 100um range from the colony edge using the previously measured spatiotemporal gradients of BMP and Activin response. Finally, the data in Figure 6f shows mean expression levels as opposed to the percentage double positive cells for the same data in Figure 4q because our model does not simulate individual cells and noise, only allowing us to compare mean expression. We explain all this in the text now. As a minor change to facilitate comparison of data and model we have now plotted the concentrations of BMP and Activin in Figure 6 rather than the scaled model parameters from 0 to 1, we also further optimized the model parameters without qualitative changes.

The authors' claim that PGCLC formation can be rescued by exogenous Activin when blocking endogenous Wnt production is surprising given the literature. The authors only show that they can restore a TFAP2C+SOX17+ population but do not actually stain for an established germ cell marker. It appears essential to perform a PRDM1 staining in these conditions (Figure 4A) to unambiguously identify this population.

We have significantly extended our analysis of the effect of WNT inhibition and subsequent rescue of PGCs by Activin treatment. This includes staining for TFAP2C,NANOG,PRDM1 and staining for LEF1 as a measure of WNT signaling. Figure 4 and Figure 4—figure supplement 1 now also include treatment with IWR-1, a different small molecule inhibitor of WNT signaling, as well inhibition by IWR-1 and IWP2 at different times and different doses.

The authors only provide weak evidence that the fates depend on the relative signaling levels of BMP and Nodal. Indeed, fewer cells acquire a fate the lower BMP concentration they use, including the fates marked by Sox17 expression. It would more convincing to show the assay of Figure 4F for a range of BMP concentrations at which the overall differentiation works sufficiently well.

As suggested, we have now included a range of BMP concentrations. The reduction in PGCs at lower BMP doses is in line with our model and does not contradict a dependence on the relative signaling levels of BMP and Nodal by which we mean that optimal dose of Activin for PGCLC specification depends on the level of BMP and vice versa. We have amended the text to state this more clearly.

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Author Response

Reviewer #1:

This is a very timely paper that addresses an important and difficult-to-address question in the decision-making field - the degree to which information leakage can be strategically adapted to optimise decisions in a task-dependent fashion. The authors apply a sophisticated suite of analyses that are appropriate and yield a range of very interesting observations. The paper centres on analyses of one possible model that hinges on certain assumptions about the nature of the decision process for this task which raises questions about whether leak adjustments are the only possible explanation for the current data. I think the conclusions would be greatly strengthened if they were supported by the application and/or simulation of alternative model structures.

We thank the reviewer for this positive appraisal of our study. We now entirely agree with their central comment about whether leak adjustments are the only (or even the best) explanation for the current data. We hope that the additional modelling sections that we have discussed in response to main comment 1 above have strengthened the paper. We have responded point-by-point to their public review, as this contained their main recommendations for revision.

The behavioural trends when comparing blocks with frequent versus rare response periods seem difficult to tally with a change in the leak. […] Are there other models that could reproduce such effects? For example, could a model in which the drift rate varies between Rare and Frequent trials do a similar or better job of explaining the data?

We can see why the reviewer has advocated for a possible change of drift rate (or ‘gain’ applied to sensory evidence) between conditions to explain our behavioural findings. We found, however, that changes in drift rate could elicit qualitatively similar changes in integration kernels to changes in decision threshold:

Author response image 1.

Changes in gain applied to incoming sensory evidence (A parameter in model) have similar effects on recovered integration kernels from Ornstein-Uhlenbeck simulation as changes in decision threshold.

The likely reason for this is that the overall probability of emitting a response at any point in the continuous decision process is determined by the ratio of accumulated evidence to decision threshold. A similar logic applies to effects on reactions times and detection probability (main figure 2): increasing sensory gain/decreasing decision threshold will lead to faster reaction times and increased detection probability during response periods.

Both parameters may even have a similar effect on ‘false alarms’, because (as the reviewer notes below) false alarms in our paradigm are primarily being driven by the occurrence of stimulus changes as well as internal noise. In fact, the false alarm findings mean it is difficult to fully reconcile all of our behavioural findings in terms of changes in a single set of model parameters in the O-U process. It is possible that other changes not considered within our model (such as expectations of hazard rates of inter-response intervals leading to dynamic thresholds etc.) may have had a strong impact upon the resulting false alarm rates. A full exploration of different variations in O-U model (with varying urgency signals, hazard rates, etc.) is beyond the scope of this paper.

For this reason, we have decided in our new modelling section to focus primarily on a single, well-established model (the O-U process) and explore how changes in leak and threshold affect task performance and the resulting integration kernels. We note that this is in line with the suggestion of reviewer #2, who focussed on similar behavioural findings to reviewer #1 but suggested that we look at decision threshold rather than drift rate as our primary focus.

This ties in to a related query about the nature of the task employed by the authors. Due to the very significant volatility of the stimulus, it seems likely that the participants are not solely making judgments about the presence/absence of coherent motion but also making judgments about its duration (because strong coherent motion frequently occurs in the inter-target intervals). If that is so, then could the Rare condition equate to less evidence because there is an increased probability that an extended period of coherent motion could be an outlier generated from the noise distribution? Note that a drift rate reduction would also be expected to result in fewer hits and slower reaction times, as observed.

As mentioned above, the rare and frequent targets are indeed matched in terms of the ease with which they can be distinguished from the intervening noise intervals. To confirm this, we directly calculated the variance (across frames) of the motion coherence presented during baseline periods and response periods (until response) in all four conditions:

Author response image 2.

The average empirical standard deviation of the stimulus stream presented during each baseline period (‘baseline’) and response period (‘trial’), separated by each of the four conditions (F = frequent response periods, R = rare, L = long response periods, S = short). Data were averaged across all response/baseline periods within the stimuli presented to each participant (each dot = 1 participant). Note that the standard deviation shown here is the standard deviation of motion coherence across frames of sensory evidence. This is smaller than the standard deviation of the generative distribution of ‘step’-changes in the motion coherence (std = 0.5 for baseline and 0.3 for response periods), because motion coherence remains constant for a period after each ‘step’ occurs.

Some adjustment of the language used when discussing FAs seems merited. If I have understood correctly, the sensory samples encountered by the participants during the inter-response intervals can at times favour a particular alternative just as strongly (or more strongly) than that encountered during the response interval itself. In that sense, the responses are not necessarily real false alarms because the physical evidence itself does not distinguish the target from the non-target. I don't think this invalidates the authors' approach but I think it should be acknowledged and considered in light of the comment above regarding the nature of the decision process employed on this task.

This is a good point. We hope that the reviewer will allow us to keep the term ‘false alarms’ in the paper, as it does conveniently distinguish responses during baseline periods from those during response periods, but we have sought to clarify the point that the reviewer makes when we first introduce the term.

“Indeed, participants would occasionally make ‘false alarms’ during baseline periods in which the structure of the preceding noise stream mistakenly convinced them they were in a response period (see Figure 4, below). Indeed, this means that a ‘false alarm’ in our paradigm has a slightly different meaning than in most psychophysics experiments; rather than it referring to participants responding when a stimulus was not present, we use the term to refer to participants responding when there was no shift in the mean signal from baseline.”

And:

“The fact that evidence integration kernels naturally arise from false alarms, in the same manner as from correct responses, demonstrates that false alarms were not due to motor noise or other spurious causes. Instead, false alarms were driven by participants treating noise fluctuations during baseline periods as sensory evidence to be integrated across time, and the physical evidence preceding ‘false alarms’ need not even distinguish targets from non-targets.”

The authors report that preparatory motor activity over central electrodes reached a larger decision threshold for RARE vs. FREQUENT response periods. It is not clear what identifies this signal as reflecting motor preparation. Did the authors consider using other effectorselective EEG signatures of motor preparation such as beta-band activity which has been used elsewhere to make inferences about decision bounds? Assuming that this central ERP signal does reflect the decision bounds, the observation that it has a larger amplitude at the response on Rare trials appears to directly contradict the kernel analyses which suggest no difference in the cumulative evidence required to trigger commitment.

Thanks for this comment. First, we should simply comment that this finding emerged from an agnostic time-domain analysis of the data time-locked to button presses, in which we simply observed that the negative-going potential was greater (more negative) in RARE vs. FREQUENT trials. So it is simply the fact that it precedes each button press that we relate it to motor preparation; nonetheless, we note that (Kelly and O’Connell, 2013) found similar negative-going potentials at central sensors without applying CSD transform (as in this study). Like them, we would relate this potential to either the well-established Bereitschaftpotential or the contingent negative potential (CNV).

We agree that many other studies have focussed on beta-band activity as another measure of motor preparation, and to make inferences about decision bounds. To investigate this, we used a Morlet wavelet transform to examine the time-varying power estimate at a central frequency of 20Hz (wavelet factor 7). We repeated the convolutional GLM analysis on this time-varying power estimate.

We first examined average beta desynchonisation at a central cluster of electrodes (CPz, CP1, CP2, C1, Cz, C2) in the run-up to correct button presses during response periods. We found a reliable beta desynchonisation occurred, and, just as in the time-domain signal, this reached a greater threshold in the RARE trials than in the FREQUENT trials:

Author response image 3.

Beta desynchronisation prior to a correct response is greater over central electrodes in the RARE condition than in the FREQUENT condition.

We agree with the reviewer that this is likely indicative of a change in decision threshold between rare and frequent trials. We also note that our new computational modelling of the O-U process suggests that this in fact reconciles well with the behavioural findings (changes in integration kernels). We now mention this at the relevant point in the results section:

“As large changes in mean evidence are less frequent in the RARE condition, the increased neural response to |Devidence| may reflect the increased statistical surprise associated with the same magnitude of change in evidence in this condition. In addition, when making a correct response, preparatory motor activity over central electrodes reached a larger decision threshold for RARE vs. FREQUENT response periods (Figure 7b; p=0.041, cluster-based permutation test). We found similar effects in beta-band desynchronisation prior, averaged over the same electrodes; beta desynchronisation was greater in RARE than FREQUENT response periods. As discussed in the computational modelling section above, this is consistent with the changes in integration kernels between these conditions as it may reflect a change in decision threshold (figure 2d, 3c/d). It is also consistent with the lower detection rates and slower reaction times when response periods are RARE (figure 2 b/c).”

We did also investigate the lateralised response (left minus right beta-desynchronisation, contrasted on left minus right responses). We found, however, that we were simply unable to detect a reliable lateralised signal in either condition using these lateralised responses. We suspect that this is because we have far fewer response periods than conventional trialbased EEG experiments of decision making, and so we did not have sufficient SNR to reliably detect this signal. This is consistent with standard findings in the literature, which report that the magnitude of the lateralised signal is far smaller than the magnitude of the overall beta desynchronisation (e.g. (Doyle et al., 2005))

P11, the "absolute sensory evidence" regressor elicited a triphasic potential over centroparietal electrodes. The first two phases of this component look to have an occipital focus. The third phase has a more centroparietal focus but appears markedly more posterior than the change in evidence component. This raises the question of whether it is safe to assume that they reflect the same process.

We agree. We have now referred to this as a ‘triphasic component over occipito-parietal cortex’ rather than centroparietal electrodes.

Reviewer #2:

Overall, the authors use a clever experimental design and approach to tackle an important set of questions in the field of decision-making. The manuscript is easy to follow with clear writing. The analyses are well thought-out and generally appropriate for the questions at hand. From these analyses, the authors have a number of intriguing results. So, there is considerable potential and merit in this work. That said, I have a number of important questions and concerns that largely revolve around putting all the pieces together. I describe these below.

Thanks to the reviewer for their positive appraisal of the manuscript; we are obviously pleased that they found our work to have considerable potential and merit. We seek to address the main comments from their public review and recommendations below.

1) It is unclear to what extent the decision threshold is changing between subjects and conditions, how that might affect the empirical integration kernel, and how well these two factors can together explain the overall changes in behavior.

I would expect that less decay in RARE would have led to more false alarms, higher detection rates, and faster RTs unless the decision threshold also increased (or there was some other additional change to the decision process). The CPP for motor preparatory activity reported in Fig. 5 is also potentially consistent with a change in the decision threshold between RARE and FREQUENT. If the decision threshold is changing, how would that affect the empirical integration kernel? These are important questions on their own and also for interpreting the EEG changes.

This important comment, alongside the comments of reviewer 1 above, made us carefully consider the effects of changes in decision threshold on the evidence integration kernel via simulation. As discussed above (in response to ‘essential revisions for the authors’), we now include an entirely new section on how changes in decision threshold and leak may affect the evidence integration kernel, and be used to optimise performance across the different sensory environments. In particular, we agree with the reviewer that the motor preparatory activity that differs between RARE and FREQUENT is consistent with a change in decision threshold, and our simulations have suggested that our behavioural findings on evidence integration are also consistent with this change as well. These are detailed on pp.1-4 of the rebuttal, above.

2) The authors find an interesting difference in the CPP for the FREQUENT vs RARE conditions where they also show differences in the decay time constant from the empirical integration kernel. As mentioned above, I'm wondering what else may be different between these conditions. Do the authors have any leverage in addressing whether the decision threshold differs? What about other factors that could be important for explaining the CPP difference between conditions? Big picture, the change in CPP becomes increasingly interesting the more tightly it can be tied to a particular change in the decision process.

We fully agree with the spirit of this comment, and we’ve tried much more carefully to consider what the influences of decision threshold and leak would be on our behavioural analyses. As discussed in the response to reviewer 1, we think that the negative-going potential at the time of responses (which is greater in RARE vs. FREQUENT, main figure 7b, and mirrored by equivalent changes in beta desynchronisation, see Reviewer Response Figure 5 above) are both reflective of a change in decision threshold between RARE and FREQUENT conditions. We have tried to make this link explicit in the revised results section:

“As large changes in mean evidence are less frequent in the RARE condition, the increased neural response to |Devidence| may reflect the increased statistical surprise associated with the same magnitude of change in evidence in this condition. In addition, when making a correct response, preparatory motor activity over central electrodes reached a larger decision threshold for RARE vs. FREQUENT response periods (Figure 7b; p=0.041, cluster-based permutation test). We found similar effects in beta-band desynchronisation prior, averaged over the same electrodes; beta desynchronisation was greater in RARE than FREQUENT response periods. As discussed in the computational modelling section above, this is consistent with the changes in integration kernels between these conditions as it may reflect a change in decision threshold (figure 2d, 3c/d). It is also consistent with the lower detection rates and slower reaction times when response periods are RARE (figure 2 b/c).”

I'll note that I'm also somewhat skeptical of the statements by the authors that large shifts in evidence are less frequent in the RARE compared to FREQUENT conditions (despite the names) - a central part of their interpretation of the associated CPP change. The FREQUENT condition obviously has more frequent deviations from the baseline, but this is countered to some extent by the experimental design that has reduced the standard deviation of the coherence for these response periods. I think a calculation of overall across-time standard deviation of motion coherence between the RARE and FREQUENT conditions is needed to support these statements, and I couldn't find that calculation reported. The authors could easily do this, so I encourage them to check and report it.

See Author response image 2.

3) The wide range of decay time constants between subjects and the correlation of this with another component of the CPP is also interesting. However, in trying to interpret this change in CPP, I'm wondering what else might be changing in the inter-subject behavior. For instance, it looks like there could be up to 4 fold changes in false alarm rates. Are there other changes as well? Do these correlate with the CPP? Similar to my point above, the changes in CPP across subjects become increasingly interesting the more tightly it can be tied to a particular difference in subject behavior. So, I would encourage the authors to examine this in more depth.

Thanks for the interesting suggestion. We explored whether there might be any interindividual correlation in this measure with the false alarm rate across participants, but found that there was no such correlation. (See Author response image 4; plotting conventions are as in main figure 9).

Author response image 4.

No evidence of between-subject correlations in CPP responses and false alarm rates, in any of the four conditions.

We hope instead that the extended discussion of how the integration kernel should be interpreted (in light of computational modelling) provides at least some increased interpretability of the between-subject effects that we report in figure 9.

Reviewer #3 (Public Review):

The main strength is in the task design which is novel and provides an interesting approach to studying continuous evidence accumulation. Because of the continuous nature of the task, the authors design new ways to look at behavioral and neural traces of evidence. The reverse-correlation method looking at the average of past coherence signals enables us to characterize the changes in signal leading to a decision bound and its neural correlate. By varying the frequency and length of the so-called response period, that the participants have to identify, the method potentially offers rich opportunities to the wider community to look at various aspects of decision-making under sensory uncertainty.

We are pleased that the reviewer agrees with our general approach as a novel way of characterising various aspects of decision-making under uncertainty.

The main weaknesses that I see lie within the description and rigor of the method. The authors refer multiple times to the time constant of the exponential fit to the signal before the decision but do not provide a rigorous method for its calculation and neither a description of the goodness of the fit. The variable names seem to change throughout the text which makes the argumentation confusing to the reader. The figure captions are incomplete and lack clarity.

We apologise that some of our original submission was difficult to follow in places, and we are very grateful to the reviewer for their thorough suggestions for how this could be improved. We address these in turn below, and we hope that this answers their questions, and has also led to a significant improvement in the description and rigour of the methodology.

Author Response

Reviewer #2 (Public Review):

I am not a specialist in cryo-EM, so cannot comment on the technicalities of the structure reconstruction or methods used. I thus focus on the conclusions and observations that the authors provide in the manuscript and their relevance to functional photosynthesis.

The authors attempt to resolve the structure of PSII from Dunaliella and noticed that three types of PSII could be identified: two conformational states, and a stacked configuration. There is no doubt that these structures add to our current knowledge of PSII and that they exist in abundance upon solubilisation of the sample. My main issue however is the relevance to in vivo conditions, and the efforts to exclude the possibility that pigment loss and conformational states and stacking are a reflection of ex-vivo manipulations.

Our compact model contains 202 Chls molecules while the stretched conformation contains 206 Chls. All of the differences in Chl binding are attributed to CP29. We have compiled a table enumerating the different CP29 structures currently available from plants and green alga at similar resolution to our work (Supplementary table 2). In the larger plant complexes (C2S2M2) CP29 contains 14 chls, while CP29 in smaller C2S2 complexes contains 10-13 chls, so it appears the some chl loss from CP29 is associated with the release of LHCIIM. In the green alga structures, CP29 contains less chls in general and shows a similar trend. The currently published structure most relevant to our work contains 8 chls (6KAC), a somewhat lower amount then both the compact and stretched models (9 and 11 chls, respectively). The stretched orientation, which is the closest match to the known PSII core arrangement, therefore contains more chls than comparable models. While the in-vivo configuration is not known in the sense that it could contain more chls, the current structure is apparently the closest representation of it.

The presence of CP29 with lower chls content in the chlamy C2S2 (6KAC, which is in a stretched orientation) supports a conclusion that pigment loss from CP29 alone is not sufficient to trigger the stretch to compact transition although it is associated with it. In general, the precise orientation of CP29 is variable and seem to depend on the binding of additional LHCII, it is possible that some chl loss is accompanied with these changes in vivo.

I see a number of questions pertaining to this work. Starting from the two conformations of PSII, compact and stretched, the authors say that both are highly active based on oxygen measurements at a saturating light intensity. In the meantime, they report large variations in the chl content and positions of the chlorophyll molecules in these structures (also compared to other known PSIIs). This gives the impression that one can lose two chlorophylls, and freely modify the distance between others without losing efficiency, certainly a risky conclusion. Are the samples highly active also in light-limiting conditions? It is thought that even tiny movements and alterations in chl-chl distances alter their coupling and spectral properties, how come the variations in this report are so huge? In other words, the assay tests the charge separation activity of the PSII RC in the preps, but not the light-harvesting efficiency.

The chl content differences reported in this work amounts to 2%. In our opinion this represents quite a low variation in pigment content, which exist in virtually any experiment involving large complexes. We agree that measurements of activity in limiting light conditions are interesting, however this goes beyond the scope of the current work. Light harvesting efficiency in PSII is known to vary substantially as a result of additional mechanisms (NPQ in some of its forms), not associated with chl loss or gain. While the formation of quenching centers is attributed to small structural changes within specific pigment protein complexes, what we are showing in this work are structural changes between pigment protein complexes. These can affect transfer rates between the different complexes but are distinct from the structural changes thought to accompany the formation of quenching centers within specific pigment protein complexes.

How does one ascertain that the lost chlorophyll molecules in CP29 are not a preparation error? Does slightly increasing the detergent concentration impact the proportion of stretched:compact forms?

The effect of detergent concentration on the proportion of the different forms was not tested directly. However, we do not detect many differences in lipids or bound detergent molecules content between the two conformations, suggesting that for these “ligands” the differences are not substantial. We can only distinguish these two forms at the very last stages of data processing, at the present state of cryoEM cost and time availability, mapping the effect of detergent concentration on the different orientations is outside our reach.

On a similar note, how do the authors exclude that a certain interaction with this type of grid impacts the distribution of these complexes? Is it identical to a biologically separate preparation of algae? In case of discoveries of this type, it is of high importance to exclude as many possibilities of non-native conditions or influences on the structure.

It’s hard to completely exclude grid and sample preparation issues. However, we employed relatively standard grids and vitrification conditions. The observed complexes are embedded in vitrified ice and do not interact with the grid directly. The differences we observed are mainly in the orientations of the PSII cores, all the interactions between PSII subunits within each core are preserved and agree with previously published structures. Since the interactions within the core and between cores involve the same physical principles, we think its fairly conservative to think that the observed core orientations are not an artefact of sample preparation.

I would further like to encourage the authors to elaborate on the CP29 phosphorylation. What is the proportion of PSIIcomp that are phosphorylated? I assume it is not 100%, as in this case, the authors would propose that this is the effect that modulates between compact and stretched architectures.

Its difficult to estimate the proportion of observed phosphorylation/sulfinylation. To be detected in maps, most of the residues (above 50%) are probably modified. We attempted to estimate this by refining the atom occupancies of the Pi molecule on Ser84 and the oxygens attached to Cys218, both values suggested that about 70% of the complexes are modified. With regards to the possibility that these modifications can promote the formation of the compact state, we think that this is certainly a possibility, since these modifications were detected in this state and are in close proximity to each other. However, this can also result from the resolution differences of the maps and the structural implications of both modifications are hard to predict. At this point we prefer to note their existence without further interpretations.

In line 290, the authors highlight the structural heterogeneity within the two groups' PSII conformations. I would like to see how does the distribution look like for all the structures together: are the two (stretched and compact) specifically forming two heterogenous distributions? Or is it possible that the distribution between the two is quasi-continuous? In other words, if the structures are not perfectly defined, how do the authors decide that two- and not more or less subtypes exist?

We went back and refined the initial particle group (containing both compact and stretched orientations) using multibody with masks defining the two PSII monomers. This analysis showed the expected two peaks only in the first Principal components which accounted for ~38% of the variance in the dataset.

Multibody refinement carried out on the combined particle dataset shows one very large PC accounting for about 38% of the variance and the presence of two distinct peaks in the particle distribution of the first PC.

From this analysis it’s clear that there are two distinct classes in this particle set (as expected), as none of the other PC’s shows any signs of multiple peaks, this analysis suggests that two distinct models are the best representation of this eukaryotic PSII. Whether these are quasi continuous or distinct is more complex. There is continuity in this representation (particle distributions along PC), a different picture may appear if characters such as CP29 state are considered, but the size of CP29 and the remaining heterogeneity does not provide enough signal to carry out this classification at the moment.

Considering the stacked PSII, I also have a few concerns. Contrary to previous studies the authors do not assign a functional role to the stacking beyond the structural aspect. This could be better backed by a discussion about the closest chlorophyll a molecules across the stacked PSII, which given the rather large distance shown in fig. 4L seems to be too large for any EET across the stromal gap.

The closest chl-chl distance that we can measure in the stacked PSII dimer is ~54 Å, with most distances at the ~70 Å range, making EET between staked complexes very slow. We have added a statement clarifying this to our manuscript. In our opinion a structural role for the staked PSII dimer is more likely.

There is a report that suggests the presence of some density between the stacked PSII - could the authors comment on the differences between it and their work? Are the angles and positions conserved between these types of stacks? https://doi.org/10.1038/s41598-017-10700-8

We referred to Albanese et al, in our manuscript. We isolated the C2S2 complex from green alga, the analysis in Albanese et al was done on C2S2M1 complexes from pea and this can account for some of the differences. At any rate, our conclusion that we don’t find any evidence for protein linkers in the stacked complex is stated clearly. The angles described in Albanese et al are consistent with our analysis.

Line 387, the authors state that due to the transient nature of the interactions across the stromal gap, the stacks could be "under-detected" in cryo-ET data. This statement is in my opinion misformulated. For once, the transient interaction argument would apply the same (if not more due to changing conditions induced by the purification process) to the single particle analysis performed in this paper. Second, tomographic volumes detect hundreds of PSII in a suspended state. Any transient interaction that adds up to 25% of particle population in a steady state cell should be clearly visible, while the in situ data suggests not more than random cross-stromal-gap orientations. Of course, this can be a specificity of Chlamydomonas or a particular growth condition. The statement used by the authors could be indeed converted into: the PSII stacks are over-detected in vitro, and it is certainly a simpler explanation for their presence. It is also important to mention that PSII stacking alone is not the only reason for grana architecture - stacking with the antenna of larger complexes, absent in the authors' preparation could also contribute to grana maintenance; and auxiliary proteins such as CURT help with this issue as well. Here a recent demonstration of the importance of minor antenna should probably be also cited: https://doi.org/10.1101/2021.12.31.474624

We used the term “flexible” rather than “transient” to describe the interactions within the stacked PSII dimer. Our data (and tomographic data) do not contain any temporal component. When we used the term under-detected we refer to the fact that PSII is mainly detected by the luminal extrinsic subunits. The flexibility detected in our analysis may affect the concurrent visibly of these features in the PSII complexes making up an individual PSII stack. Specifically, Wietrzynski et al mainly analyze C2S2M2L2 complexes while our analysis only contained C2S2 complexes. It is likely that the different amount of bound LHCII affect PSII stacking as well. For example, Wietrzynski et al, show some overlap between LHCII complexes and little overlap between cores in the larger complexes they analyzed. We observe mainly core to core overlap with little LHCII overlap in the smaller C2S2, although we did not observe any states where LHC’s were not included in what appear to be the binding interface. We agree with the reviewer on the relevance Lhcb’s and CURT contributions to stacking but prefer to focus on what was directly demonstrated in our data. We clearly note that we are discussing in-vitro results.

Taking these last thoughts, I would like to finish by mentioning one more thing - almost philosophical. The authors are certainly at the forefront of the booming cryoEM revolution in biology which is profoundly changing the way we understand the living. There is absolutely zero doubt that this powerful technique is of the highest interest. But a growing number of structures of photosynthetic complexes remain puzzling, in particular with regard to their abundance in vivo (such as the PSII stacks) and functional relevance. How do we ascertain that these interactions are not due to in vitro preparation (isolation from cells, solubilisation)? Which ways can we use to try to exclude this (simple) hypothesis? I suggest that at least a small extent of biological replicas - experiments performed on separate batches, in different technical conditions, with slightly altered solubilization conditions, and so on - could shed light on the nature of these structures and their occurrence in vivo. Technical reps of the freezing+analysis pipeline could also be tried to see the variability. This would strongly reinforce this manuscript and its conclusions, and while not completely unequivocal (the stacked PSII, for example, could form upon each purification), a quantification of the effects would be of high interest.

We certainly share the reviewer hope of being able to conduct cause and effect cryoEM experiments covering a complete set of experimental parameters. This is still beyond reach in terms of time and cost. Within each cryoEM experiment, however, all the analysis is consistent and, more importantly, transparent with regards to image analysis, which is the most important factor in our opinion. Preparation artefacts are always a possibility but, in our opinion, cryoEM is not affected by them differentially compared to other techniques. As we mentioned above, the particles are being observed suspended in vitreous ice, this is not different, and one can say even better, then numerous low temperature spectroscopic observations on samples suspended in glass state or crystals obtained in the presence of high concentrations of various agents. One thing that validates structural studies are the chemical details (bond lengths and angles etc…) underlying every model which are consistence with known values to close tolerances.

Reviewer #3 (Public Review):

In this manuscript, Caspy et al. present a detailed structural analysis of eukaryotic photosystem II (PSII) isolated from the green alga Dunaliella salina. By combining single-particle cryo-EM with multibody refinement, the authors not only reveal a high-resolution (2.4Å) structure of the eukaryotic PSII, but also demonstrate alternate conformations and intrinsic flexibility of the overall complex. Stretched and compact conformations of the PSII dimer were readily identified within the single-particle dataset. From this structural analysis, the authors propose that excitation energy transfer properties may be modulated by changes in transfer distance between key chlorophyll molecules observed in different conformational states of the PSII dimer. Due to the high resolution of the maps obtained, the authors identify post-translational modifications and a sodium binding site based on the observed cryo-EM maps. Additionally, the authors analyze PSII complexes in stacked and unstacked configurations, and find that compact and stretched states also exist within the stacked PSII complexes. From their cryo-EM maps, the authors demonstrate that there is no direct protein-protein interaction between stacked PSII complexes, and rather propose a model wherein long-range electrostatic interactions mediated by divalent cations such as magnesium, can facilitate PSII stacking.

The conclusions and models presented in the manuscript are mostly well justified by the data. The cryo-EM maps are high quality and the models appear generally well refined. However, some aspects of data processing and analysis, as well as the resultant conclusions need to be clarified.

1) In general, it is not clear from the cryo-EM processing workflow (suppl. Fig 1) or the methods section when exactly symmetry was applied during 3D classification and refinement. In the case of C2S2 unstacked particles, when was symmetry first applied in the overall processing workflow? To identify the compact and stretched configurations of C2S2, did the 3D classification without alignment (and/or the refinement preceding this classification) have C2 symmetry applied? If so, have you considered the possibility that some particles may actually be asymmetric in some regions?

We modified figure S1 to clearly indicate the use of symmetry and particle expansion. In general, we refined most of the particle sets without symmetry (C1). At the final processing stage of the unstacked PSII sets, after we separated both conformations, we used C2 symmetry to expand the data, this was followed by multibody refinement. No symmetry or symmetry expansion was used for the stacked PSII particle sets.

2) Following multibody refinement in Relion individual maps and half-maps for each body will be generated. There is no mention in the methods of how these individual maps for each C2S2 "monomer" were combined to produce an overall map of the dimer following multibody refinement. There are several methods currently used to combine such maps, including taking the maximum or average of the two maps or using a model-based approach in phenix. The authors should be explicit about the method they used, any potential artifacts that may develop from this map combination process, and/or the interface between masks used in multibody refinement.

We used phenix.combined_focused_maps to combine the maps. This is now indicated in the method section.

3) In addition to the point raised above, following multibody refinement there will be an individual FSC curve and resolution for each body. However, in supplemental figure 2 and supplemental table 1, only a single FSC curve and resolution are reported. Are these FSC curves/resolutions only reported for the better of the two bodies? If not, how was a single resolution calculated for the overall map of combined bodies?

Both FSC curves were calculated and were highly similar, as expected following C2 expansion. This can also be evaluated from the local resolution maps which are highly similar between the two bodies. The reported resolutions are all taken from the displayed FSC curves generated through relion PostProcess.

4) One of the major conclusions from the 3D classification and multibody refinement is that conformational changes and inherent flexibility of the PSII dimers have the potential to change distances between cofactors in the complex, ultimately leading to altered excitation energy transfer. However, it is unclear whether or not the authors believe one conformation over another may more readily support the evolution of oxygen. It would be nice if the authors could elaborate slightly upon this topic in the discussion.

As discussed above the structural changes associated with the formation of quenching centers are not expected to be detected in the current work. The changes we observe can however affect the transfer to such centers and by doing so can play an important part in PSII biology. We do not detect any changes around the OEC and we don’t find any reason to think the two conformations are different with respect to their ETC.

5) Along the lines of point 4 above, on line 95 the authors claim that "the high specific activity of 816 umol O2/ (mg Chl * hr) suggest that" both the C2S2 compact and stretched conformation are highly active. However, it is not clear to me why this measure of specific activity would suggest that both PSII conformations should have "high" activity. Maybe a reference here would help guide readers to previous measures of specific activity?

Looking at specific activity from previously published structural studies on eukaryotic PSII we find that Sheng et al, 2019 reported on a specific activity of 272 mol O2/ (mg Chl * hr), this difference can stem partially from the presence of larger complexes in their preparation and is comparable to the activity that we measured in our As fraction (276 mol O2/ (mg Chl * hr), Figure 1-figure supplement 9). Reported specific activity values from plants (Pisum sativum) are also similar, Su et al, reported on a maximal value of 288 mol O2/ (mg Chl * hr), again, for larger complexes which can explain some of the difference. However, the specific activity measured for the C2S2 PSII isolated in the current study is 2.8 X higher than this value, more than the differences in chl content which ranges between 1.5 X to 2 X in favor of the larger complexes. If either one of the conformations is not as active, it would only mean that the other conformation will display even higher specific activity which seems less likely. In addition, we find no difference around the oxygen evolution center or in the peripheral luminal subunits in both the shape or map strength so both orientations show highly similar structures around these regions which determine the oxygen evolution activity.

6) It is claimed that "more than 2100 water molecules were detected in the C2S2 compressed model", and the water distribution is shown in Figure 3. Obtaining resolutions capable of visualizing waters with cryo-EM is still a significant challenge. Upon visual inspection of the map supplied, it appears that several of the waters that were built into the atomic model simply do not have supporting peaks in the coulomb potential map above the level of noise. While some of the modeled waters are certainly supported by the map, in my opinion, there are many waters that simply are not, or at best are questionable. What method or tool was originally used to build waters into the model, and how were these waters subsequently validated during structure refinement?

We followed standard methods for water placement and refinement in the preparation of the model, in addition to manually curating the water structure. However, in light of the reviewer comment we undertook additional rounds of refinement and inspection of the water molecules in the model. We removed a few hundred water molecules so that the total number of water molecules is now around 1700. All the water molecules in the present model should be well supported at maps values higher then 2.5 sigma and in our opinion the current water model should be regarded as conservative and underestimates the number of bound water molecules. This also led to some improvements in additional validation statistics of the model which are listed in the Table 1. The new model has been deposited in the PDB and the new PDB validation report is included in our resubmission.

7) The authors claim to identify several unique map densities during model building. One of these is a sodium ion close to the OEC, which is coordinated by D1-His337, several backbone carbonyls, and a water molecule. When looking closely at the cryo-EM map supplied, it appears that the coulomb potential map is quite weak for this sodium, and is only visible at quite low contour levels. In fact, the features for the coordinating water, and chloride ions located ~7-9A away are much stronger than the sodium. Do the authors have any explanation for why the cryo-EM map is significantly weaker for the sodium compared to the coordinating water or chloride ions in the same general vicinity? Similar to what they did for the other post-translational modifications, the authors should consider showing the actual cryo-EM map for the bound sodium in supplemental Figure 10 a,b.

Our main support for the placement of a Na+ ion in this location stems from the analysis of Wang et al. Our maps show the presence of a density which is discernible at 4 σ with an elongated shape suggesting the presence of multiple atoms/waters. Although in principle positive ions should have very strong densities in cryoEM maps due to their interactions with electrons, other factors such as occupancy, coordination and b-factor also play a role making the distinction between water and sodium complicated and case specific. The sodium peak is not observed in unsharpened maps (as do most of the water molecules which occupy conserved positions).

  We collected a few examples from comparable cases (cryo-EM maps of similar resolution ranges) where the presence of sodium ions is highly probable based on additional evidence. These maps densities highlight the factors we discussed above. In cases ‘a’ (dual oxidase 1 prepared in high sodium conditions) and ‘b’ (human voltage-gated sodium channel), Na+ is observed in a highly coordinated states and especially in ‘a’ shows the expected increase density values compared to water molecules. However, cases ‘d’ (human Na+/K+ P type Atpase) and ‘e’ (voltage-gated sodium channel) appear very similar to the proposed Na+ assignment in PSII. We conclude that map density alone is not enough to distinguish between Na+ and water molecules and rely on the additional experiments described by Wang et al. which show increase PSII activity in elevated Na+ levels in basic conditions.

8) The cryo-EM maps showing CP29-Ser84 phosphorylation and CP47-Cys218 sulfinylation are quite convincing. However, it is interesting that these modifications are only observed in the compact conformation, and not in the stretched conformation. Can the authors elaborate on whether or not they believe the compact and stretched conformations could be a result of these posttranslational modifications, or vice versa?

This is an interesting suggestion. In our opinion it is less likely that the modification themselves trigger the transition between compact and stretched states. It is not clear how these modifications will stabilize the compact vs the stretched states. It is equally likely that these modifications are somehow triggered by the structural change. We cannot be certain that these modifications are not present in the stretched orientation as well but remain unobserved due to resolution differences. The correlation between the states and post translation modifications should be verified before a discussion on their possible roles in the transitions.

9) Do the authors believe that PSII dimers in the solution can readily interconvert between compact and stretched conformations? Or is the relative ratio of these conformations fixed at the time of membrane solubilization with decyl-maltoside?

We think that its more probable that the transition between these states occur in the membrane phase. The main reason for this will be that pigment loss and structural transitions in CP29 are more likely to occur in the membrane rather than in aqueous/micelle environments.

10) The model proposed for divalent cation-mediated stacking of PSII dimers is compelling, and seems to be in agreement with previous investigations that observed a lack of stacked dimers in cryo-EM preparations lacking calcium/magnesium. However, my understanding from reading the methods section is that the observed lack of density between the stacked PSII dimers was inferred from maps obtained after multibody refinement. Based on the way the masks to define bodies were created for multibody refinement (Fig. 4A), the region between stacked dimers would be highly prone to map artifacts following multibody refinement. Have the authors looked closely at the interfacial region between stacked dimers following conventional 3D classification/refinement to ensure that there are indeed no features observed in the interfacial region even at low contour levels?

We’ve made several attempts to resolve differences in the space between the stacked PSII dimer. These include focused classification with masks containing selected volumes from this regions and masks that include only one of the stacked PSII dimers to avoid signal subtraction in this region. All of these did not reveal any discernible features in this region. In addition, any stable binding of a bridging protein across the stacked dimer will probably be at least partially visible as additional density over the unstacked PSII. We searched for such features and found none.

Author Response:

Reviewer #1:

This manuscript by Gabor Tamas' group defines features of ionotropic and metabotropic output from a specific cortical GABAergic cell cortical type, so-called neurogliaform cells (NGFCs), by using electrophysiology, anatomy, calcium imaging and modelling. Experimental data suggest that NGFCs converge onto postsynaptic neurons with sublinear summation of ionotropic GABAA potentials and linear summation of metabotropic GABAB potentials. The modelling results suggest a preferential spatial distribution of GABA-B receptor-GIRK clusters on the dendritic spines of postsynaptic neurons. The data provide the first experimental quantitative analysis of the distinct integration mechanisms of GABA-A and GABA-B receptor activation by the presynaptic NGFCs, and especially gain insights into the logic of the volume transmission and the subcellular distribution of postsynaptic GABA-B receptors. Therefore, the manuscript provides novel and important information on the role of the GABAergic system within cortical microcircuits.

We have made all changes humanely possible under the current circumstances and we are open to further suggestions deemed necessary.

Reviewer #2:

The authors present a compelling study that aims to resolve the extent to which synaptic responses mediated by metabotropic GABA receptors (i.e. GABA-B receptors) summate. The authors address this question by evaluating the synaptic responses evoked by GABA released from cortical (L1) neurogliaform cells (NGFCs), an inhibitory neuron subtype associated with volume neurotransmission, onto Layer 2/3 pyramidal neurons. While response summation mediated by ionotropic receptors is well-described, metabotropic receptor response summation is not, thereby making the authors' exploration of the phenomenon novel and impactful. By carrying out a series of elegant and challenging experiments that are coupled with computational analyses, the authors conclude that summation of synaptic GABA-B responses is linear, unlike the sublinear summation observed with ionotropic, GABA-A receptor-mediated responses.

The study is generally straightforward, even if the presentation is often dense. Three primary issues worth considering include:

1) The rather strong conclusion that GABA-B responses linearly summate, despite evidence to the contrary presented in Figure 5C.

2) Additional analyses of data presented in Figure 3 to support the contention that NGFCs co-activate.

3) How the MCell model informs the mechanisms contributing to linear response summation.

These and other issues are described further below. Despite these comments, this reviewer is generally enthusiastic about the study. Through a set of very challenging experiments and sophisticated modeling approaches, the authors provide important observations on both (1) NGFC-PC interactions, and (2) GABA-B receptor mediated synaptic response dynamics.

The differences between the sublinear, ionotropic responses and the linear, metabotropic responses are small. Understandably, these experiments are difficult – indeed, a real tour de force – from which the authors are attempting to derive meaningful observations. Therefore, asking for more triple recordings seems unreasonable. That said, the authors may want to consider showing all control and gabazine recordings corresponding to these experiments in a supplemental figure. Also, why are sublinear GABA-B responses observed when driven by three or more action potentials (Figure 5C)? It is not clear why the authors do not address this observation considering that it seems inconsistent with the study's overall message. Finally, the final readout – GIRK channel activation – in the MCell model appears to summate (mostly) linearly across the first four action potentials. Is this true and, if so, is the result inconsistent with Figure 5C?

GABAB responses elicited by three and four presynaptic NGFC action potentials were investigated to have a better understanding about the extremities of NGFC-PC connection. Although, our spatial model suggests that in L1 in a single volumetric point one or two NGFCs could provide GABAB response with their respective volume transmission, it is still important that in the minority of the percentage three or more NGFCs could converge their output. The experiments in Fig 5 not only offer mechanistic understanding that possible HCN channel activation and GABA reuptake do not influence significantly the summation of metabotropic receptor-mediated responses, but also support additional information about the extensive GABAB signaling from more than two NGFC outputs. Interestingly in this experiment the summation until two action potentials show very similar linear integration as seen in the triplet recordings. This result suggests that the temporal and spatial summation is identical when limited inputs are arriving to the postsynaptic target cell. Similar summation interaction can be seen in our model until two consecutive GABA releases. Three or four consecutive GABA releases in our model still produces linear summation, our experiments show moderate sublinearity. One possible answer for this inconsistency is the vesicle depletion in NGFCs after multiple rapid release of GABA, which was not taken into account in our model.

Presumably, the motivation for Figure 3 is that it provides physiological context for when NGFCs might be coactive, thereby providing the context for when downstream, PC responses might summate. This is a nice, technically impressive addition to the study. However, it seems that a relevant quantification/evaluation is missing from the figure. That is, the authors nicely show that hind limb stimulation evokes responses in the majority of NGFCs. But how many of these neurons are co-active, and what are their spatial relationships? Figure 3D appears to begin to address this point, but it is not clear if this plot comes from a single animal, or multiple? Also, it seems that such a plot would be most relevant for the study if it only showed alpha-actin 2-positive cells. In short, can one conclude that nearby, presumptive NGFCs co-activate, and is this conclusion derived from multiple animals?

The aim of Fig. 3 D was to indicate that the active, presumably NGFCs are spatially located close to each other. The figure comes from a single animal. We agree with the reviewer, therefore changed the scatter plot figure in Fig. 3D to another one, that provides information about the molecular profiles of the active/inactive cells. We made an effort to further analyze our in vivo data and the spatial localization of the monitored interneurons (see Author response image 3.). The results are from 4 different animals, in these experiments numerous L1 interneurons are active during the sensory stimulus, as shown in the scatter plot. We calculated the shortest distance between all active cells and all ɑ-actinin2+ that were active in experiments. The data suggest that in the case of identified active ɑ-actinin2+ cells, the interneuron somas were on average 182.69+60.54 or 305.135+34.324 μm distance from each other. Data from Fig. 2D indicates that the average axonal arborization of the NGFCs is reaching ~200-250μm away. Taken these two data together, in theory it is probable that the spatial localization would allow neighboring NGFCs to directly interact in the same spatial point.

The inclusion of the diffusion-based model (MCell) is commendable and enhances the study. Also, the description of GABA-B receptor/GIRK channel activation is highly quantitative, a strength of the study. However, a general summary/synthesis of the observations would be helpful. Moreover, relating the simulation results back to the original motivation for generating the MCell model would be very helpful (i.e. the authors asked whether "linear summation was potentially a result of the locally constrained GABAB receptor - GIRK channel interaction when several presynaptic inputs converge"). Do the model results answer this question? It seems as if performing "experiments" on the model wherein local constraints are manipulated would begin to address this question. Why not use the model to provide some data – albeit theoretical – that begins to address their question?

We re-formulated the problem to be addressed in this Results section. We admit that our model is has several limitations in the Discussion and, consequently, we restricted its application to a limited set of quantitative comparisons paired to our experimental dataset or directly related to pioneering studies on GABAB efficacy on spines vs shafts. We believe that a proper answer to the reviewer’s suggestion would be worth a separate and dedicated study with an extended set of parameters and an elaborated model.

In sum, the authors present an important study that synthesizes many experimental (in vitro and in vivo) and computational approaches. Moreover, the authors address the important question of how synaptic responses mediated by metabotropic receptors summate. Additional insights are gleaned from the function of neurogliaform cells. Altogether, the authors should be congratulated for a sophisticated and important study.

Reviewer #3:

The authors of this manuscript combine electrophysiological recordings, anatomical reconstructions and simulations to characterize synapses between neurogliaform interneurons (NGFCs) and pyramidal cells in somatosensory cortex. The main novel finding is a difference in summation of GABAA versus GABAB receptor-mediated IPSPs, with a linear summation of metabotropic IPSPs in contrast to the expected sublinear summation of ionotropic GABAA IPSPs. The authors also provide a number of structural and functional details about the parameters of GABAergic transmission from NGFCs to support a simulation suggesting that sublinear summation of GABAB IPSPs results from recruitment of dendritic shaft GABAB receptors that are efficiently coupled to GIRK channels.

I appreciate the topic and the quality of the approach, but there are underlying assumptions that leave room to question some conclusions. I also have a general concern that the authors have not experimentally addressed mechanisms underlying the linear summation of GABAB IPSPs, reducing the significance of this most interesting finding.

1) The main novel result of broad interest is supported by nice triple recording data showing linear summation of GABAB IPSPs (Figure 4), but I was surprised this result was not explored in more depth.

We have chosen the approach of studying GABAB-GABAB interactions through the scope of neurogliaform cells and explored how neurogliaform cells as a population might give rise to the summation properties studied with triple recordings. This was a purposeful choice admittedly neglecting other possible sources of GABAB-GABAB interactions which possibly take place during high frequency coactivation of homogeneous or heterogeneous populations of interneurons innervating the same postsynaptic cell. We agree with the reviewer that the topic of summation of GABAB IPSPs is important and in-depth mechanistic understanding requires further separate studies.

2) To assess the effective radius of NGFC volume transmission, the authors apply quantal analysis to determine the number of functional release sites to compare with structural analysis of presynaptic boutons at various distances from PC dendrites. This is a powerful approach for analyzing the structure-function relationship of conventional synapses but I am concerned about the robustness of the results (used in subsequent simulations) when applied here because it is unclear whether volume transmission satisfies the assumptions required for quantal analysis. For example, if volume transmission is similar to spillover transmission in that it involves pooling of neurotransmitter between release sites, then the quantal amplitude may not be independent of release probability. Many relevant issues are mentioned in the discussion but some relevant assumptions about QA are not justified.

Indeed, pooling of neurotransmitter between release sites may affect quantal amplitude, therefore we examined quantal amplitude under low release probability conditions using 0.7- 1.5 mM [Ca]o to detect postsynaptic uniqantal events initiated by neurogliaform cell activation (Author response image 7). This way we measured similar quantal current amplitudes comparing with BQA method with no significant difference (4.46±0.83 pA, n=4, P=0.8, Mann-Whitney Test).

3) The authors might re-think the lack of GABA transporters in the model since the presence and characteristics of GATs will have a large effect on the spread of GABA in the extracellular space.

We agree that the presence of GAT could effectively shape the GABA exposure, e.g. (Scimemi 2014). During the development of the model, we took into consideration different possibilities and solutions to create the model’s environment. To our knowledge, there is no detailed electron microscopic study that would provide ultrastructural measurements of structural elements around the NGFC release sites and postsynaptic pyramidal cell dendrites in layer 1 while preserving the extracellular space. Moreover, quantitative information is scarce about the exact localization and density of the GATs along the membrane surface of glial processes around confirmed NGFC release sites. We felt that developing a functional environment that would contain GABA transporters without possessing such information would be speculative. Furthermore, during the development of the model it became clear that incorporating thousands of differentially located GABA transporters would massively increase the processing time of single simulations including monitoring each interaction between GATs and GABA molecules, and requiring computational power calculating the diffusion of GABA molecules in the extracellular space, even if GABA molecules are far from the postsynaptic dendritic site without any interaction.

As an admittedly simple and constrained alternative, we decided to set a decay half-life for the GABA molecules released. This approach allows us to mimic the GABA exposure time of 20-200 ms, based on experimental data (Karayannis et al 2010). In the model the GABA exposure time was 114.87 ± 2.1 ms with decay time constants of 11.52 ± 0.14 ms. After ~200 ms all the released GABA molecules disappeared from the simulation environment.

A detailed extracellular diffusion aspect was out of the scope of our model, we were interested in investigating how the subcellular localization of receptors and channels determine the summation properties.

4) I'm not convinced that the repetitive stimulation protocol of a single presynaptic cell shown (Figure 5) is relevant for understanding summation of converging inputs (Figure 4), particularly in light of the strong use-dependent depression of GABA release from NGFCs. It is also likely that shunting inhibition contributes to sublinear summation to a greater extent during repetitive stimulation than summation from presynaptic cells that may target different dendritic domains. The authors claim that HCN channels do not affect integration of GABAB IPSPs but one would not expect HCN channel activation from the small hyperpolarization from a relatively depolarized holding potential.

Use-dependent synaptic depression of NGFC induced postsynaptic responses was nicely documented by Karayannis and coworkers (2010) although they investigated the GABAA component of the responses and they found that the depression is caused by the desensitization of postsynaptic GABAA receptors. We are not aware of experiments published on the short term plasticity of GABAB responses. In our experiments represented in Fig 5 we found linearity in the summation of GABAB responses up to two action potentials and sublinearity for 3 and 6 action potentials. In fact, our results show that no synaptic depression is detectable in response to paired pulses since amplitudes of the voltage responses were doubled compared to a single pulse which means that the paired pulse ratio is around 1. To verify our result, we repeated our dual recording measurements with one, two, three and four spike initiation in the presynaptic neurogliaform cell (Author response image 6). Measuring both the amplitude and the overall charge of GABAB responses we again found linear relationship among one and two spike initiation protocol.

Author response image 6 - Integration of GABAB receptor-mediated synaptic currents (A) Representative recording of a neurogliaform synaptic inhibition on a voltage clamped pyramidal cell. Bursts of up to four action potentials were elicited in NGFCs at 100 Hz in the presence of 1 μM gabazine and 10 μM NBQX (B) Summary of normalized IPSC peak amplitudes (left) and charge (right). (C) Pharmacological separation of neurogliaform initiated inhibitory current.

Author Response:

Reviewer #1 (Public Review):

Overall the work is an impressive analysis of an understudied cell-type in human MS, and represents an important finding. The paper is well presented and the figures very clear. However, the manuscript is descriptive and, although this is not a problem by itself, the depth and limitations of the Cytof (only 37 markers) leaves the reader without a clear idea of what these cells could be doing.

Some single-cell RNAseq and other ways to interrogate potential mechanisms and function would be particularly helpful here, but is perhaps beyond the scope of the paper.

We thank the reviewer for this nice comment. We fully agree that a next informative step would be the investigation of the function and mechanisms of the NK cell populations in MS pathology. At this moment, that is indeed beyond the scope of the current manuscript. We do believe that our findings can guide future studies to explore potential mechanisms of NK cells in more depth.

At minimum more immunohistochemical and smFish or in situ hybridization to validate key findings (using the markers identified by CyTOF) and add to the spatial relationships of Nk Cells with other border and brain cells would be informative.

We appreciate this suggestion and have performed different immunohistochemical analysis to study the spatial relationship of NK cells and other immune and brain cells in the MS brain (Essential Revisions Fig. 1). We have stained the same cohort described in the manuscript for CD45, NKp46, GrB and Iba1 as well as CD45, NKp46, GrB and GFAP, to study the interaction of NK cells with microglia/macrophages and astrocytes, respectively, and with CD45+ immune cells in general. In MS lesions, we were able to detect a small but similar percentage of putative CD56bright NK cells (CD45+ NKp46+ GrB- cells) interacting with CD45+ Iba1- cells and with CD45+ Iba1+ cells (Essential Revisions Figure 1a-b). Due to astrogliosis, the processes of astrocytes densely populate the MS lesions and as such, we cannot infer if the interaction between NK cells and astrocytes is functional. Furthermore, the absolute number of NK cells in control brains is low, so we can only obtain reliable data from MS brains. As a result, we are unable to compare the observed interactions in MS lesions with a control condition. Of note, CD56bright NK cells are potent cytokine producers and their potential regulatory functions are not be limited to contact-dependent interactions.

Essential Revisions Fig. 1 cellular interactions of Granzyme B- NK cells (a) Representative immunohistochemical staining of Granzyme B- NK cells stained for CD45 (green), NKp46 (magenta) and negative for Granzyme B (cyan), together with microglia stained with iba1 (red). Scale bar = 10µm. (b) Pie chart displays the percentage of CD45+ NKp46+ Granzyme Bcells interacting with CD45+ Iba1+ and C45+ Iba1- cells in MS lesions. (c) Representative immunohistochemical staining of NK cells stained for CD45 (green), NKp46 (magenta) and negative for Granzyme B (cyan), together with astrocytes stained with GFAP (red). Scale bar = 10µm.

A major weakness of the study is that is is underpowered and thus not clear how robust or representative these findings are in MS given the heterogeneity of the disease and also potential differences in Sex, Age and lack of healthy controls. (AD samples labelled as control.)

We thank the reviewer for their comment. First we would like to comment on the presumed lack of healthy controls. In this study, we included two ‘control’ groups, one of them consisted out of non-neurological controls (“NNC”), free of any neurological disease, and the other consisted of neurological controls (“NC”), including demented and Alzheimer patients. We acknowledge that this terminology leaves the reader confused; as such, we renamed the “NC” group with patients suffering from dementia to “Dementia” and the “NNC” group of donors without neurological disease to “Controls”.

Secondly, while our sample size is rather small, it is comparable to other studies that use fresh post-mortem brain tissue (Böttcher et al, 2020).. The usage of this unique postmortem brain tissue from human donors is severely limited by the number of well-characterized samples available, their demographics and clinical background. To overcome the underpowered design and possible effects of confounders as sex and age, we validated our main finding by multiplex immunohistochemistry in a separate cohort. This included 5 controls (2 females, 3 males, f:m ratio of 0.667) and 7 MS cases (3 females and 4 males, f:m of 0.75), with a similar female/male ratio and matched age (Wilcoxon rank sum test with continuity correction, p-value = 0.41). We now included the characteristics of the validation cohort in the manuscript as well.

“Finally, to confirm that CD56bright NK cells accumulate in periventricular brain regions in MS donors, we used multiplex immunohistochemistry in an independent cohort (Table 1), wherein MS and control groups were age-matched (Wilcoxon rank sum test with continuity correction, p-value = 0.41) and had a similar female:male ratio (0.667 in controls and 0.75 in MS).”

Böttcher C, van der Poel M, Fernández-Zapata C, Schlickeiser S, Leman JKH, Hsiao CC, Mizee MR, Adelia, Vincenten MCJ, Kunkel D, Huitinga I, Hamann J, Priller J (2020) Single-cell mass cytometry reveals complex myeloid cell composition in active lesions of progressive multiple sclerosis. Acta neuropathologica communications, 8(1), 1-18

It is also important to show the NK cells are actually in the parenchyma and interacting with other cells (e.g., microglia) of the lesion. If the authors have this tissue and antibodies to do that, this would add to the study. Moreover, the details on samples and controls should be more clearly communicated in the text and legends as well as the caveats and limitations of the study in the Discussion.

The location of NK cells within the brain parenchyma is an important determinant of their function within the CNS. Thus, we included a basement membrane marker (collagen IV) in our multiplex IHC panel in order to exclude the cells within the vessel lumen. As this has not been clearly communicated, we have adjusted the sentence from the subsection Multiplex immunohistochemistry in the Methods (from “Cells within the lumen of vessels from the choroid plexus sections were excluded manually” to “Cells within the lumen of vessels were excluded manually with the aid of collagen IV staining.”). We have addressed in Essential Revisions Fig. 1 the additional IHC experiments performed to explore the interactions of NK cells with other brainresident cells. We thank the reviewer for warning us on the difficulty of our nomenclature. We have thus adjusted the labels of the three main groups throughout the manuscript as follows: Control (previously, NNC), Dementia (previously, NC) and MS (same as before). We also have expanded the limitations of this study in the Discussion.

“Our study has two main limitations, first scarcity of fresh human tissue prevented having sex and age-matched groups with large sample sizes for the CyTOF analysis. To overcome the underpowered design and possible effects of confounders, we have validated our main finding by multiplex immunohistochemistry in a separate cohort with a similar age and female/male ratio. Secondly, there is a strong contribution of blood-derived immune cells in the choroid plexus, which precluded a clear distinction between circulating and stromal immune cells. This may have prevented the detection of choroid-plexus specific changes in the stroma, such as an accumulation of CD8+ T cells in the choroid plexus from MS donors, previously described by our group using immunohistochemistry [47]. In addition, the high proportion of granulocytes in the CP as detected by our CyTOF analysis likely originates from the circulation [47,63]. Contrariwise, the scarcity of B cells, despite the high vascularisation, is in line with previous reports [47,63]; and the detection of rare ASCs in the choroid plexus but not in the blood reassures their tissue specificity [63].”

Reviewer #2 (Public Review):

The data are extensive, valuable, convincing, and entirely descriptive (as studies using human post-mortem material must be, of necessity). What emerges is a detailed account of NK cells in specific regions of the MS brain (although here the authors slightly overplay how little is known about NK cells in MS). The study provides a very comprehensive resource. The authors speculate on what their data might mean in terms of disease dynamics is a reasonable and informed way, but much of what is concluded is inference not backed up by experiment studies that would allow this to be more than a resource paper.

We thank the reviewer for his/her compliments and agree that in this manuscript we can only speculate on the role of NK cells and their way of migration or proliferation, to and within the brain. Only future research can solve these speculations. We have addressed these concerns accordingly in the discussion and have removed any concluding or far-fetched speculations which is not backed-up by our own data.

Reviewer #3 (Public Review):

The authors introduce their work in the context of the prevailing uncertainties about the pathogenesis of multiple sclerosis (MS) and, in particular, seem to reference the initiation of immune lesions in early MS. However, the work itself addresses end-stage MS situations, which is quite possibly an entirely different landscape altogether, and may not be informative about MS initiation.

We want to thank the reviewer for pointing out this misleading part of the text. We agree that our study does not provide any information on the initial stages of MS, and have therefore adjusted this part of the introduction to avoid confusion. “Brain regions around the ventricles are hotspots for MS lesions [8,21,39,52], but underlying mechanisms are poorly understood [41]. Since the majority of periventricular MS lesions occur around a central vessel [1,57], it has been suggested that vascular topography may influence MS pathology [33].”

As a textual point, the manuscript makes far too many speculations about possible cell trafficking between compartments than is justified by a cross-section study.

We appreciate this concern and we have therefore tuned down our speculations in the results and discussion sections.

That said, the work itself is a carefully done descriptive characterisation of the leucocyte landscape found in the periventricular septum, choroid plexus (and peripheral blood) post-mortem from cases of multiple sclerosis (MS), non-MS neurological disease (dementia), and non-neurological controls (8-12 each). The material is rare, the post-mortem delays are quite short, the cell lineage characterisation is fairly extensive and some of the data are well supported by immunohistochemistry.

We thank the reviewer for these compliments.

Author Response:

Reviewer #4 (Public Review):

In this work, Tee et al. study the implications of Heparan Sulfate (HS) binding mutations observed on the Enterovirus A71 (EV-A71) capsid. HS-binding mutations are observed for several virus infections and are often presumed to be a cell culture adaptation. However, in the case of EV-A71, the presence of HS-binding mutations in clinical samples and the contradictory findings in animal studies have made the clinical relevance of HS-binding a subject of debate. Therefore, to better understand the role of HS-binding in EV-A71, the authors use a mouse-adapted EV-A71 variant (MP4) and compare it to a cell-adapted strong HS-binder (MP4-97R/167G). Using these two variants, the authors show that the strong HS-binder does not require acidification for uncoating and genome release. Furthermore, it is demonstrated that the capsid stability of the HS-binding variant is compromised, resulting in pH-independent uncoating. Overall, this study provides new insights demonstrating that seemingly beneficial mutations increasing viral replication may be counterbalanced by other unintended consequences.

Strengths:

The thoroughness of the experiments performed to demonstrate that the HS-binding phenotype results in pH-independent entry and capsid destabilisation is worth highlighting. In this regard, the authors have explored viral entry using a range of approaches involving lysosomotropic drugs, viral binding assays, and neutral red-labelled viruses coupled with diverse techniques such as FISH, RNAscope, and transient expression of constitutively active molecules to inhibit parts of the viral cycle. In my opinion, this is necessary to rule out the other downstream effects of the lysomotropic drugs and to confirm the role of the HS-binding mutation in the entry phase. The use of in silico analysis coupled with negative staining electron microscopy and environmental challenge assays is notable. Finally, the demonstration of some of the work using a human-relevant strain is commendable.

We appreciate the reviewer recognition of the significance of our study and the precious advises.

Weaknesses:

A major weakness in this study is the focus on using a mouse-adapted EV-A71 strain (MP4). In the introduction, it is argued that HS-binding mutations are controversial due to their occurrence in cell culture. However, due to host limitations, mice are not the natural hosts for EV-A71 and thus, the same argument can be made for a mouse-adapted strain. It is not clear how different this strain is from circulating EV-A71 strains and the relevance of these findings to the human situation is questionable. This is particularly made evident in the discussion where it is highlighted that HS-binding variants (VP1-145G/Q mutants) have been associated with severe neurological cases while the same variants show attenuated phenotypes in mice and monkeys. This contrast between clinical data and animal studies should be highlighted in the introduction, rather than later in the discussion, as currently the in vivo animal studies are presented as the optimal situation and may lead to misconstrued conclusions from the results.

As requested by the reviewer, we included new experiments performed with a clinical strain isolated in an immunosuppressed patient (Cordey et al., 2012). We compared the sensitivity of this human strain harboring or not the VP1 L97R and E167G mutations to HCQ and confirmed that the similar differential sensitivity to HCQ was observed as with the MP4 variant. This result is presented as a new supplementary figure (Figure 6-figure supplement 1) and is described in the result section of the revised manuscript (Page 7, lines 251).

Page 7, lines 251: To determine if our observations are applicable to human strains, we examined the sensitivity of a closely related clinical strain. This strain was isolated from the respiratory tract of an immunosuppressed patient with a disseminated EV-A71 infection27. Additionally, we tested a strong HS-binding derivative that harbors the same VP1-L97R and E167G mutations as our MP4 double mutant. Notably, this human clinical strain shares 98.3% amino acid similarity with the MP4 variant used in this study and exhibits similar HS-binding phenotypes28. As shown in Figure 6-figure supplement 1, the original human strain was inhibited by HCQ, whereas the double mutant exhibited insensitivity to the drug.

We also added the comment about discrepancy between clinical data and animal studies in the introduction as requested (page 2, lines 69-76): However, epidemiological surveillance of human EV-A71 infections19-21 and experimental evidence from 2D human fetal intestinal models22, human airway organoids23 and air-liquid interface cultures24 suggest that HS binding may enhance viral replication and virulence in humans. In addition, recent research has shown that EV-A71 can be released and transmitted via cellular extrusions25 or exosomes26, potentially preventing viral trapping of HS-binding strains in the circulation. Further studies are required to evaluate the true impact of HS-binding mutations on the spread and virulence of EV-A71 in both animal models and humans.

An important consideration is that the results are based primarily on image analysis. The inclusion of RT-qPCR and/or plaque assays as supplementary data will help strengthen the findings.

We have performed RT-qPCR to confirm the immunostaining data and included them in the supplementary data (Figure 1-figure supplement 1E). Reference to these data is made in the result section [Page 4, lines 114-116: These results were confirmed by viral load quantification with real-time RT-PCR (Figure 1-figure supplement 1E).]

Moreover, there are suggestions of an intermediate binder having a different phenotype. As this intermediate binder is the clinical phenotype, data on the entry of this intermediate binder will be valuable.

While we agree with reviewer that the single mutant is an intermediate binder and exhibits a clinical phenotype, we made the decision to work with variants that display clear phenotypes, selecting MP4 and the double mutant, as the latter is fully attenuated in both immunocompetent and immunosuppressed mice (Weng et al., 2023). Additionally, we performed an experiment using HCQ, where we observed an intermediate effect with the single mutant. This further confirmed our decision to proceed with MP4 and the double mutant for all experiments. The data supporting this are shown in Author response image 1, which we are sharing exclusively with the reviewer.

Author response image 1.

Differential sensitivity of MP4, MP4-97R and MP4-97R167G to Lysosomotropic drugs

Another weakness in the study is the lack of contextualization of the results to current EV-A71 literature. For instance, SCARB2 is referred to as the internalization receptor but a recent study has shown that SCARB2 is not required for internalization (https://doi.org/10.1128%2Fjvi.02042-21). The findings from this study are consistent with the localization of SCARB2 in the lysosomal membranes. Furthermore, the same study has highlighted host sulfation as a key factor in EV-A71 entry. Post-translational sulfation introduces negatively charged residues on host proteins including HS and SCARB2. This increases the binding of HS-binding strains to these proteins. In this regard, the reduced infectivity upon soluble SCARB2 treatment may simply be due to enhanced binding rather than capsid opening as suggested in the results. Therefore, additional experiments (e.g. nSEM following soluble SCARB2 treatment) must be performed to support the conclusion of capsid opening, due to inherent instability, upon SCARB2 binding.

We apologize for not citing this relevant literature excluding the role of SCARB2 in viral attachment. We have now included these references in the revised version of the manuscript. (Page 2, lines 54-56: “Since SCARB2 is mostly localized on endosomal and lysosomal membrane and sparsely on plasma membrane3,5, it seems to play only a minor role in EV-A71 cell attachment6,7.

We thank the reviewer for mentioning the possibility that the sulfation of SCARB2 may enhance its binding to the mutated virus compared to the wild-type virus, potentially explaining the selective competitive inhibition of this variant by soluble SCARB2 produced in mammalian cells. To investigate this hypothesis, we performed nsEM imaging of the double mutant incubated with soluble SCARB2 and we observed an increase in the proportion of empty capsids in the presence of soluble SCARB2 (4% versus 0.7%), supporting our original findings that the inactivation is indeed associated with capsid opening. The results are included in the revised manuscript in Figure 5-figure supplement 4 and described on Page 7, lines 243-245: “However, the double mutant exhibited a ~5-fold increase in empty capsid percentage after treatment with sSCARB2 (Figure 5-figure supplement 4), consistent with the functional data above.”

In addition to the above, other existing literature on EV-A71 pathogenesis using organoids contradicts some of the explanations of differential phenotype in clinical observations versus mice models. In the introduction, it is suggested that reduced neurovirulence of HS-binding strains is due to binding to the vascular endothelia. However, the correlation of clinical severity to viremia (https://doi.org/10.1186/1471-2334-14-417) and the association of HS-binding mutants to clinical disease counteract this suggestion. Similarly, viral infection in human organoids with EV-A71 results in as low as 0.4% of the cells being infected (https://doi.org/10.1038/s41564-023-01339-5). In this case, if viral binding to (ubiquitously expressed) HS results in viral trapping then the HS-binding mutants should show lowered infectivity in organoid models rather than the observed higher infectivity (https://doi.org/10.3389/fmicb.2023.1045587, https://doi.org/10.1038/s41426-018-0077-2). Finally, EV-A71 release has also been shown to occur in exosomes (https://doi.org/10.1093%2Finfdis%2Fjiaa174) which effectively provides a protective lipid membrane. These recent findings must be incorporated into the article and will help better contextualize their findings.

We appreciate the reviewer thoughtful comments. We do not believe that the correlation between clinical severity and viremia contradicts the viral trapping hypothesis. For strains that do not bind to HS, the absence of viral trapping could indeed lead to higher viral concentrations in the bloodstream, potentially increasing neurovirulence. However, we agree with the reviewer that other observations in humans, along with experimental data from more relevant models such as organoids, challenge the trapping hypothesis. We are grateful for the suggested citations and have incorporated these references in the introduction, where we discuss this point in more detail

Page 2, lines 69-76: “However, epidemiological surveillance of human EV-A71 infections19-21 and experimental evidence from 2D human fetal intestinal models22, human airway organoids23 and air-liquid interface cultures24 suggest that HS binding may enhance viral replication and virulence in humans. In addition, recent research has shown that EV-A71 can be released and transmitted via cellular extrusions25 or exosomes26, potentially preventing viral trapping of HS-binding strains in the circulation. Further studies are required to evaluate the true impact of HS-binding mutations on the spread and virulence of EV-A71 in both animal models and humans.”

Overall, the authors present new findings with convincing methodology. The manuscript can be improved in the contextualization of the findings and highlighting the weakness in translating these findings to resolve the debate surrounding the relevance of HS-binding phenotype. The inclusion of additional experiments and data recommended to the authors will also help strengthen the manuscript.<br />

Author Response:

Reviewer #1 (Public Review):

This manuscript investigates the gene regulatory mechanisms that are involved in the development and evolution of motor neurons, utilizing cross-species comparison of RNA-sequencing and ATAC-sequencing data from little skate, chick and mouse. The authors suggest that both conserved and divergent mechanisms contribute to motor neuron specification in each species. They also claim that more complex regulatory mechanisms have evolved in tetrapods to accommodate sophisticated motor behaviors. While this is strongly suggested by the authors' ATAC-seq data, some additional validation would be required to thoroughly support this claim.

Strengths of the manuscript:

1) The manuscript provides a valuable resource to the field by generating an assembly of the little skate genome, containing precise gene annotations that can now be utilized to perform gene expression and epigenetic analyses. The authors take advantage of this novel resource to identify novel gene expression programs and regulatory modules in little skate motor neurons.

2) Cross-species RNA-seq and ATAC-seq data comparisons are combined in a powerful approach to identify novel mechanisms that control motor neuron development and evolution.

Weaknesses:

1) It is surprising that the analysis of RNA-seq datasets between mouse, chick, and little skate only identified 5 genes that are common between the 3 species, especially given the authors' previous work identifying highly conserved molecular programs between little skate and mouse motor neurons, including core transcription factors (Isl1, Hb9, Lhx3), Hox genes and cholinergic transmission genes. This raises some questions about the robustness of the sequencing data and whether the genes identified represent the full transcriptome of these motor neurons.

To address reviewer #1’s questions, we have generated RNA sequencing data with mouse forelimb MNs and re-analyzed the RNA-seq data using only the homologous MN populations (Figure 3) among different species. As a result, many genes (1038 genes) are commonly expressed in MNs in different species, including many known MN marker genes. In the result section, we have added the following:

“The evolution of genetic programs in MNs was investigated unbiasedly by comparing highly expressed genes in pec-MNs (percentile expression > 70) of little skate with the ones from MNs of mouse and chick, two well-studied tetrapod species. In order to compare gene expression with homologous cell types from each species, we performed RNA sequencing on forelimb MNs of mouse embryos at embryonic day 13.5 (e13.5) and wing level MNs of chick embryos at Hamburger-Hamilton (HH) stage 26–27…”

We have also compared our re-analysis with previous results in Figure 2–figure supplement 1, shown above. Most of the fin MN genes (21/24) are highly expressed in pecMNs (percentile > 70), consistent with the previous in situ experiments. In the Results we have added the following:

“Although the total number of DEGs are different from the previous data (592 vs. 135 genes in pec-MN DEGs), which might be caused by different statistical analysis with different reference genome, previous RNA-seq data based on de novo assembly and annotation using zebrafish was mostly recapitulated in our DEG analysis based on our new skate genome (21 out of 24 previous fin MN marker genes have the expression level ranked above 70th percentile in Pec-MNs; Figure 2‒figure supplement 1).”

2) The authors suggest based on analysis of binding motifs in their ATAC-seq data that the greater number of putative binding sites in the mouse MNs allows for a higher complexity of regulation and specialization of putative motor pools. This could certainly be true in theory but needs to be further validated. The authors show FoxP1 as an example, which seems to be more heavily regulated in the mouse, but there is no evidence that FoxP1 expression profile is different between mouse and skate. It is suggested in Fig.5 that FoxP1 might be differentially regulated by SnaiI in mouse and skate but the expression of SnaiI in MNs in either species is not shown.

We have added further discussion and data about differential expression of Foxp1 in mouse and little skate in Figure 5–figure supplement 16 and have discussed as follows:

“Foxp1, the major limb/fin MN determinant appears to be differentially regulated in tetrapod and little skate. Although Foxp1 is expressed in and required for the specification of all limb MNs in tetrapods, Foxp1 is downregulated in Pea3 positive MN pools during maturation in mice (Catela et al., 2016; Dasen et al., 2008). In addition, preganglionic motor column neurons (PGC MNs) in the thoracic spinal cord of mouse and chick express half the level of Foxp1 expression than limb MNs. Although PGC neurons have not yet been identified in little skate, we tested the expression level of Foxp1 using a previously characterized tetrapod PGC marker, pSmad. We observed that Foxp1 is not expressed in MNs that express pSmad (Figure 5‒figure supplement 3). Since there is currently no known marker for PGC MNs in little skate, our conclusion should be taken with caution.”

As for Snai1, in the revision we performed a motif enrichment analysis with an unbiased gene list where Snai1 didn’t show up. However, when we performed an RNA in situ hybridization experiment for Snai1 (Figure 5–figure supplement 3), we found that Snai1 is expressed in MNs of both mouse and little skate, but not in chick, which has been shown previously (Cheung et al., 2005). In order to examine the function of Snai1 in the regulation of Foxp1 expression, we ectopically expressed Snai1 in chick spinal cord by performing in ovo electroporation. However, we did not detect any changes in Foxp1. Instead we observed an increase in the number of neurons and abnormal MN exits from the spinal cord, which is the reminiscent of a previous observation (Zander et al., 2014). Although we did not detect any changes in Foxp1 expression, we cannot rule out the possibility that Snai1 regulates Foxp1 in mouse and little skate, which may require a gene knock out experiment. Because binding sites of Snai1 were not enriched in the new gene sets that we analyzed in the revision, we have not further discussed the Snai1 in the text.

3) In their discussion section the authors state that they found both conserved and divergent molecular markers across multiple species but they do not validate the expression of novel markers in either category beyond RNA-seq, for example by in situ or antibody staining.

We have added RNA in situ hybridization results in Figure 3C and Figure 3–figure supplement 1 and 2. Most of the genes were expressed in tissues in accordance with the sequencing results (6 out of 9 common MN genes; 4 out of 6 mouse specific genes; 5 out of 7 skate specific genes). Specifcally, Uchl1, Slc5a7, Alcam, and Serinc1 are expressed in MNs of all three species; Coch, Ppp1rc, Ctxn1, and Clmp are expressed in MNs of mouse but not in MNs of other species; Eya1, Etv5, Dnmbp, and Spint1 are expressed in MNs of skate but not in MNs of other species. In the result section, we have summarized the results as follow:

“These results were validated by performing RNA in situ hybridization in tissue sections on a subset of species-specific genes …”

Author Response

Reviewer #2 (Public Review):

Regulation of NAD and its intermediary metabolites is of critical importance in axon degeneration and neurodegenerative disease. Mounting evidence supports a scenario in which low NAD, and high NMN triggers axon degeneration by competitive allosteric inhibition/activation of SARM1. Strategies to increase NAD levels and/or lower NMN levels provide neuroprotection in a variety of contexts. NAD metabolism is a partially conserved process, however, there are key differences in pathway routes and dynamics between model organisms used for NAD research (yeast, worm, fly, zebrafish, mouse/mammalian systems). Drosophila is a key model organism for axon degenerative research based on its ease of use and range of available genetic tools, in addition, the effector of axon degeneration - SARM1 - was first identified in the fly. As Drosophila has some key differences in the NAD synthesis pathways to mammalian systems it is important to test and develop tools to enable exploration of these pathways on the fly. Llobet Rosell and colleagues have developed clear and demonstrable tools in Drosophila for exploring NAD-related axon degenerative pathways by modulating the use of NMN via the addition of NMN consuming and NMN generating enzymes. They utilize Drosophila genetics to adequately support the claims made in the manuscript. Importantly, the authors well-demonstrate that consuming NMN through an alternate route to NaMN provides neuroprotection and that the neuroprotective components of low NMN are upstream of SARM1. These should be useful tools for neuroscientists in the future to use Drosophila for neurodegenerative research.

Strengths:

• Clear demonstration that low NMN provides neuroprotection using novel, stable, enzymatic depletion of NMN (to NaMN).

• Development of a novel Drosophila tool (NMN-D transgenics) to explore NMN metabolism in vivo, including a stabilized version to permit chronic NMN depletion.

• Metabolomic profiles across the pathway to show all pathway changes (not just isolated NMN or NAD assays). • Neurodegenerative assays that include both histological outcomes (axon degeneration) but also circuitry/functional outcomes. Data from both series of experiments all support each other.

• Assessment of other known potent axon degenerative genes via genetics in combination with the tools developed. • Staging of the molecular processes by strategic ablation of the inhibitory ARM domain on SARM1 (dSarm deltaARM). These experiments suggest that low NAD AND high NMN (i.e. ratio between the two) is the critical factor that drives axon degeneration. Once NAD is low, axon degeneration cannot be recovered by further lowering of NMN. The dSarm delta-ARM and dnmnat sgRNAs experiments support a hypothesis in that (high) NMN triggers, but doesn't, execute axon degeneration.

We appreciate his recognition of the quality of our research.

Weaknesses:

• The authors use murine NAMPT (mNAMPT) to increase NMN. The degeneration assays support the hypotheses made, yet mNAMPT doesn't actually increase NMN. Thus it is unclear in this setting whether mNAMPT promotes axon degeneration by an NMN-related mechanism or through another route. It is also unclear as to why the murine form was chosen versus a human or other orthologues, or changing the metabolism of the intrinsic pathway (NR and NRK).

Why mNAMPT:

We decided to use mouse NAMPT (mNAMPT) because it was readily available by Giuseppe Orsomando (Amici et al., 2017), and because we did not have access to human NAMPT (hNAMPT).<br /> We agree with the observation that under physiological conditions, the expression of mNAMPT does not change NMN. However, we argue that after injury, once dNmnat is degraded, the additional NMN synthesis provided by mNAMPT expression (in addition to dNrk), leads to a faster NMN accumulation. It is supported by the observation that NMNAT2 is more labile than NAMPT in mammals (Gilley and Coleman, 2010; Stefano et al., 2015).

• The authors use metabolic profiling to look at the individual metabolites during axon degenerative evens and treatments however it is unclear if any of these proteins or genes change as a consequence. This is likely not important for understanding the findings however, might be helpful in explaining the mNAMPT data.

We agree with the idea to test whether there is a change induced at the mRNA or protein level when the metabolic flux is altered. To do this, first, we measured the relative expression levels of axon death and NAD+ synthesis genes (Figure 2 – figure supplement 1B). Then, we measured potential changes upon mNAMPT expression (Figure 4 – figure supplement 1). Importantly, while the Gal4-driven expression resulted in an increase of relative mNAMPT transcript abundance from 30 to 12’000, the change observed in the other genes was not notable. Importantly, compared to Actin–Gal4, dnrk is 2-fold lower in UAS-mNAMPT and Actin > mNAMPT backgrounds (control vs. experiment, respectively). Thus, overall, there appears to be no change in mRNAs of either axon death or NAD+ synthesis genes.

In the results, we changed the text accordingly:

"We then tested the effect of mNAMPT on the NAD+ metabolic flux in vivo. Surprisingly, NAM, NMN, and NAD+ levels remained unchanged under physiological conditions (Figure 4C). However, we noticed 3-fold higher NR and a moderate but significant elevation of ADPR and cADPR levels upon mNAMPT overexpression (Figure 4C). We also asked whether mNAMPT impacts on NAD+ homeostasis thereby altering the expression of axon death or NAD+ synthesis genes. Besides the expected significant increase in the Gal4-mediated expression of mNAMPT, we did not observe any notable changes at the mRNA level (Figure 4 – figure supplement 1)."

• The authors repeatedly introduce a novel PncC antibody. However, no details on this, its generation, or its testing are found within the manuscript as presented. The antibody detects with several bands. The authors speculate that this could be a degradation product but nothing substantial is shown.

In Materials and methods, we added a new section:

"PncC antibody generation Rabbit anti-PncC antibodies were generated by Lubioscience under a proprietary protocol. The immunogen used was purified from Escherichia coli, strain K12, corresponding to the full protein sequence of NMN-D. The amino acid sequence is the following: MTDSELMQLSEQVGQALKARGATVTTAESCTGGWVAKVITDIAGSSAWFERGFVTYSNEAKAQMIGVREETLAQHGAVSEPVVVEMAIGALKAARADYAVSISGIAGPDGGSEEKPVGVWFAFATARGEGITRRECFSGDRDAVRRQAT AYALQTLWQQFLQNT"

We also updated the results referencing it.

"We found that both wild-type and enzymatically dead NMN-D enzymes are equally expressed in S2 cells, as detected by newly generated PncC antibodies (Materials & Methods, Figure 1–figure supplement 2). Notably, we observed two immunoreactivities per lane, with the lower band being a potential degradation product."

In addition, we now provide evidence why we believe that the upper band is NMN-D, while the lower one is a degradation product. In the figure attached below, the samples of the first five lanes were denatured at 70 °C, while the samples of the last two lanes were denatured at 95 °C (each for 10 min, respectively). The resulting Western blot shows that at 70 °C, there is more unspecific background, but no lower degradation product, while at 95 °C, the background is drastically reduced; however, there is a lower degradation product appearing. NMN-D is indicated by an asterisk. We feel that it is important to show this data here in the rebuttal. But we feel that it would add confusion to the readers in the manuscript.

• Olfactory receptor neuron degeneration assays are shown in Fig1 but no data is presented with it to support the images.

We agree that a quantification would support our observation. However, it is difficult to precisely quantify individual axons in the ORN injury assay, for two main reasons:

1. Severed axons are often bundled, thus the exact number cannot be scored.

2. Due to the removal of the cell body, the axonal GFP intensity decreases over time, due to the absence of mCD8::GFP synthesis. It adds another level of difficulty. Nevertheless, we added numbers to each example in Figure 1E and D, where we quantified the % of brains where severed preserved axons were observed, similar to Figure 2 in (MacDonald et al., 2006).

In the results section, we changed the text as indicated below:

"We extended the ORN injury assay and found preservation at 10, 30, and 50 dpa (Figure 1E). While quantifying the precise number of axons is technically not feasible, severed preserved axons were observed in all 10, 30, and 50 dpa brains, albeit fewer at later time points (MacDonald et al., 2006). Thus, high levels of NMN-D confer robust protection of severed axons for multiple neuron types for the entire lifespan of Drosophila."

In the Figure 1 legend, we changed the text accordingly:

"D Low NMN results in severed axons of olfactory receptor neurons that remain morphologically preserved at 7 dpa. Examples of control and 7 dpa (arrows, site of unilateral ablation). Lower right, % of brains with severed preserved axon fibers. E Low NMN results in severed axons that remain morphologically preserved for 50 days. Representative pictures of 10, 30, and 50 dpa, from a total of 10 brains imaged for each condition (arrows, site of unilateral ablation). Lower right, % of brains with severed preserved axon fibers."

Author Response

eLife assesssment:

This paper conducts human and rodent experiments of non-invasive diffusion MRI estimates of axon diameter with the aim to establish whether these estimates provide biologically specific markers of axonal degeneration in MS. It will be of interest to researchers developing quantitative MRI methods and scientists studying neurodegeneration. The experiments provide evidence for the sensitivity of these markers, but do not directly validate axon diameter and do not reflect common pathological mechanisms across rodents and humans.

We thank the Editor for the appreciation of our work. Thanks to the addition of an extensive electron microscopy paradigm, we now include a direct validation of axonal damage and expand on the common pathological mechanisms across the two species. The new results are detailed in the manuscript and summarized in Fig. 3 in the manuscript

Reviewer #1 (Public Review):

1.1 My primary concern relates to how meaningful the human-rodent comparisons are, and whether these comparisons really advance our understanding of AxCaliber estimates in MS. I applaud the aim to conduct "matched" experiments in both rodent models and human disease. It is a strength that the experiments are aligned with respect to the MRI measurements (although there are some caveats to this mentioned below). But beyond that, the overlap is not what one might hope for: the pathology would seem to be very distinct in humans and rodents, and the histological validation is not specific to what the MRI measurements claim to estimate. To summarize the main findings: (i) in a rat model of general axonal degeneration, axon calibre estimates correlate with neurofilaments; (ii) in MS in humans, axon calibre estimates correlate with demyelinating lesions. This gives a picture of AxCalibre estimates correlating with neuropathology, but is this something that has not already been established in the literature? If the aim is to validate AxCaliber, then there is a logic in using a rodent model that isolates alterations to axonal radius, but what then does this add to the existing literature in that space? If the aim is to study MS (for which AxCaliber results have been previously reported in Huang et al), then why not use a rodent model of MS?

We thank the reviewer for their very insightful comments. Indeed, multiple sclerosis (MS) is a chronic neuroinflammatory and neurodegenerative disease of unknown etiology. An enormous effort has been made to obtain animal models that simulate the pathogenesis of this disease. However, while several models exist recapitulating distinct aspects of the disease (mostly related to demyelination), MS fundamentally remains a disease that only affects humans. This does not mean that EAE or lysolecithin models do not provide information on specific aspects and are therefore valuable. In fact, we believe that trying to replicate the pathological mechanisms of this disease in an animal model goes beyond the scope of the present work. In this work, our intention is to validate a biomarker of axonal damage preclinically, and for this, we use a model of axonal degeneration. We do not claim that this model should be valid to capture the complex clinical and pathological manifestation of MS, but we do think that it is a necessary step to ensure MRI sensitivity to axonal pathology. Why necessary? Because all the available (very limited) MRI literature which provides some form of validation: i) only focuses on healthy tissue, and ii) has an n of 1. Our preclinical paradigm gives conclusive evidence that the MRI axonal diameter proxy detects axonal damage as an increase in the mean diameter. This is now detailed in the discussion.

After this necessary preclinical validation, we then apply the same framework to a human disease like MS that, among other manifestations, is believed to also cause axonal pathology. The improvements with respect to the one published work about axonal diameter in MS are: i) the whole brain analysis, which allowed us to characterize the extent of these early alterations outside the demyelinated lesions; and ii) the larger sample size, which allowed us to uncover an association with disease duration, strengthening our hypothesis about increased axonal diameter being a marker of early disease (new Fig. 5).

Regarding the nonspecificity of histological validation, we thank the reviewer for this insightful comment, which triggered an additional analysis that we believe has added further value to the paper. Using electron microscopy, we found that in our model of neurodegeneration, axonal damage is indeed reflected as an increase in axon diameter (new Fig. 3). These recent findings strongly support the validation of our noninvasive diffusion MRI estimates of axon diameter alterations as an early-stage hallmark of normal-appearing tissue in MS.

Coming back to the comparison between pathology in humans and in rodents, the EM data also support our choice of preclinical model, showing axonal swelling, the same phenomenon reported and characterized in recent postmortem histological data in the normal-appearing white matter of MS patients (Luchicchi et al., Ann Neurol 2021) and in lesions (Fisher et al. Ann Neurol 2007).

All in all, we are confident that the new data supports the validity of this translational approach, and shed new light into the degenerating aspect of MS.

Changes in the manuscript

• Discussion, pag.12: It is important to stress that the aim of this work is not to propose a new animal model of MS, a disease that only affects humans, but rather to validate axonal damage detection (independently from the pathology that has induced it) through noninvasive MRI and apply the framework to characterize axonal pathology in MS.

1.2 I appreciate that both rodent and patient studies are time intensive, major endeavors. Neverthless, the number of subjects is very low in both rodent (n=9) and human (MS=10, control=6) studies. At the very least, this should be more openly acknowledged. But I'm concerned that this is a major weakness of the paper. Related to this, I find it hard to tell how carefully multiple comparison correction was performed throughout. It seems reasonably clear for the TBSS analyses, but then other analyses were performed in ROIs. Are these multiple comparisons corrected as well? Similarly, in Methods, I am confused by the statement that: "post hoc t tests corrected for multiple comparisons whenever a significant effect was detected". What does this mean?

We thank the reviewer for this comment. We agree that a small sample size was a weakness of the previous version of the paper, and therefore, in the new version, we have substantially increased the n for both animal and human experiments (from n=9 to 19 in animals, from 16 to 21 in humans). We removed the ROI analysis in the new version, and thus the confusing statement, and clarified the strategy for multiple comparisons.

Changes in the manuscript

• Data analysis, pag. 18: Lesion masks were excluded from the statistical analysis, and multiple comparisons across clusters were controlled for by using threshold-free cluster enhancement.

1.3 While I do not think the text is in any sense deliberately misleading, I think the authors would do well to either tone down their claims or consider more carefully the implications of the text in many places. Some that stuck out for me are:

Throughout, language in the paper (e.g., "Paired t tests were used to assess differences in the axonal diameter") presumes that the AxCaliber estimates specifically reflect axon diameter. I think the jury is out over whether this is true, particularly for measurements conducted with limited hardware specs. At the very least, I would encourage the author to refer to these measurements throughout as "estimates" of axon diameter.

Thank you for this clarification. We have indeed changed the notation, and now consistently refer to the estimates of axon diameter through MRI as the “MRI axonal diameter proxy”.

1.4 The authors suggest that their results provide "new tools for patient stratification" based on differences in lesion type, but it isn't clear what new information these markers would confer given that the lesions are differentiated based on T1w hypo/hyperintensities. In other words, these lesions are by definition already differentiable from a much simpler MRI marker.

Thank you for this insightful comment. The reviewer is right, and following the general reviewers’ assessment we have decided to not include the lesion analysis in the new version of the manuscript.

1.5 The authors note in the Discussion that: "sensitive to early stages of axonal degeneration, even before alterations in the myelin sheet are detected". Whether intentional or not, the implication in the context of this study is that this would hold for MS (that these markers would detect axonal degeneration preceding demyelination). While there is some discussion of alterations to axonal diameter in MS, the authors do not discuss whether these are the same mechanisms thought to occur in the IBO intervention used here.

Thank you for this comment. Indeed, the scope of the paper is not to assess whether axonal swelling precedes or not myelin alterations, so we agree with the reviewer that this sentence might be misleading and have removed it in the text. While we do not claim that ibotenic acid injections are able to replicate the complex clinical and pathological manifestation of MS (and now we made it clear in the revised manuscript, see comment 1), the electron microscopy paradigm indicates the presence of axonal swelling in the damaged fimbria, which is indeed the same pathological manifestation found in MS post-mortem data (see e.g. Fisher et al. Ann Neurol 2007).

1.6 In the Discussion, the authors note the lack of evidence for a relationship with disability or disease duration, but nevertheless, go on to interpret the "trends" they do observe. I would advise strongly against this: the authors acknowledge that their numbers are low, so I would avoid the temptation to speculate here.

The reviewer is 100% correct. We should have refrained from speculating. In the new version of the paper, however, thanks to the larger human cohort, we were able to find significant associations with disease duration in voxelwise analysis of the white matter skeleton in standard space and in the whole white matter in single subject space (new Figure 5).

1.7 In the Discussion state that "the use of neurofilaments has also been well validated in MS". Well validated for what? MS is a complex disease with a broad range of pathology, so this statement could be read to mean "neurofilaments are known to be altered in MS". However, in the context of this paragraph, the implication would seem to be that neurofilaments are a wellestablished proxy for axonal diameter. Is that the implication, and if so what general evidence is there for this?

We thank the reviewer for this insightful comment. Indeed, altered neurofilaments are not conclusive evidence of increased axonal diameter. In this context, the addition of electron microscopy data in the new manuscript version supports the claim.

Reviewer #2 (Public Review):

Diffusion MRI is sensitive to the brain microstructure, and it has been used to assess the integrity of white matter for nearly 3 decades. Its main limitation is the limited specificity, which makes it difficult to link changes in diffusion parameters to a given pathological substrate. Recently methods based on diffusion MRI that enable the estimation of axonal diameter, non invasively, have become available. This paper aims at validating one of such methods using an experimental model of neurodegeneration. The authors found a significant correlation between axonal diameter estimated by MRI and an histological marker of neurodegeneration. Although this is of great interest, as it demonstrates that this method is sensitive to neurodegeneration, a direct validation would require a measurement of axonal diameter using electron or confocal microscopy, rather than a correlation with a measure of axonal degeneration not directly related to axonal diameter. So, although these data are compelling, they do not prove that the increase in axonal diameter suggested by diffusion MRI corresponds to actual axonal swelling. The Authors also apply the same method to compare the white matter of patients with multiple sclerosis (MS) and healthy controls, showing widespread increases in axonal diameter in the patients. These data are compelling, but again, not conclusive. Other factors such as gloss could bias the MRI measurement and lead to an apparent increase in axonal diameter.

We would like to thank the reviewer for the positive assessment of our work and for the valuable suggestion. We are confident that the new version of the manuscript, by including an extensive validation based on electron microscopy, has addressed the reviewer´s criticisms.

Reviewer #3 (Public Review):

3.1 In this paper, Toschi et al. performed dMRI to in vivo estimate axon diameter in the brain and demonstrated that multi-compartmental modeling (AxCaliber) is sensitive to microstructural axonal damage in rats and axon caliber increase in demyelinating lesions in MS patients, suggesting that axon diameter mapping provides a potential biomarker to bridge the gap between medical imaging contrasts and biological microstructure. In particular, authors injected ibotenic acid (IBO) and saline in the left and right rat hippocampus, respectively, and compared in vivo estimated axon diameter and ex vivo neurofilament staining in left and right fimbria. The axon size estimation was larger in the fimbria of IBO injection side, where the neurofilament intensity is higher. Correlation of axon size estimation and neurofilament intensity was observed in both injection sides. Further, higher axon diameter estimation was observed in normal appearing white matter (NAWM) of MS patients, compared with the healthy subjects. The axon size estimation increased in hypointense lesions of T1 weighted contrast, but not in isointense lesions. Through the comparison of dMRI-estimated axon size and histology-based fluorescence intensity, authors indirectly validated the sensitivity of axon diameter mapping to the tissue microstructure in the rat brain, and further explored the axon size change in the brain of MS patients. However, the dMRI protocol and biophysical modeling in this study were not fully optimized to maximize the sensitivity to axon size estimation, and the dMRI-estimated axon size (4.4-5.4 micron) was much larger than values reported in previous histological studies (0.5-3 micron) [Barazany et al., Brain 2009]. Finally, although the modified AxCaliber model incorporated two fiber bundles in different directions, the fiber dispersion in each bundle was not considered (c.f. fiber dispersion ~20-30 degree in corpus callosum), potentially leading to overestimated axon diameter.

We thank the reviewer for their appreciation of our work, which we believe is substantially improved in this revised version through the inclusion of an electron microscopy paradigm. Below, the point-by-point response to the specific points raised.

3.2 The conclusions in this study are supported by experimental results. However, the dMRI protocol and biophysical model could be further optimized and validated: 1. To in vivo estimate the axon diameter ~1 micron using dMRI, strong diffusion weighting (b-value) should be applied to maximize the signal decay due to intra-axonal restricted diffusion and minimize the signal contribution of extra-cellular hindered diffusion. However, authors only applied maximal b-value = 4000 s/mm2, much smaller than values ~15,00020,000 s/mm2 in previous studies [Assaf et al., MRM 2008; Huang et al., BSAF 2020, 225:1277]. The use of low diffusion weighting in this study leads to a lower bound ~4-6 micron for accurate diameter estimation, the so-called resolution limit in [Nilsson et al., NMR Biomed 2017, 30:e3711]. In other words, the estimated axon diameter is potentially overestimated and related with the imaging protocol and image quality, confounding the biological interpretation.

We thank the reviewer for this insightful comment. Indeed, while the resolution limit is a concern, the chosen b-value has been a compromise between sensitivity to small structure and SNR, as indicated by recent animal (Crater et al., 2022) and human (Jensen et al., 2016; McKinnon et al., 2017; Moss et al., 2019) work, pointing at 3000-4000 s/mm2 as the b-value for which the intra-axonal water signal is dominant. In addition, a paper from the laboratory that first developed the Axcaliber method recently came out (Gast et al., 2023, DOI: 10.1007/s12021-023-09630-w) demonstrating that an MRI protocol with a maximum b-value between 3000 and 4000 s/mm2 (and even lower) is sufficient to capture, in vivo and in humans, various well-known aspects of axonal morphometry (e.g., the corpus callosum axon diameter variation) as well as other aspects that are less explored (e.g., axon diameter-based separation of the superior longitudinal fasciculus into segments). The same paper contains resources and further bibliography supporting the fact that experimental evidence suggests that the contribution of intra-axonal water to restricted diffusion signals dominates other factors (see Online Resource 1, section A of the same paper). To challenge this recent evidence from a neurobiology perspective, we include in the supplementary material a subset of experiments in animals with lower maximum b-value (2500 s/mm2, Fig. S1), where we are able to detect the same effect of increased MRI axonal diameter proxy in the injected hemisphere compared to control.

We would like to add that while extremely valuable and informative, simulation studies such as the excellent study by Veraart et al., 2020, are inevitably valid under certain assumptions. Among them, some critical ones are i) the need to neglect nonaxonal cells such as glia, ii) assuming that the bulk diffusivity of water in cerebral tissue would be the same as that of free water, and iii) impermeable barriers. All these assumptions are expected to play a role in the estimated resolution limit, a role difficult to quantify but likely substantial.

For this reason, we believe that our approach, which is 100% focused on neurobiology and measurements performed in real tissue, can offer a different perspective and fuel the ongoing debate on axonal diameter measurement feasibility. We acknowledge the value of the reviewer comment and discuss the issue of b-value in the discussion (see also comment 1.8).

Changes in the manuscript

• Discussion, pag. 12:<br /> Despite some inevitable minor differences due to different brain sizes and magnet features, the human protocol was built to match the main characteristics of the preclinical diffusion sequence, such as the b-value and diffusion time range. The chosen b-value has been a compromise between sensitivity to small structures and the signalto-noise ratio (SNR), as indicated by recent animal (Crater et al., 2022) and human (Gast et al., 2023; Jensen et al., 2016; McKinnon et al., 2017; Moss et al., 2019) work, pointing at 4000 s/mm2 as the b-value for which the intra-axonal water signal is dominant. However, following recent work supporting sensitivity of diffusion-weighted MRI to axonal diameter even at lower b-values (Gast et al., 2023), we tested a protocol with a lower b-value in a subset of animals, with the aim of facilitating future clinical AxCaliber studies. We found no qualitative differences in the outcome (MRI axonal diameter proxy was increased following fimbria damage). Further work and perhaps more realistic simulations, considering real cell composition and morphology, are needed to clarify this issue.

3.3 In this study, the positive correlation of dMRI-estimated axon size and neurofilament fluorescence intensity is indeed an encouraging result, and yet this validation is indirect since it relies on the positive correlation between neurofilament intensity and axon diameter in histology.

The reviewer correctly points out a severe limitation of the previous manuscript version, which is now addressed by including an extensive electron microscopy evaluation, recapitulated in new Fig. 3.

3.4 Authors did not consider the fiber dispersion in the proposed dMRI model. This can lead to overestimated axon diameter, even in the highly aligned WM, such as corpus callosum with ~20-30 degree dispersion in histology [Ronen et al., BSAF 2014, 219:1773; Leergaard et all, PLoS One 2010, 5(1), e8595] and MRI [Dhital et al., NeuroImage 2019, 189, 543; Novikov et al., NeuroImage 2018, 174:518].

The reviewer is correctly pointing out an important characteristic of while matter microstructure as is fibre dispersion. However, we would like to point out that the use of a second fiber population is expected to mitigate this effect by absorbing some axonal directional dispersion in areas of a single fiber. To support this, we quantified dispersion as the angle between the two main fiber orientations captured by the AxCaliber fit, as showed in Author response image 1 for two representative subjects (one control, upper line, and one MS, lower line; the “dispersion” maps are masked by a white matter probability mask, and superimposed to a T2w). Indeed, the angle between the two main fibres in the corpus callosum is around 20 degrees or lower, compatible with the bibliography cited by the reviewer, and higher in other white matter areas known to be characterized by fiber crossing and dispersion.

Author response image 1.

Angle in radians between the two main fiber orientations captured by the AxCaliber fit, as showed below for two representative subjects (one control, upper line, and one MS, lower line). The dispersion maps are masked by a white matter probability mask (P>=0.95), and superimposed to a T2-weighted image.

Author Response

Reviewer #1 (Public Review):

This paper shows that a principled, interpretable model of auditory stimulus classification can not only capture behavioural data on which the model was trained but somewhat accurately predict behaviour for manipulated stimuli. This is a real achievement and gives an opportunity to use the model to probe potential underlying mechanisms. There are two main weaknesses. Firstly, the task is very simple: distinguishing between just two classes of stimuli. Both model and animals may be using shortcuts to solve the task, for example (this is suggested somewhat by Figure 8 which shows the guinea pig and model can both handle time-reversed stimuli).

The task structure is indeed simple. In the context of categorization tasks that are typically used in animal experiments, however, we would argue that we are the higher end of stimulus complexity. Auditory categories used in most animal experiments typically employ a category boundary along a single stimulus parameter (for example, tone frequency or modulation frequency of AM noise). Only a few recent studies (for example, Yin et al., 2020; Town et al., 2018) have explored animal behavior with “non-compact” stimulus categories. Thus, we consider our task a significant step towards more naturalistic tasks.

We were also faced with the practical factor of the trainability of guinea pigs (GPs). Prior to this study, guinea pigs have been trained using classical conditioning and aversive reinforcement on detecting tone frequency (e.g., Heffner et al., 1971; Edeline et al., 1993). More recently, competitive training paradigms have been developed for appetitive conditioning, using a single “footstep” sound as a target stimulus and manipulated sounds as non-target stimuli (Ojima and Horikawa, 2016). But as GPs had never been trained on more complex tasks before our study, we started with a conservative one vs. one categorization task. We mention this in the Discussion section of the revised manuscript (page 27, line 665).

To determine whether these results hold for more complex tasks as well, after receiving the reviews of the original manuscript, we trained two GPs (that were originally trained and tested on the wheeks vs. whines task) further on a wheeks vs. many (whines, purrs, chuts) task. As earlier, we tested these GPs with new exemplars and verified that they generalized. In the figure below, the average performance of the two GPs on the regular (training) stimuli and novel (generalization) stimuli are shown in gray bars, and individual animal performances are shown as colored discs. The GPs achieved high performance for the novel stimuli, demonstrating generalization. We also implemented a 4-way WTA stage for a wheek vs. many model and verified that the model generalized to new stimuli as well.

For frequency-shifted calls, these two GPs performed better for wheeks vs. many compared to the average for wheeks vs. whines shown in the main manuscript. The 4-way WTA model closely tracked GP behavioral trends.

The psychometric curves for wheeks vs. many categorization in noise (different SNRs) did not differ substantially from the wheeks vs. whines task.

We focused our one vs. many training on the two conditions that showed the greatest modulation in the one vs. one tasks. However, these preliminary results suggest that the one vs. one results presented in the manuscript are likely to extend to more complex classification tasks as well. We chose not to include these new data in the revised manuscript because we performed these experiments on only 2 animals, which were previously trained on a wheeks vs. whines task. In future studies, we plan to directly train animals on one vs. many tasks.

Secondly, the predictions of the model do not appear to be quite as strong as the abstract and text suggest.

We now replace subjective descriptors with actual effect size numbers to avoid overstatingresults. We also include additional modeling (classification based on the long-term spectrum) and discuss alternative possibilities to provide readers with points of comparison. Thus, readers can form their own opinions of the strengths of the observed effects.

The model uses "maximally informative features" found by randomly initialising 1500 possible features and selecting the 20 most informative (in an information-theoretic sense). This is a really interesting approach to take compared to directly optimising some function to maximise performance at a task, or training a deep neural network. It is suggestive of a plausible biological approach and may serve to avoid overfitting the data. In a machine learning sense, it may be acting as a sort of regulariser to avoid overfitting and improve generalisation. The 'features' used are basically spectro-temporal patterns that are matched by sliding a crosscorrelator over the signal and thresholding, which is straightforward and interpretable.

This intuition is indeed accurate – the greedy search algorithm (described in the original visionpaper by Ullman et al., 2002) sequentially adds features that add the most hits and the least false alarms compared to existing members of the MIF set to the final MIF set. The latter criterion (least false alarms) essentially guards against over-fitting for hits alone. A second factor is the intermediate size and complexity of MIFs. When MIFs are too large, there is certainly overfitting to the training exemplars, and the model does not generalize well (Liu et al., 2019).

It is surprising and impressive that the model is able to classify the manipulated stimuli at all. However, I would slightly take issue with the statement that they match behaviour "to a remarkable degree". R^2 values between model and behaviour are 0.444, 0.674, 0.028, 0.011, 0.723, 0.468. For example, in figure 5 the lower R^2 value comes out because the model is not able to use as short segments as the guinea pigs (which the authors comment on in the results and discussion). In figure 6A (speeding up and slowing down the stimuli), the model does worse than the guinea pigs for faster stimuli and better for slower stimuli, which doesn't qualitatively match (not commented on by the authors). The authors state that the poor match is "likely because of random fluctuations in behavior (e..g motivation) across conditions that are unrelated to stimulus parameters" but it's not clear why that would be the case for this experiment and not for others, and there is no evidence shown for it.

Thank you for this feedback. There are two levels at which we addressed these comments inthe revised manuscript.

First, regarding the language – we have now replaced subjective descriptors with the statement that the model captures ~50% of the overall variance in behavioral data. The ~50% number is the average overall R2 between the model and data (0.6 and 0.37 for the chuts vs. purrs and wheeks vs. whine tasks respectively). We leave it to readers to interpret this number.

Second, our original manuscript lacked clarity on exactly what aspects of the categorization behavior we were attempting to model. As recent studies have suggested, categorization behavior can be decomposed into two steps – the acquisition of the knowledge of auditory categories, and the expression of this knowledge in an operant task (Kuchibhotla et al., 2019; Moore and Kuchibhotla, 2022). Our model solely addresses how knowledge regarding categories is acquired (through the detection of maximally informative features). Other than setting a 10% error in our winner-take-all stage, we did not attempt to systematically model any other cognitive-behavioral effects such as the effect of motivation and arousal. Thus, in the revised manuscript, we have included a paragraph at the top of the Results section that defines our intent more clearly (page 5, line 117). We conclude the initial description of the behavior by stating that these factors are not intended to be captured by the model (page 6, line 171). We also edited a paragraph in the Discussion section for clarity on this point (page 26, line 629).

In figure 11, the authors compare the results of training their model with all classes, versus training only with the classes used in the task, and show that with the latter performance is worse and matches the experiment less well. This is a very interesting point, but it could just be the case that there is insufficient training data.

This could indeed be the case, and we acknowledge this as a potential explanation in therevised manuscript (page 22, line 537; page 27, line 653). Our original thinking was that if GPs were also learning discriminative features only using our training exemplars, they would face a similar training data constraint as well. But despite this constraint, the model’s performance is above d’=1 for natural calls – both training and novel calls; it is only the similarity with behavior on the manipulated stimuli that is lower than the one vs. many model. This phenomenon warrants further investigation.

Reviewer #2 (Public Review):

Kar et al aim to further elucidate the main features representing call type categorization in guinea pigs. This paper presents a behavioral paradigm in which 8 guinea pigs (GPs) were trained in a call categorization task between pairs of call types (chuts vs purrs; wheek vs whines). The GPs successfully learned the task and are able to generalize to new exemplars. GPs were tested across pitch-shifted stimuli and stimuli with various temporal manipulations. Complementing this data is multivariate classifier data from a model trained to perform the same task. The classifier model is trained on auditory nerve outputs (not behavioral data) and reaches an accuracy metric comparable to that of the GPs. The authors argue that the model performance is similar to that of the GPs in the manipulated stimuli, therefore, suggesting that the 'mid-level features' that the model uses may be similar to those exploited by the GPs. The behavioral data is impressive: to my knowledge, there is scant previous behavioral data from GPs performing an auditory task beyond audiograms measured using aversive conditioning by Heffner et al., in. 1970. [One exception that is notably omitted from the manuscript is Ojima and Horikawa 2016 (Frontiers)]. Given the popularity of GPs as a model of auditory neurophysiology these data open new avenues for investigation. This paper would be useful for neuroscientists using classifier models to simulate behavioral choice data in similar Go/No-Go experiments, especially in guinea pigs. The significance of the findings rests on the similarity (or not) of the model and GP performance as a validation of the 'intermediary features' approach for categorization. At the moment the study is underpowered for the statistical analysis the authors attempt to employ which frequently relies on non-significant p values for its conclusions; using a more sophisticated approach (a mixed effects model utilizing single trial responses) would provide a more rigorous test of the manipulations on behavior and allow a more complete assessment of the authors' conclusions.

We thank the reviewer for their feedback and the suggestion for a more robust statistical approach. We have now replaced the repeated measures ANOVA based statistics for the behavior and model where more than 2 test conditions were presented (SNR, segment length, tempo shift, and frequency shift) with generalized linear models with a logit link function (logistic activation function). In these models, we predict the trial-by-trial behavioral or model outcome from predictors including stimulus type (Go or Nogo), parameter value (e.g., SNR value), parameter sign (e.g., positive or negative freq. shift), and animal ID as a random effect. To evaluate whether parameter value and sign had a significant contribution to the model, we compare this ‘full’ model against a null model that only has stimulus type as a predictor and animal ID as a random effect. These analyses are described in detail in the Materials and Methods section of the revised manuscript (page 36, line 930).

These analyses reveal significant effects of segment length changes, and weak effects of tempo changes on behavior (as expected by the reviewer). Both the behavior and model showed similar statistical significance (except tempo shift for wheeks vs. whines) for whether performance was significantly affected by a given parameter.

The behavioral data presented here are descriptive. The central conceptual conclusions of the manuscript are derived from the comparison between the model and behavioral data. For these comparisons, the p-value of statistical tests is not used. We realized that a description of how we compared model and behavioral data was not clear in the original manuscript. To compare behavioral data with the model, we fit a line to the d’ values obtained from the model plotted against the d’ values obtained from behavior, and computed the R2 value. We used the mean absolute error (MAE) to quantify the absolute deviation between model and behavior d’ values. Thus, high R2 values would signify a close correspondence between the model and behavior regardless of statistical significance of individual data points. We now clarify this in page 12, line 289. We derive R2 values for individual stimulus manipulations, as well as an overall R2 by pooling across all manipulations (presented in Fig. 11). This is now clarified in page 21, line 494.

Reviewer #3 (Public Review):

The authors designed a behavioral experiment based on a Go/ No-Go paradigm, to train guinea pigs on call categorization. They used two different pairs of call categories: chuts vs. purrs and wheeks vs. whines. During the training of the animals, it turned out that they change their behavioral strategies. Initially, they do not associate the auditory stimuli with rewards, and hence they overweight the No-Go behavior (low hit and false alarm rate). Subsequently, they learned the association between auditory stimuli and reward, leading to overweighting the Go behavior (high hit and false alarm rates). Finally, they learn to discriminate between the two call categories and show the corresponding behaviors, i.e. suppress the Go behavior for No-go stimuli (improved discrimination performance due to stable hit rates but lower false alarm rates).

In order to derive a mechanistic explanation of the observed behaviors, the authors implemented a computational feature-based model, with which they mirrored all animal experiments, and subsequently compared the resulting performances.

Strengths:

In order to construct their model, the authors identified several different sets of so-called MIFs (most informative features) for each call category, that were best suited to accomplish the categorization task. Overall, model performance was in general agreement with behavioral performance for both the chuts vs. purrs and wheeks vs. whines tasks, in a wide range of different scenarios.

Different instances of their model, i.e. models using different of those sets of MIFs, performed equally well. In addition, the authors could show that guinea pigs and models can generalize to categorize new call exemplars very rapidly.

The authors also tested the categorization performance of guinea pigs and models in a more realistic scenario, i.e. communication in noisy environments. They find that both, guinea pigs and the model exhibit similar categorization-in-noise thresholds.

Additionally, the authors also investigated the effect of temporal stretching/compression of calls on categorization performance. Remarkably, this had virtually no negative effect on both, models and animals. And both performed equally well, even for time reversal. Finally, the authors tested the effect of pitch change on categorization performance, and found very similar effects in guinea pigs and models: discrimination performance crucially depends on pitch change, i.e. systematically decreases with the percentage of change.

Weaknesses:

While their computational model can explain certain aspects of call categorization after training, it cannot explain the time course of different behavioral strategies shown by the guinea pigs during learning/training.

Thank you for bringing this up – in hindsight the original manuscript lacked clarity on exactlywhat aspects of the behavior we were trying to model. As recent studies have suggested, categorization behavior can be decomposed into two steps – the acquisition of the knowledge of auditory categories, and the expression of this knowledge in an operant task (Kuchibhotla et al., 2019; Moore and Kuchibhotla, 2022) . Our model solely addresses how knowledge regarding categories is acquired (through the detection of maximally informative features). Other than setting a 10% error in our winner-take-all stage, we did not attempt to systematically model any other cognitive-behavioral effects such as the effect of motivation and arousal, or behavioral strategies. Thus, in the revised manuscript, we have included a paragraph at the top of the Results section that defines our intent more clearly (page 5, line 117). We conclude the initial description of the behavior by stating that these factors are not intended to be captured by the model (page 6, line 171). We also edited a paragraph in the Discussion section for clarity on this point (page 26, line 629).

Furthermore, the model cannot account for the fact that short-duration segments of calls (50ms) already carry sufficient information for call categorization in the guinea pig experiment. Model performance, however, only plateaued after a 200 ms duration, which might be due to the fact that the MIFs were on average about 110 ms long.

The segment-length data indeed demonstrates a deviation between the data and the model.As we had acknowledged in the original manuscript, this observation suggests further constraints (perhaps on feature length and/or bandwidth) that need to be imposed on the model to better match GP behavior. We originally did not perform this analysis because we wanted to demonstrate that a model with minimal assumptions and parameter tuning could capture aspects of GP behavior.

We have now repeated the modeling by constraining the features to a duration of 75 ms (thelowest duration for which GPs show above-threshold performance). We found that the constrained MIF model better matched GP behavior on the segment-length task (R2 of 0.62 and 0.58 for the chuts vs. purrs and wheeks vs. whines tasks; with the model crossing d’=1 for 75 ms segments for most tested cases). The constrained MIF model maintained similarity to behavior for the other manipulations as well, and yielded higher overall R2 values (0.66 for chuts vs. purrs, 0.51 for wheeks vs. whines), thereby explaining an additional 10% of variance in GP behavior.

In the revised manuscript, we included these results (page 28, line 699), and present results from the new analyses as Figure 11 – Figure Supplement 2.

In the temporal stretching/compressing experiment, it remains unclear, if the corresponding MIF kernels used by the models were just stretched/compressed in a temporal direction to compensate for the changed auditory input. If so, the modelling results are trivial. Furthermore, in this case, the model provides no mechanistic explanation of the underlying neural processes. Similarly, in the pitch change experiment, if MIF kernels have been stretched/compressed in the pitch direction, the same drawback applies.

We did not alter the MIFs in any way for the tests – the MIFs were purely derived by trainingthe animal on natural calls. In learning to generalize over the variability in natural calls, the model also achieved the ability to generalize over some manipulated stimuli. The fact that the model tracks GP behavior is a key observation supporting our argument that GPs also learn MIF-like features to accomplish call categorization.

We had mentioned at a few places that the model was only trained on natural calls. To addclarity, we have now included sentences in the time-compression and frequency-shifting results affirming that we did not manipulate the MIFs to match test stimuli. We also include a couple of sentences in the Discussion section’s first paragraph stating the above argument (page 26, line 615).

Author Response:

Reviewer #2:

Non-canonical pathways for regulating protein synthesis serve important roles for controlling gene expression in critical developmental pathways. Homeobox (Hox) genes encode many mRNAs regulated at the level of translation. A general feature for many of these mRNAs has been the proposal they are regulated by Internal Ribosome Entry Sites (IRESs) and possess sequences in the 5'-untranslated regions (5'-UTR) of the mRNA that prevent canonical cap-dependent translation, termed "translation inhibitory elements" or TIEs. However, the mechanisms by which these Hox mRNAs are regulated remain unclear. Here, the authors focus on two Hox mRNAs, Hox a3 and Hox a11, and find they use entirely different means to achieve the same end of repressing cap-dependent translation. Hox a3 uses the non-canonical translation initiation factor eIF2D and an upstream open reading fram (uORF), whereas a11 uses a "start-stop" uORF followed by a thermodynamically stable stem-loop to inhibit translation. Overall, the experiments support the major conclusions drawn by the authors, and nail down mechanisms that have been left unresolved since the Hox mRNAs were first discovered to be regulated at the level of translation. These results will be of wide interest to the translation and developmental biology fields.

Some issues the authors should consider:

1) The mapping of the TIE boundaries are in general well-supported by the luciferase reporter experiments. However, there seems to be a disconnect in the luciferase values in Fig. 1B compared to the western blots in Supplementary Fig. 1D, however. For example, in the a3 case the 106 and 113 bands don't seem to correspond to levels consistent with the luciferase activity. For a11, the 153 band is not consistent with the luciferase activity. Also, the gels at the bottom are confusing. Should 74 in the left gel be 77? It would help to have a clearer explanation in the figure legend.

The reviewer is right, supplementary figure 1D is misleading. We have clarified the data with a new supplementary figure 1D. The gels presented in this figure are not western blots, they are SDS-page analysis of translated product (i.e. Renilla luciferase protein) in the presence of 35S-Methionin. Since the function of TIE elements was measured in comparison with reporters that do not contain any TIE element, we loaded on each gel a reference (lanes w/o TIE) for quantification purposes. Since the exposure time of distinct gels was variable, one should not compare the intensities in between gels. We added the quantification of the gel intensity related to the reference construct (w/o TIE). We agree with the reviewer that the two gels at the bottom are not informative, we removed them from the new supplemental figure 1D.

2) The results in the various sucrose gradients are not entirely convincing as presented. In all these cases, the experiment would benefit from the use of high-salt conditions (See Lodish and Rose, 1977, JBC 252, 1181-ff) in the gradient to remove background 80S not engaged with mRNAs. For the +cycloheximide sample in Fig. 8, this looks more like a "half-mer" between a monosome and disome, rather than a standard polysome.

We do not agree with the point raised by the reviewer on sucrose gradients. Obviously this is due to a misunderstanding of the conducted experiments. We would like to remind that the plots shown in the manuscript represent the percentage of mRNA transcripts labelled with a radioactive cap that were introduced in cell-free translation extracts. Therefore, since we monitor only radioactivity, the sole radioactive mRNA transcripts tested in these experiments are observed, consequently there is no background 80S that are not engaged with mRNAs. Such background 80S are visible on the OD profile shown now in a novel supplementary figure S6. However, non-engaged 80S are not radioactive and mRNAs that are not engaged in the 80S are found in the RNP fraction. The absence of radioactive background 80S is further corroborated by the use of edeine that prevents the codon-anticodon interaction (see data below).

When we setup our experimental strategy, we first used edeine to validate our protocol, in this case no radioactive 80S is observed confirming that no background 80S is present in our assays. In conclusion, peaks at the level of 80S can only be radioactive mRNA engaged in an 80S. We have extended the figure legend to clarify the conducted experiments.

Concerning Fig 8, we agree that this experiment is not conclusive and propose to remove it as mentioned in response to a comment from reviewer #1.

3) In Fig. 7, it would be helpful to see the absolute level of translation from the reporters, as it is not clear what the baseline level of translation is in the knockdown cell lines. It's hard to judge the eIF4E knockdown case in particular without this information. Also in panel B, the GGCCC147 cell line is missing.

As previously mentioned, we agree that Fig 7 is misleading and we have completely remodelled the figure in the revised manuscript. See also point 5 from reviewer #1. Because the GGCCC147 mutation had no effect in RRL, we decided not to test it in HEK cells and focused on the GGCC107 that has a significant effect both in RRL and in HEK cells.

4) From the MS experiments in Fig. 6 and Supplementary Fig. 6, the authors focus on eIF2D, which makes sense. But they don't comment on two other highly suggestive hits in the a3 vs. beta-globin and a3 vs. a11 comparisons. These are eIF5B and HBS1L. Both are highly suggestive of what might be going in with the eIF2D-dependent translation mechanism. They don't show up in the GMP-PNP samples in Supplementary Fig. 6, which is interesting and would deserve a comment.

We are grateful for this very interesting comment. As suggested, we have inserted a comment related to HBS1L and eIF5B in the discussion of the manuscript.

Author Response

Reviewer #1 (Public Review):

The authors have tried to correlate changes in the cellular environment by means of altering temperature, the expression of key cellular factors involved in the viral replication cycle, and small molecules known to affect key viral protein-protein interactions with some physical properties of the liquid condensates of viral origin. The ideas and experiments are extremely interesting as they provide a framework to study viral replication and assembly from a thermodynamic point of view in live cells.

The major strengths of this article are the extremely thoughtful and detailed experimental approach; although this data collection and analysis are most likely extremely time-consuming, the techniques used here are so simple that the main goal and idea of the article become elegant. A second major strength is that in other to understand some of the physicochemical properties of the viral liquid inclusion, they used stimuli that have been very well studied, and thus one can really focus on a relatively easy interpretation of most of the data presented here.

There are three major weaknesses in this article. The way it is written, especially at the beginning, is extremely confusing. First, I would suggest authors should check and review extensively for improvements to the use of English. In particular, the abstract and introduction are extremely hard to understand. Second, in the abstract and introduction, the authors use terms such as "hardening", "perturbing the type/strength of interactions", "stabilization", and "material properties", for just citing some terms. It is clear that the authors do know exactly what they are referring to, but the definitions come so late in the text that it all becomes confusing. The second major weakness is that there is a lack of deep discussion of the physical meaning of some of the measured parameters like "C dense vs inclusion", and "nuclear density and supersaturation". There is a need to explain further the physical consequences of all the graphs. Most of them are discussed in a very superficial manner. The third major weakness is a lack of analysis of phase separations. Some of their data suggest phase transition and/or phase separation, thus, a more in-deep analysis is required. For example, could they calculate the change of entropy and enthalpy of some of these processes? Could they find some boundaries for these transitions between the "hard" (whatever that means) and the liquid?

The authors have achieved almost all their goals, with the caveat of the third weakness I mentioned before. Their work presented in this article is of significant interest and can become extremely important if a more detailed analysis of the thermodynamics parameters is assessed and a better description of the physical phenomenon is provided.

We thank you for the comments and, in particular, for being so positive regarding the strengths of our manuscript and for raising concerns that will surely improve it. We have taken the following actions to address your concerns:

1) Extensive revisions have been made to the use of English, particularly in the abstract and introduction. Key terms are defined as they are introduced in the text to enhance the clarity of the argument. This is a significant revision that is highlighted within the text, but it is too extensive to detail here.

2) In the results section, we improved and extended the discussion of our graphs to the extent possible. However, we found that attempting to explain the graphs' meanings more thoroughly would detract from our manuscript's main focus: identifying thermodynamic changes that could potentially lead to alterations in material properties, specifically aspect ratio, size, and Gibbs free energy. As a result, we introduced the type of information we could obtain from our analyses in the introduction (Lines 112-125) and briefly commented on it in the ‘results’ section (Lines 304-306, sentences below).

From introduction – lines 112-125:

“In addition, other parameters like nucleation density determine how many viral condensates are formed per area of cytosol. Overall, the data will inform us if changing one parameter, e.g. the concentration, drives the system towards larger condensates with the same or more stable properties, or more abundant condensates that are forced to maintain the initial or a different size on account of available nucleation centres (Riback et al., 2020:Snead, 2022 #1152). It will also inform us if liquid viral inclusions behave like a binary or a multi-component system. In a binary mixture, Cdilute is constant (Klosin et al., 2020). However, in multi-component systems, Cdilute increases with bulk concentration (Riback et al., 2020). This type of information could have direct implications about the condensates formed during influenza infection. As the 8 different genomic vRNPs have a similar overall structure, they could, in theory, behave as a binary system between units of vRNPs and Rab11a. However, a change in Cdilute with concentration would mean that the system behaves as a multi-component system. This could raise the hypothesis that the differences in length, RNA sequence and valency that each vRNP has may be relevant for the integrity and behaviour of condensates.”.

From results lines 304-306:

This indicates that the liquid inclusions behave as a multi-component system and allow us to speculate that the differences in length, RNA sequence and valency that each vRNP may be key for the integrity and behaviour of condensates.

3) The reviewer has drawn our attention to the absence of phase separation analysis in our study. We believe that the formation of influenza A virus condensates is governed by phase separation (or percolation coupled to phase separation). However, we must exercise caution at this point because the condensates we are studying are highly complex, and the physics of our cellular system may not be adequate to claim phase separation without being validated by an in vitro reconstitution system. IAV inclusions contain a variety of cellular membranes, different vRNPs, and Rab11a. While we have robust data to propose a model in which the liquid-like properties of IAV inclusions arise from a network of interacting vRNPs that bridge multiple cognate vRNP-Rab11 units on flexible membranes, similar to what occurs in phase-separated vesicles in neurological synapses, our model for this system still lacks formal experimental validation. As a note, the data supporting our model includes: the demonstration of the liquid properties of our liquid inclusions (Alenquer et al. 2019, Nature Communications, 10, 1629); and impairment of recycling endocytic activity during IAV infection Bhagwat et al. 2020, Nat Commun, 11, 23; Kawaguchi et al. 2012, J Virol, 86, 11086-95; Vale-costa et al. 2016, J Cell Sci, 129, 1697-710. This leads to aggregated vesicles seen by correlative light and electron microscopy (Vale-Costa et al., 2016 JCS, 129, 1697-710) and by immunofluorescence and FISH (Amorim et al. 2011,. J Virol 85, 4143-4156; Avilov et al. 2012, Vaccine 30, 7411-7417; Chou et al. 2013, PLoS Pathog 9, e1003358; Eisfeld et al. 2011, J Virol 85, 6117-6126 and Lakdawala et al. 2014, PLoS Pathog 10, e1003971.

To be able to explore the significance of the liquid material properties of IAV inclusions, we used the strategy described in this current work. By developing an effective method to manipulate the material properties of IAV inclusions, we provide evidence that controlled phase transitions can be induced, resulting in decreased vRNP dynamics in cells and a negative impact on progeny virion production. This suggests that the liquid character of liquid inclusions is important for their function in IAV infection. We have improved our explanation addressing this concern in the limitations of our study (as outlined below in the box and in manuscript in lines 857-872).

We are currently establishing an in vitro reconstitution system to formally demonstrate, in an independent publication, that IAV inclusions are formed by phase separation (or percolation coupled to phase separation). For this future work, we teamed up with Pablo Sartori, a theorical physicist to derive in-depth analysis of the thermodynamics of the viral liquid condensates in the in vitro reconstituted system and compare it to results obtained in the cell. This will provide means to establish comparisons. We think that cells have too many variables to derive meaningful physics parameters (such as entropy and enthalpy) and models that need to be complemented by in vitro systems. For example, increasing the concentration inside a cell is not a simple endeavour as it relies on cellular pathways to deliver material to a specific place. At the same time, the 8 vRNPs, as mentioned above, have different size, valency and RNA sequence and can behave very differently in the formation of condensates and maintenance of their material properties. Ideally, they should be analysed individually or in selected combinations. For the future, we will combine data from in vitro reconstitution systems and cells to address this very important point raised by the reviewer.

From the paper on the section ‘Limitations of the study’:

“Understanding condensate biology in living cells is physiological relevant but complex because the systems are heterotypic and away from equilibria. This is especially challenging for influenza A liquid inclusions that are formed by 8 different vRNP complexes, which although sharing the same structure, vary in length, valency, and RNA sequence. In addition, liquid inclusions result from an incompletely understood interactome where vRNPs engage in multiple and distinct intersegment interactions bridging cognate vRNP-Rab11 units on flexible membranes (Chou et al., 2013, Gavazzi et al., 2013, Sugita et al., 2013, Shafiuddin and Boon, 2019, Haralampiev et al., 2020, Le Sage et al., 2020). At present, we lack an in vitro reconstitution system to understand the underlying mechanism governing demixing of vRNP-Rab11a-host membranes from the cytosol. This in vitro system would be useful to explore how the different segments independently modulate the material properties of inclusions, explore if condensates are sites of IAV genome assembly, determine thermodynamic values, thresholds accurately, perform rheological measurements for viscosity and elasticity and validate our findings. The results could be compared to those obtained in cell systems to derive thermodynamic principles happening in a complex system away from equilibrium. Using cells to map how liquid inclusions respond to different perturbations provide the answer of how the system adapts in vivo, but has limitations.

Reviewer #2 (Public Review):

During Influenza virus infection, newly synthesized viral ribonucleoproteins (vRNPs) form cytosolic condensates, postulated as viral genome assembly sites and having liquid properties. vRNP accumulation in liquid viral inclusions requires its association with the cellular protein Rab11a directly via the viral polymerase subunit PB2. Etibor et al. investigate and compare the contributions of entropy, concentration, and valency/strength/type of interactions, on the properties of the vRNP condensates. For this, they subjected infected cells to the following perturbations: temperature variation (4, 37, and 42{degree sign}C), the concentration of viral inclusion drivers (vRNPs and Rab11a), and the number or strength of interactions between vRNPs using nucleozin a well-characterized vRNP sticker. Lowering the temperature (i.e. decreasing the entropic contribution) leads to a mild growth of condensates that does not significantly impact their stability. Altering the concentration of drivers of IAV inclusions impact their size but not their material properties. The most spectacular effect on condensates was observed using nucleozin. The drug dramatically stabilizes vRNP inclusions acting as a condensate hardener. Using a mouse model of influenza infection, the authors provide evidence that the activity of nucleozin is retained in vivo. Finally, using a mass spectrometry approach, they show that the drug affects vRNP solubility in a Rab11a-dependent manner without altering the host proteome profile

The data are compelling and support the idea that drugs that affect the material properties of viral condensates could constitute a new family of antiviral molecules as already described for the respiratory syncytial virus (Risso Ballester et al. Nature. 2021)

Nevertheless, there are some limitations in the study. Several of them are mentioned in a dedicated paragraph at the end of a discussion. This includes the heterogeneity of the system (vRNP of different sizes, interactions between viral and cellular partners far from being understood), which is far from equilibrium, and the absence of minimal in vitro systems that would be useful to further characterize the thermodynamic and the material properties of the condensates.

There are other ones.

We thank reviewer 2 for highlighting specific details that need improving and raising such interesting questions to validate our findings. We have addressed the comments of Reviewer 2, we performed the experiments as described (in blue) below each point raised.

1) The concentrations are mostly evaluated using antibodies. This may be correct for Cdilute. However, measurement of Cdense should be viewed with caution as the antibodies may have some difficulty accessing the inner of the condensates (as already shown in other systems), and this access may depend on some condensate properties (which may evolve along the infection). This might induce artifactual trends in some graphs (as seen in panel 2c), which could, in turn, affect the calculation of some thermodynamic parameters.

The concern of using antibodies to calculate Cdense is valid, and we thought it was very important. We addressed this concern by performing the same analyses using a fluorescent tagged virus that has mNeon Green fused to the viral polymerase PA (PA-mNeonGreen PR8 virus). Like NP, PA is a component of vRNPs and labels viral inclusions, colocalising with Rab11 when vRNPs are in the cytosol. However, per vRNP there is only one molecule of PA, whilst of NP there are 37-96 depending on the size of vRNPs. As predicted, we did observe changes in the Cdilute, Cdense and nucleation density. However, the measurements and values obtained for Gibbs free energy, size, aspect ratio detecting viral inclusions with fluorescently tagged vRNPs or antibody staining followed the same trend and allow us to validate our conclusion that major changes in Gibbs free energy occur solely when there is a change in the valency/strength of interactions but not in temperature or concentration (Figure 1 below). Given the extent of these data, we show here the results but, in the manuscript, we will describe the limitations of using antibodies in our study within the section ‘Limitations of the study’ from lines 881-894. Given the importance of the question regarding the pros and cons of the different systems for analysing thermodynamic parameters, we have decided to systematically assess and explore these differences in detail in a future manuscript.

For more information. This reviewer may be asking why we did not use the PA-fluorescent virus in the first place to evaluate inclusion thermodynamics and avoid problems in accessibility that antibodies may have to get deep into large inclusions. Our answer is that no system is perfect. In the case of the PA-fluorescent virus, the caveats revolve around the fact that the virus is attenuated (Figure 1a below), exhibiting a delayed infection as demonstrated by reduced levels of viral proteins (Figure 1b below). Consistently, it shows differences in the accumulation of vRNPs in the cytosol and viral inclusions form later in infection and the amount of vRNPs in the cytosol does not reach the levels observed in PR8-WT virus. After their emergence, inclusions behave as in the wild-type virus (PR8-WT), fusing and dividing (Figure 1c below) and displaying liquid properties.

As the overarching goal of this manuscript is to evaluate the best strategies to harden liquid IAV inclusions and given that one of the parameters we were testing is concentration, we reasoned that using PR8-WT virus for our analyses would be reasonable.

In conclusions, both systems have caveats that are important to systematically assess, and these differences may shift or alter thermodynamic parameters such as nucleation density, inclusion maturation rate, Cdense, Cdilute in particular by varying the total concentration. As a note, to validate all our results using the PA-mNeonGreen PR8 virus, we considered the delayed kinetics and applied our thermodynamic analyses up to 20 hpi rather than 16 hpi.

However, because of the question raised by this reviewer, on which is the best solution for mitigating errors induced by using antibodies, we re-checked all our data. Not only have we compared the data originated from attenuated fluorescently tagged virus with our data, but also made comparisons with images acquired from Z stacks (as used for concentration and for type/strength of interactions) with those acquired from 2D images. Our analysis revealed that there is a very good match using images acquired with Z-stacks and analysed as Z projections with between antibody staining and vRNP fluorescent virus. Therefore, we re-analysed all our thermodynamic data done with temperature using images acquired from Z stacks and altered entirely Figure 2. We believe that all these comparisons and analyses have greatly improved the manuscript and hence we thank all reviewers for their input.

Figure 1 – The PA-mNeonGreen virus is attenuated in comparison to the WT virus and data obtained is consistent for Gibbs free energy with analyses done with images processed with antibody fluorescent vRNPs. A. Representation of the PA-mNeonGreen virus (PA-mNG; Abbreviations: NCR: non coding region). B. Cells (A549) were transfected with a plasmid encoding mCherry-NP and co-infected with PA-mNeonGreen virus for 16h, at an MOI of 10. Cells were imaged under time-lapse conditions starting at 16 hpi. White boxes highlight vRNPs/viral inclusions in the cytoplasm in the individual frames. The dashed white and yellow lines mark the cell nucleus and the cell periphery, respectively. The yellow arrows indicate the fission/fusion events and movement of vRNPs/ viral inclusions. Bar = 10 µm. Bar in insets = 2 µm. C-D. Cells (A549) were infected or mock-infected with PR8 WT or PA-mNG viruses, at a multiplicity of infection (MOI) of 3, for the indicated times. C. Viral production was determined by plaque assay and plotted as plaque forming units (PFU) per milliliter (mL) ± standard error of the mean (SEM). Data are a pool from 2 independent experiments. D. The levels of viral PA, NP and M2 proteins and actin in cell lysates at the indicated time points were determined by western blotting. (E-G) Biophysical calculations in cells infected with the PA-mNeonGreen virus upon altering temperature (at 10 hpi, evaluating the concentration of vRNPs (over a time course) in conditions expressing native amounts of Rab11a or overexpressing low levels of Rab11a and upon altering the type/strength of vRNP interactions by adding nucleozin at 10 hpi during the indicated time periods. All data: Ccytoplasm/Cnucleus; Cdense, Cdilute, area aspect ratio and Gibbs free energy are represented as boxplots. Above each boxplot, same letters indicate no significant difference between them, while different letters indicate a statistical significance at α = 0.05 using one-way ANOVA, followed by Tukey multiple comparisons of means for parametric analysis, or Kruskal-Wallis Bonferroni treatment for non-parametric analysis.

2) Although the authors have demonstrated that vRNP condensates exhibit several key characteristics of liquid condensates (they fuse and divide, they dissolve upon hypotonic shock or upon incubation with 1,6-hexanediol, FRAP experiments are consistent with a liquid nature), their aspect ratio (with a median above 1.4) is much higher than the aspect ratio observed for other cellular or viral liquid compartments. This is intriguing and might be discussed.

IAV inclusions have been shown to interact with microtubules and the endoplasmic reticulum, that confers movement, and undergo fusion and fission events. We propose that these interactions and movement impose strength and deform inclusions making them less spherical. To validate this assumption, we compared the aspect ratio of viral inclusions in the absence and presence of nocodazole (that abrogates microtubule-based movement). The data in figure 2 shows that in the presence of nocodazole, the aspect ratio decreases from 1.42±0.36 to 1.26 ±0.17, supporting our assumption.

Figure 2 – Treatment with nocodazole reduces the aspect ratio of influenza A virus inclusions. Cells (A549) were infected with PR8 WT for 8 h and treated with nocodazole (10 µg/mL) for 2h, after which the movement of influenza A virus inclusions was captured by live cell imaging. Viral inclusions were segmented, and the aspect ratio measured by imageJ, analysed and plotted in R.

3) Similarly, the fusion event presented at the bottom of figure 3I is dubious. It might as well be an aggregation of condensates without fusion.

We have changed this (check Fig 5A and B in the manuscript), thank you for the suggestion.

4) The authors could have more systematically performed FRAP/FLAPh experiments on cells expressing fluorescent versions of both NP and Rab11a to investigate the influence of condensate size, time after infection, or global concentrations of Rab11a in the cell (using the total fluorescence of overexpressed GFP-Rab11a as a proxy) on condensate properties.

We have included a new figure, figure 5 with the suggested data.

Author Response

Reviewer #1 (Public Review):

This paper evaluates the effect of knocking out CST7(Cystatin 5) on the APPNL-G-F Alzheimer's disease mouse model. They found sexually dimorphic outcomes, with differential transcriptional responses, increased phagocytosis (but interestingly a higher plaque burden) in females and suppressed inflammatory microglial activation in males (but interestingly no change in plaque burden). This study offers new insight into the functional role of CST7 that is upregulated in a subset of disease- associated microglia in AD models and human brain. Despite the discovery of disease-associated microglia several years ago, there has been little effort in understanding the function of the different genes that make up this profile, making this paper especially timely. Overall, the experiments are well-controlled and the data support the main conclusions and the manuscript could be strengthened by addressing the below comments and clarifying questions that could impact the interpretation of their data/ findings.

1) In the first section discussing CST7 expression levels in AD models, it would be good to involve a discussion of levels of CST7 change in human AD samples. There are sufficient available datasets to look at this, and it would help us understand how comparable the animal models are to human patients. For example, while in mice CST7 is highly enriched in microglia/macrophages, in human datasets it seems like it is not quite so specific to microglia - it is equally expressed in endothelial cells. This might have a significant impact on the interpretation of the data, and it would be good to introduce and assess the findings in mice through the human subjects lens. There is a discussion of the human data in the discussion section, but it would be more appropriately assessed in the same way as the mouse data and comparatively presented in the results section. The authors could also include the data from Gerrits et al. 2021 in their first figure.

We agree with the reviewer on the importance of considering the work in the context of human disease. While CST7 is not as strongly upregulated in human AD brain as it is in mouse expression is observed predominantly in myeloid cells in the brain with very minimal expression detected in endothelial cells (see screenshots in Author response image 1 from Brain Myeloid Landscape platform (http://research-pub.gene.com/BrainMyeloidLandscape/BrainMyeloidLandscape2/) and is enriched in AD clusters vs homeostatic in scRNASeq studies (Gerrits et al., 2021). We attempted immunostaining for human CF (CST7) in AD brains to assess expression and co-localisation with microglial markers but failed to validate any of the antibodies tested. Additionally, King et al., 2023 (PMID: 36547260) recently showed increase in CST7 expression in bulk hippocampal RNASeq in AD vs mid-life controls suggesting an ageing/AD mechanism. CST7 has also been shown to be expressed following overexpression of TREM2 in human microglia in vitro and that siRNA-mediated knockdown of expression leads to an increase in phagocytosis (Popescu et al., 2023 - PMID: 36480007), mirroring our data and suggesting a conserved role in human cells. Overall, we believe that, even in the context of mouse models, the understanding of the function of genes upregulated in disease is of importance to the field and that this study paves the way for further work investigating human CST7 in disease. We have added this (with citations to the datasets mentioned) to the discussion (highlighted).

Author response image 1

2) The differential RNAseq data is perhaps one of the most striking results of this paper; however it is difficult to see exactly how similar the male v female APPNL-G-F profiles are, in addition to the genes shared or not between the KO condition. Venn diagrams, in addition to statistical tests, would enhance this part of the paper and add more clarity.

We have added Venn diagrams to show DEGs between male and female AppNL-G-F microglia vs WT control to show how similar the male v female APPNL-G-F profiles are. Additionally, to exemplify the Cst7KO-Sex interaction, a Venn showing DEGs between male and female AppNL-G-F microglia vs. AppNL-G-FCst7-/- microglia (Fig. 2 – Fig. supplement 3). We confirm we have derived all differential gene expression changes reported (including those represented in the Venn diagrams) using appropriate Padj statistical approaches (see Methods).

3) A major argument in the paper is a continuation of Sala-Frigerio 2019 which says that the female phenotype is an acceleration of the male phenotype. Does this mean that if males were assessed at later timepoints, they would be more similar to the females? Or are there intrinsic differences that never resolve? It would be helpful to see a later timepoint for males to get at the difference between these two options

This is an interesting question and while we acknowledge that empirically addressing with a later timepoint could add insight, we believe it would actually need multiple closely-spaced timepoints as choosing what single later timepoint would be optimal is difficult to judge (and likely not possible at all) for reasons below. We also believe data already published combined with our observations show it is most-likely a cell-intrinsic effect that explains our sex-specific differences.

First, we emphasize the acceleration of the microglial phenotype in female AppNL-G-F mice previously published is fairly subtle and relative rather than absolute e.g. the DAM/ARM microglia state represents ~50% of all microglia in male and ~55% of all microglia in females at 12 months old therefore both sexes have similarly abundant microglia in the state that most highly express Cst7. Indeed, after the age at which DAM/ARM state microglia appear in appreciable numbers (~ 6 months), both females and males both have an abundance of them. It is important to note that a 12-month male is far more “progressed” than a 6-month female hence the stepped age effect is temporally short.

Second, Cst7 deletion in the AppNL-G-F mice condition caused qualitative differences affecting distinct genes and/or overlapping genes moving in different directions between female and male mice - if a stepped age effect explained sex differences from Cst7 deletion, given that it could only be stepped by a very short timeframe (several weeks maximum) from reasoning above, we would expect to see similar qualitative changes but of different magnitude in female and male mice arising from Cst7 deletion; this is not the pattern we see.

Third, beyond 12 months old, regression from ARM/DAM actually occurs, again making it unlikely males would “catch up” with females to show the same profile from Cst7 deletion but just at an older age – practically, this also complicates choosing a single later timepoint (and age-related systemic morbidity emerges as a potential confounder as well).

In summary, while the acceleration of the DAM signature in female microglia offers an intriguing possible explanation to our observation of sexual dimorphism in response to deletion of one of the key genes in this signature, we believe it more likely that intrinsic effects are responsible for the Cst7 deletion sex-related impact. Taking the alternative perspective, even if a stepped age effect in the underlying progression of the model could explain our findings, this would need multiple timepoints with short gaps between (e.g. monthly at 12, 13, 14, 15 months old) to provide the temporal resolution to expose this pattern; we would not have the resources to conduct such a resource-intensive and lengthy study. We hope this reasoning appears logical and conscious of the importance to convey this in our manuscript we have revised the Discussion to as concisely as possible capture some key points outlined above.

4) If the central argument is that CST7 in females decreases phagocytosis and in males increases microglia activation, are there changes in amyloid plaque burden or structure in the APPNL-G-F /CST 7 KO mice compared to APPNL-G-F/CST7 WT that reflect these changes? Please address. If not, how does this affect the functional interpretation of differential expression observed in phagocytic/reactive microglia genes? Pieces of this are discussed but it could be clearer.

We emphasise the data already presented in Fig 6 and Fig. 6 – Fig. Supplement 2 showing altered Aβ burden (6E10 staining) and plaque count (MeX04) but no change in plaque area. Regarding the functional interpretation of Cst7-dependent gene changes in microglia beyond the endolysosomal function we present in figures 3-5, we have included additional data using simple immunohistochemistry, as suggested by the reviewer, to assess synapse abundance. We show loss of Sy38 coverage around plaques (Fig. 6I) and a moderate but significant decrease in coverage between AppNL-G-F/Cst7-/- vs AppNL-G-F brains only in females (Fig. 6J). This reflects the effect observed with plaque coverage whereby we observe increased burden in AppNL-G-F/Cst7-/- vs AppNL-G-F females but not males (Fig. 6B-F) suggesting the increased plaque burden in Cst7-/- female mice may lead to increased synapse loss. We would also emphasise that altered expression of phagolysosomal genes could affect disease in ways beyond interactions with amyloid and synapses.

5) It is confusing that increased phagocytosis in the APPNL-G-F/CST7 KO females leads to greater plaque burden, considering proteolysis is not affected. What might explain this observation? Additionally, it is interesting that suppression of microglial activation doesn't lead to an increase in plaques in the male APPNL-G-F/CST7 KO mice. How does the profile of phagocytic microglia in the male APPNL-G-F/CST7 KO mice differ from the APPNL-G-F males?

We emphasize our comments on this topic in the discussion where we speculate that the greater plaque burden in females is linked to increased uptake of Aβ (which we observe in Fig. 4B&C) and deposition into plaques as suggested by Huang et al., 2021 (PMID: 33859405), d’Errico et al., 2022 (PMID: 34811521) and Shabestari et al., 2022 (PMID: 35705056). Regarding the lack of effect in males despite the suppression of inflammatory genes, we agree this is a curious observation, although may point to as yet ill-defined mechanisms for how inflammatory pathways influence plaque pathology. Unfortunately, we were not able to specifically compare the profile of phagocytic microglia in AppNL-G-F vs AppNL-G-FCst7-/- as we did not perform single-cell RNASeq. However, our bulk RNASeq profiling suggests modest downregulation of phagocytic/endolysosomal genes (eg Lilrb4a, Fig. 2I) and reduced expression of LAMP2 in microglia by immunostaining. We have added further comment on this in the discussion.

6) Seems that the authors have potentially discovered an unusual mechanism for how CST7 could regulate cell autonomous function without impacting its canonical protease target. The authors deal with this extensively in the discussion but an ELISA or ICC to localize CST7 to microglia in vitro or in vitro would help address this point.

We have added FISH data localising Cst7 expression to IBA1+ cells specifically around plaques in App brains (Fig. 1B-E). We agree that assessing the subcellular localisation and any non-microglial expression of Cystatin-F (the protein coded by Cst7) would offer valuable insight into the protease target and may reveal details on the precise mechanism by which CF deletion leads the phenotype we observe in this study. However, despite attempting numerous commercially available and gifted antibodies to detect CF we were unable to validate (using Cst7-/- as controls) any methods other than FISH.

7) The authors focus on plaques in their final figure, however dysregulated microglial phagocytosis could impact many other aspects of brain health. Simple immunohistochemistry for synapses and myelin/oligodendrocytes (especially given the results of the in vitro phagocytosis assay) could provide more insight here.

We fully agree with the reviewer. As also outlined in our responses elsewhere, phagocytic changes could have multiple consequences, and we have included additional data using immunohistochemistry as advised for synapses in WT, AppNL-G-F, and AppNL-G-F/Cst7-/- brains. We show loss of Sy38 coverage around plaques (Fig. 6I) and a moderate but significant decrease in coverage between AppNL-G-F/Cst7-/- vs AppNL-G-F brains only in females (Fig. 6J). This reflects the effect observed with plaque coverage whereby we observe increased burden in AppNL-G-F/Cst7-/- vs AppNL-G-F females but not males (Fig. 6B-F) suggesting the increased plaque burden in Cst7-/- female mice may lead to increased synapse loss.

We also performed immunohistochemistry for myelin makers MAG and MBP but found no plaque-associated pathology. Finally, we searched for dystrophic neurites using LAMP1 but found that the antibody stained microglial lysosomes rather than dystrophic neurites in this model (see Author response image 2), an observation that has been made by others (Sharoar et al., 2021 - PMID: 34215298).

Overall, our data suggest Cst7 may play a protective role in females, limiting phagocytosis, reducing plaque burden and blunting synapse loss.

Author response image 2.

Reviewer #3 (Public Review):

In this manuscript, Daniels et al explored the role of Cystatin F in an A-driven mouse model of Alzheimer's disease. By crossing a constitutive knockout mouse lacking the gene that encodes Cystatin F, Cst7, to the AppNL-G-F mouse line, the authors describe impairments in microglial gene expression and phagocytic function that emerge more prominently in females versus males lacking Cst7. A strength of the study is its focus: given mounting evidence that microglia are a hub of neurological dysfunction with particular potential to trigger or exacerbate neurodegenerative disorders, it is essential to determine the changes in microglia that occur pathologically to promote disease progression. Similarly, the wide-spread identification of the gene in question, Cst7, as upregulated in AD models makes this gene a good target for mechanistic studies.

The paper in its current form also has several weaknesses which limit the insights derived, weaknesses that are largely related to the experimental tools and approaches chosen by the authors to test their hypotheses. For example, the paper begins with a figure replotting data from previous studies showing that Cst7 is upregulated in mouse models of Alzheimer's disease. Though relevant to the current study, there are no new insights provided here. Next, the authors perform bulk RNA-sequencing on microglia isolated from male and female mice in the Cst7-/-; AppNL-G-F mouse line. In the methods, it is unclear whether the authors took precautions to preserve the endogenous transcriptional state of these cells given evidence that microglia can acquire a DAM-like signature simply due to the process of dissociation (Marsh et al, Nature Neuroscience, 2022). If the authors did not control for this, their results may not support the conclusions they draw from the data. Relatedly, it appears the authors pooled all microglia together here, instead of just isolating DAMs specifically or analyzing microglia at single-cell resolution, which could reveal the heterogeneous nature of the role of Cst7 in microglia. In addition to losing information about heterogeneity, another concern is that they could be diluting out the major effects of the model on microglial function by including all microglia. Overall, the biggest issue I have with the RNA-sequencing data is the lack of validation of the gene expression changes identified using a different method that does not require dissociation, like immunohistochemistry or fluorescence in situ hybridization. Especially given the limited number of genes they found to be mis-regulated (see Fig. 2 E and G), I worry that these changes might simply be noise, especially since the authors provide no further evidence of their mis-regulation. Without further validation, the data presented are not sufficient to support the authors' claims.

We believe we have addressed this comment in the “Essential Revisions (for the authors)” section above. Please see again below:

We took standard precautions to minimise the risk of aberrant ex vivo cell activation, including maintaining cells on ice during non-enzyme steps of the procedure and carrying out preps in small batches to minimise time taken from removal of brain to purification of microglial RNA. Importantly, we also validated key expression data by in situ methods such as RNA FISH for Cst7 and Lilrb4a (Fig. 1B-E, Fig 2. - Fig. supplement 3) thus eliminating dissection-induced effects. Additionally, when performing qPCR on microglia from non-disease mice to test the disease-specific role of Cst7-dependent gene regulation we did not observe the same gene changes (Fig 2. - Fig. supplement 4) which, if such changes were dependent on tissue dissociation, we would expect to observe in WT or disease animals. We utilised the resources provided by Marsh et al. 2022 to search for overlap between enzyme-induced genes and our DEG lists from our key comparisons. We found the enzyme-induced gene set had very minimal overlap with any of our comparisons with overlap of only 4 genes between enzyme-induced genes and Cst7-dependent genes in males and no overlap between enzyme-induced genes and Cst7-dependent genes in females. We would further point out that the disease-induced microglial RNAseq profile in the AppNL-G-F Cst7+/+ (i.e. disease WT) condition mirrors those observed previously by multiple methods including in situ profiling (Zeng et al 2023 - PMID: 36732642) and RiboTag approaches (Kang et al 2018 - PMID: 30082275). We believe these combined approaches provide convincing validation of the RNAseq data.

In assessing the changes in microglial function and A pathology that occur in males and females of the Cst7-/-; AppNL-G-F line, the authors identify some differences between how females and males are affected by the loss of Cst7. While the statistical analyses the authors perform as given in the figure legends appear to be correct, the plots do not show significant changes between males and females for a given parameter. Take for example Figure 3H. Loss of Cst7 decreases IBA+Lamp+ microglia in males but increases this parameter in females. However, it does not appear that there is a significant difference in IBA+Lamp+ microglia in male versus female mice lacking Cst7. If there is no absolute difference between males and females, can the differential effects of Cst7 knockout on the sexes really be so relevant to the sexual dimorphism observed in the disease? I question this connection, but perhaps a greater discussion of what the result might mean by the authors would be helpful for placing this into context.

We understand the reviewer’s perspective and we agree that the interpretations could be presented and explained better in the text - we have updated the discussion as suggested to address this.

We designed our study initially to search for sex-specific effects of Cst7. Therefore, whilst our ANOVA does include main effects analysis for disease or sex, we carried out post-hoc analysis primarily to investigate effects of Cst7 deletion within sex. In the case of Fig. 3H pointed out by the reviewer, we observe a main effect for disease in the ANOVA and for disease-sex interaction but not for sex. Post-hoc analysis revealed the sex-specific effects of Cst7 we describe in the manuscript. This approach on analysis was also taken by Hoghooghi et al. (2020 - PMID: 33027652) who show related pathway gene Cstc is detrimental in EAE in females but not males (included in the discussion in this manuscript). The observation in Fig. 3H that there appears to be a Cst7 effect in males and females but not a sex effect in Cst7-/- is accurate but a relative anomaly in this study. Generally, we find that, alongside Cst7 deletion affecting females differently to males, we also see a sex effect in Cst7-/- animals but not in Cst7+/+ animals i.e. absolute levels in disease condition as well as relative changes from control to disease condition are different between males and females. This is exemplified in Fig. 4B&C where we observe increased microglial Aβ in female Cst7-/- animals vs male Cst7-/- animals and in Fig. 6D where we observe increased Aβ plaque burden in female Cst7-/- animals vs male Cst7-/- animals. This is most strikingly demonstrated in the case of our RNASeq data where we observe a difference in sex-dependent genes in AppNL-G-F vs AppNL-G-F/Cst7-/- (Fig. 2 – Fig. supplement 3B) implying removal of the Cst7 gene led to an ‘unlocking’ of sexual dimorphism in our cohort which we comment on in the discussion.

Finally, the use of in vitro assays of microglial function can be helpful as secondary analyses when coupled with in vivo or ex vivo approaches, but are not on their own sufficient to support the authors' conclusions. Quantitative engulfment assays (see Schafer et al, Neuron, 2012) on brain tissue showing that male and female microglia lacking Cst7 engulf different amounts of material (e.g. plaques, synapses, myelin) in the intact brain would be more convincing.

We agree that in vitro assays for microglial function are not always sufficient as standalone methods to support conclusions on functions in disease. The reviewer may have missed our in vivo MeX04 uptake assays (Fig 4A-D) which use measurements by flow cytometry on isolated microglia, this is a reflection of the microglial uptake in vivo following MeX04 injection pre-mortem – this experiment showed increased microglial Aβ in female Cst7-/- animals vs male Cst7-/- animals (Fig. 4B&C). Our in vitro assays complement and extend insight in ways not possible in vivo, for example they offer key insight into uptake/degradation kinetics that would be extremely challenging to carry out in vivo.

In general, a major limitation to the insights that can be derived in the study is the decision of the authors to perform all experiments at a single late-stage time point of 12 months of age. As this is quite far into disease progression for many AD models, phenotypic changes identified by the authors could arise due to the downstream effects of plaque deposition and therefore may not implicate Cst7 as a mechanism driving neurodegeneration rather than one of many inflammatory changes that accompany AD mouse models nearing the one-year time point. A related problem is that the study uses a constitutive KO mouse that has lacked Cst7 expression throughout life, not just during disease processes that increase with aging. In summary, the topic of the article is important and timely, but the connection between the data and the authors' conclusions is not as strong as it could be.

As described above, Cst7 expression is absent at steady-state and low until 6-12 months. Therefore, we predict that deletion would have little effect until 12+ months whereby cells expressing Cst7 have had the temporal window to affect disease pathology, as we find in the current study. This was a key part of the reasoning in our choice of the 12-month age for analyses. The negligible expression of Cst7 at baseline/early stages of disease suggests constitutive KO of the gene will not impact the phenotype until disease onset. This is substantiated by the lack of any genotype-related differences in the WT vs Cst7-/- comparisons in the non-disease condition.

Author Response:

Reviewer #1:

The paper uses a microfluidic-based method of cell volume measurement to examine single cell volume dynamics during cell spreading and osmotic shocks. The paper successfully shows that the cell volume is largely maintained during cell spreading, but small volume changes depend on the rate of cell deformation during spreading, and cell ionic homeostasis. Specifically, the major conclusion that there is a mechano-osmotic coupling between cell shape and cell osmotic regulation, I think, is correct. Moreover, the observation that fast deforming cell has a larger volume change is informative.

The authors examined a large number of conditions and variables. It's a paper rich in data and general insights. The detailed mathematical model, and specific conclusions regarding the roles of ion channels and cytoskeleton, I believe, could be improved with further considerations.

We thank the referee for the nice comment on our work and for the detailed suggestions for improving it.

Major points of consideration are below.

1) It would be very helpful if there is a discussion or validation of the FXm method accuracy. During spreading, the cell volume change is at most 10%. Is the method sufficiently accurate to consider 5-10% change? Some discussion about this would be useful for the reader.

This is an important point and we are sorry if it was not made clear in our initial manuscript. We have now made it more clear in the text (p. 4 and Figure S1E and S1F).

The important point is that the absolute accuracy of the volume measure is indeed in the 5 to 10% range, but the relative precision (repeated measures on the same cell) is much higher, rather in the 1% range, as detailed below based on experimental measures.

1) Accuracy of absolute volume measurements. The accuracy of the absolute measure of the volume depends on several parameters which can vary from one experiment to the other: the exact height of the chamber, and the biological variability form one batch of cell to another (we found that the distribution of volumes in a population of cultured cells depends strongly on the details of the culture – seeding density, substrate, etc... - which we normalized as much as possible to reduce this variability, as described in previous articles, e.g. see2). To estimate this variability overall, the simplest is to compare the average volume of the cell population in different experiments, carried out in different chambers and on different days.

Graph showing the initial average volume of cells +/- STD for 7 spreading experiments and 27 osmotic shock experiments, expressed as a % deviation from the average volume over all the experiments.

The average deviation is of 10.9 +/- 8%

2) Precision of relative volume measurements. When the same cell is imaged several times in a time-lapse experiment, as it is spreading on a substrate, or as it is swelling or shrinking during an osmotic shock, most of the variability occurring from one experiment to another does not apply. To experimentally assess the precision of the measure, we performed high time resolution (one image every 30 ms) volume measurements of 44 spread cells during 9 s. During this period of time, the volume of the cell should not change significantly, thus giving the precision of the measure.

Graph showing the coefficient of variation of the volume (STD/mean) for each individual cell (n=44) across the almost 300 frames of the movie. This shows that on average the precision of volume measurements for the same cell is 0.97±0.21%. In addition, if more precision was needed, averaging several consecutive measures can further reduce the noise, a method which is very commonly used but that we did not have to apply to our dataset.

We have included these results in the revised manuscript, since they might help the reader to estimate what can be obtained from this method of volume measurement. We also point the reviewer to previous research articles using this method and showing both population averages and time-lapse data2–8 . Another validation of our volume measurement method comes from the relative volume changes in response to osmotic shock (Ponder’s relation) measured with FXm, which gave results very similar to the numbers of previously published studies. We actually performed these experiments to validate our method, since the results are not novel.

2) The role of cell active contraction (myosin dynamics) is completely neglected. The membrane tether tension results, LatA and Y-compound results all indicate that there is a large influence of myosin contraction during cell spreading. I think most would not be surprised by this. But the model has no contribution from cortical/cytoskeletal active stress. The authors are correct that the osmotic pressure is much larger than hydraulic pressure, which is related to active contraction. But near steady state volume, the osmotic pressure difference must be equal to hydraulic pressure difference, as demanded by thermodynamics. Therefore, near equilibrium they must be close to each other in magnitude. During cell spreading, water dynamics is near equilibrium (given the magnitude of volume change), and therefore is it conceptually correct to neglect myosin active contraction? BTW, 1 solute model does not imply equal osmolarity between cytoplasm and external media. 1 solute model with active contraction was considered before, e.g., ref. 17 and Tao, et al, Biophys. J. 2015, and the steady state solution gives hydraulic pressure difference equal to osmotic pressure difference.

This is an excellent point raised by the referee. We have two types of answers for this. First an answer from an experimental point of view, which shows that acto-myosin contractility does not seem to play a direct role in the control of the cell volume, at least in the cells we used here. Based on these results we then propose a theoretical reason why this is the case. It contrasts with the view proposed in the articles mentioned by the referee for a reason which is not coming from the physical principles, with which we fully agree, but from the actual numbers, available in the literature, of the amount of the various types of osmolytes inside the cell. We give these points in more details below and we hope they will convince the referee. We also now mention them explicitly in the main text of the article (p. 6-7, Figure S3F) and in the Supplementary file with the model.

A. Experimental results

To test the effect of acto-myosin contraction on cell volume, we performed two experiments:

1) We measured the volume of same cell before and after treatment with the Rho kinase ROCK inhibitor Y-27632, which decreases cortical contractility. The experiment was performed on cells plated on poly-L-Lysin (PLL), like osmotic shock experiments, a substrate on which cells adhere, allowing the change of solution, but do not spread and remain rounded. This allowed us to evaluate the effect of the drug. Cells were plated on PLL-coated glass. The change of medium itself (with control medium) induced a change of volume of less than 2%, similar to control osmotic shock experiments (maybe due to shear stress). When the cells were treated with Y-27, the change of volume was similar to the change with the control medium (now commented in the text p. 6-7, Figure S3F). To make the analysis more complete, we distinguished the cells that remained round throughout the experiment from the cells which slightly spread, since spreading could have an effect on volume. Indeed we observed that treatment with Y-27 induced more cells to spread (Figure S3F), probably because the cortex was less tensed, allowing the adhesive forces on PLL to induce more spreading9. Nevertheless, the spreading remained rather slow and the volume change of cells treated or not with Y-27 was not significantly different. This shows that, in the absence of fast spreading induced by Y-27, the reduction of contractility per se does not have any effect on the cell volume.

Graphs showing proportion of cells that spread during the experiments (left); average relative volume of round (middle) and spread (right) control (N=3, n=77) and Y-27 treated cells (N=4, N=297).

2) To evaluate the impact of a reduction of contractility in the total absence of adhesion, we measured the average volume of control cells versus cells which have been pretreated with Y-27, plated on a non-adhesive substrate (PLL-PEG treatment). This experiment showed that the volume of the cells evolved similarly in time for both conditions, proving that contractility per se has no effect on the cell volume or cell growth, in the absence of spreading.

Graphs showing average relative volume of control (N=5, n=354) and Y-27 (N=3, n=292) treated cells plated on PLL-PEG (left); distributions of initial volume for control (middle) and Y-27 treated cells (right) represented on the left graph.

Taken together these results show that inhibition of contractility per se does not significantly affect cell volume. It thus confirms our interpretation of our results on cell spreading that reduction of contractility has an effect on cell volume, specifically in the context of cell spreading, primarily because it affects the spreading speed.

B. Theoretical interpretation

In accordance with our experiments, in our model, the effect of contractility is implicitly included in the model because it modulates the spreading dynamics, which is an input to the model, i.e. through the parameters tau_a and A_0.

We do not include the effect of contractility directly in the water transport equation because our quantitative estimates support that the contribution of the hydrostatic pressure to the volume (or the volume change) is negligible in comparison to the osmotic pressure, and this even for small variation near the steady-state volume. The main important point is that the concentration of ions inside the cell is actually much lower than outside of the cell10,11. The difference is about 100 mM and corresponds mostly to nonionic small trapped osmolytes, such as metabolites12. The osmotic pressure corresponding to this is about 10^5 Pa. Taking the cortical tension to be of order of 1 mN/m and cell size to be about ten microns we get a hydrostatic pressure difference of about 100 Pa due to cortical tension. A significant change in cell volume, of the order observed during cell spreading (let’s consider a ten percent decrease) will increase the osmotic pressure of the trapped nonionic osmolytes by 10^4 Pa (their number in the cell remaining identical). For this osmotic pressure to be balanced by an increase in the hydrostatic pressure, the cortical tension would need to increase by a factor of 100, which we consider to be unrealistic. Therefore, we find it reasonable to ignore the contribution of the hydrostatic pressure difference in the water flux equation. It is also consistent with the novel experiments presented above which show that inhibition of cortical contractility changes the cells volume below what can be detected by our measures (thus likely at maximum in the 1% range). This is now explained in the main text and Supplementary file.

Regarding our minimal model required to define cell volume, the reason why we believe one solute model is not sufficient is fundamentally the same as above: the concentration of trapped osmolytes is comparable to the total osmolarity, which means that their contribution to the total osmotic pressure cannot be discarded. Secondly, within the simplest one solute model, the pump and leak dynamics fixes in inner osmolytes concentration but does not involve the actual cell size. The most natural term that depends on the size is the Laplace pressure (inversely proportional to the cell size in a spherical cell model). But as discussed above, this term may only permit osmotic pressure differences of the order of 100 Pa, corresponding to an osmolytes concentration difference of the order of 0.1 mM. That is only a tiny fraction of the external medium osmolarity, which is about 300 mM. Such a model could thus only work for extremely fine tuning of the pump and leak rates to values with less than about 1% variation. Furthermore, such a model could not explain finite volume changes upon osmotic shocks without involving huge (100-fold) cell surface tension variations, as discussed above. For these reasons, we believe that the one-solute model is not appropriate to describe our experiments, and we feel that a trapped population of nonionic osmolytes is needed to balance the osmolarity difference created by the solute pump and leak.

In the revised version of the manuscript, we have now added a section in Supplementary file and in the main text, explaining in more detail this approximation.

3) The authors considered the role of Na, K, and Cl in the model, and used pharmacological inhibitors of NHE exchanger. I think this part of the experiments and model are somewhat weak. I am not sure the conclusions drawn are robust. First there are many ion channels/pumps in regulating Na, K and Cl. The most important of which is NaK exchanger. NHE also involves H, and this is not in the model. The ion flux expressions in the model are also problematic. The authors correctly includes voltage and concentration dependences, but used a constant active term S_i in SM eq. 3 for active pumping. I am not sure this is correct. Ion pump fluxes have been studied and proposed expressions based on experimental data exist. A study of Na, K, Cl dynamics, and membrane voltage on cell volume dynamics was published in Yellen et al, Biophys. J. 2018. In that paper, they used different expressions based on previously proposed flux expressions. It might be correct that in small concentration differences, their expressions can be linearized or approximated to achieve similar expressions as here. But this point should be considered more carefully.

We thank the reviewer for this comment. Indeed, we have not well justified our use of the NHE inhibitor EIPA. Our aim was not to directly affect the major ion pumps involved in volume regulation (which would indeed rather be the Na+/K+ exchanger), because that would likely strongly impact the initial volume of the cell and not only the volume response to spreading, making the interpretation more difficult. We based our choice on previous publication, e.g.13, showing that EIPA inhibited the main fast volume changes previously reported for cultured cells: it was shown to inhibit volume loss in spreading cells, as well as mitotic cell swelling14,15. Using EIPA, we also found that, while the initial volume was only slightly affected, the volume loss was completely abolished even in fast spreading cells (Y-27 and EIPA combined treatment, Figure S5H). This clearly proves that the volume loss behavior can be abolished, without changing the speed of spreading, which was our main aim with this experiment.

The most direct effect of inhibiting NHE exchangers is to change the cell pH16,17, which, given the low number of H protons in the cell (negligible contribution to cells osmotic pressure), cannot affect the cell volume directly. A well-studied mechanism through which proton transport can have indirect effect on cell volume is through the effect of pH on ion transporters or due to the coupling between NHE and HCO3/Cl exchanger. The latter case is well studied in the literature18. In brief, the flux of proton out of the cell through the NHE due to Na gradient leads to an outflux of HC03 and an influx of Cl. The change in Cl concentration will have an effect on the osmolarity and cell volume.

We thus performed hyperosmotic shocks with this drug and we found that, as expected, it had no effect on the immediate volume change (the Ponder’s relation), but affected the rate of volume recovery (combined with cell growth). Overall, the cells treated with EIPA showed a faster volume increase, which is what is expected if active pumping rate is reduced. This is in contrast with the above mentioned mechanism of volume regulation which will to lead to a reduced volume recovery of EIPA treated cells. This leads us to conclude that there is potentially another effect of NHE perturbation. Changing the pH will have a large impact on the functioning of many other processes, in particular, it can have an effect on ion transport16. Overall, the cells treated with EIPA showed a faster volume increase, which is what is expected if active pumping rate is reduced.

On the model side, the referee correctly points out that there are many ion transporters that are known to play a role in volume regulation which are not included in Eq. 3. In the revised manuscript we now start with a more general ion transport equation. We show that the main equation (Eq.1 - or Supplementary file Eq.13) relating volume change to tension is not affected by this generalization. This is because we consider only the linear relation between the small changes in volume and tension. We note that the generic description of the PML (Supplementary file Eqs.1-6) can be seen as general and does not require the pump and channel rates to be constant; both \Lambda_i and S_i can be a function of potential and ion concentration along with membrane tension. It is only later in the analysis that we do make the assumption that these parameters only depend on tension. This point is now made clear in the Supplementary file.

There is a huge body of work both theoretical and experimental in which the effect of different ion transporters on cell volume is analyzed. The aim of this work is not to provide an analysis of cell volume and the effect of various co-transporters but is rather limited to understanding the coupling between cell spreading, surface tension and cell volume.

To analytically estimate the sign of the mechano-osmotic coupling parameter alpha we use a minimal model. For this we indeed take the pumps and channels to be constant. As it is again a perturbative expansion around the steady state concentration, electric potential, and volume, the expression of alpha can be easily computed for a model with more general ion transporters. This generalization will come at the cost of additional parameters in the alpha expression. We decided to keep the simpler transport model, the goal of this estimate is merely to show that the sign of alpha is not a given and depends on relative values of parameters. Even for the simple model we present, the sign of alpha could be changed by varying parameters within reasonable ranges.

Given these points, and the clarification of the reasons to use EIPA in our experiments, a full mechanistic explanation of the effect of this drug is beyond the scope of this work. Because of this we are not analyzing the effect of EIPA on the model parameter alpha in detail. We now clarified our interpretation of these results in the main text of the article.

Reviewer #2:

The work by Venkova et al. addresses the role of plasma membrane tension in cell volume regulation. The authors study how different processes that exert mechanical stress on cells affect cell volume regulation, including cell spreading, cell confinement and osmotic shock experiments. They use live cell imaging, FXm (cell volume) and AFM measurements and perform a comparative approach using different cell lines. As a key result the authors find that volume regulation is associated with cell spreading rate rather than absolute spreading area. Pharmacological assays further identified Arp2/3 and NHE1 as molecular regulators of volume loss during cell spreading. The authors present a modified mechano-osmotic pump and leak model (PLM) based on the assumption of a mechanosensitive regulation of ion flux that controls cell volume.

This work presents interesting data and theoretical modelling that contribute new insight into the mechanisms of cell volume regulation.

We thank the referee for the nice comments on our work. We really appreciate the effort (s)he made to help us improve our article, including the careful inspection of the figures. We think our work is much improved thanks to his/her input.

Reviewer #3:

The study by Venkova and co-workers studies the coupling between cell volume and the osmotic balance of the cell. Of course, a lot of work as already been done on this subject, but the main specific contribution of this work is to study the fast dynamics of volume changes after several types of perturbations (osmotic shocks, cell spreading, and cell compression). The combination of volume dynamics at very high time resolution, and the robust fits obtained from an adapted Pump and Leak Model (PLM) makes the article a step-forward in our understanding of how cell volume is regulated during cell deformations. The authors clearly show that:

-The rate at which cell deforms directly impacts the volume change

-Below a certain deformation rate (either by cell spreading or external compression), the cells adapt fast enough not to change their volume. The plot dV/dt vs dA/dt shows a clear proportionality relation.

-The theoretical description of volume change dynamics with the extended PLM makes the overall conclusions very solid.

Overall the paper is very well written, contains an impressive amount of quantitative data, comparing several cell types and physiological and artificial conditions.

We thank the referee for the positive comment on our work.

My main concern about this study is related to the role of membrane tension. In the PLM model, the coupling of cell osmosis to cell deformation is made through the membrane-tension dependent activity of ion channels. While the role of ion channels is extensively tested, it brings some surprising results. Moreover, the tension is measured only at fixed time points, and the comparison to theoretical predictions is not always as convincing as expected: when comparing fig 6I and 6J, I see that predictions shows that EIPA (+ or - Y27), CK-666 (+ or - Y27) and Y27 alone should have lower tension than in the control conditions, and this is clearly not the case in fig 6J. But I would not like to emphasize too much on those discrepancies, as the drugs in the real case must have broad effects that may not be directly comparable to the theory.

We apologize for the mislabeling of the Figure 6I (now Figure 5I). This plot shows the theoretical estimate for the difference in tension (in the units of homeostatic tension) between the case when the cell loses its volume upon spreading (as observed in experiments) compared to the hypothetical situation when the cell does not lose volume upon spreading (alpha = 0). The positive value of the tension difference predicts that the cell tension would have been higher if the cell were not losing volume upon spreading, which is the case for the treatments with EIPA and CK-666 (+ Y27) and corresponds to what we found experimentally.

It thus matches our experimental observations for drug treatments which reduce or abolish the volume loss during spreading and correspond to higher tether force only at short time.

We have corrected the figure and figure legend and explained it better in the text.

But I wonder if the authors would have a better time showing that the dynamics of tension are as predicted by theory in the first place, as comparing theoretical predictions with experiments using drugs with pleiotropic effects may be hazardous.

Actually, a recent publication (https://doi.org/10.1101/2021.01.22.427801) shows that tension follows volume changes during osmotic shocks, and overall find the same dynamics of volume changes than in this manuscript. I am thus wondering if the authors could use the same technique than describe in this paper (FLIM of flipper probe) in order to study the dynamics of tension in their system, or at least refer to this paper in order to support their claim that tension is the coupling factor between volume and deformation.

As was suggested by the referee, we tried to use the FLIPPER probe. We first tried to reproduce osmotic shock experiments adding to the HeLa cells 4% of PEG400 (+~200 mOsm) or 50% of H20 (-~170 mOsm) and measuring the average probe lifetime before and after the shock. We found significantly lower probe lifetime for hyperosmotic condition compared with control, and non-significant, but slightly higher lifetime for hypoosmotic shock. The magnitude of lifetime changes was comparable with the study cited by the reviewer, but the quality of our measures did not allow us to have a better resolution. Next we measured average lifetime for control and CK-666+Y-27 treated cells 30 min and 3 h after plating, because we have highest tether force values for CK-666+Y-27 at 30 min. We did not see a change in lifetime in control cells between 30 min and 3 h (which also did not see with the tether pulling). Cells treated with CK-666+Y-27 showed a slightly lower lifetime values than control cells, but both 30 min and 3 h after plating, which means that it did not correspond to the transient effect of fast spreading but probably rather to the effect of the drugs on the measure.

Graph showing FLIPPER lifetime before and after osmotic shock for HeLa cells plated on PLL- coated substrate. Left: control (N=3, n=119) and hyperosmotic shock (N=3, n=115); Right: control (N=3, n=101) and hypoosmotic shock (N=3, n=80). p-value are obtained by t-test.

Graph showing FLIPPER lifetime for control just after the plating on PLL-coated glass (the same data for control shown at the previous graph), 30 min (control: N=3, n=88; Y-27+CK-666: N=3, n=130) and 3 h (control: N=3, n=78; Y-27+CK-666: N=3, n=142) after plating on fibronectin-coated glass. p-value are obtained by t-test.

Because the cell to cell variability might mask the trend of single cell changes in lifetime during spreading, we also tried to follow the lifetime of individual cells every 5 min along the spreading. Most illuminated cells did not spread, while cells in non-illuminated fields of view spread well, suggesting that even with an image every 5 minutes and the lowest possible illumination, the imaging was too toxic to follow cell spreading in time. We could obtain measures for a few cells, which did not show any particular trend, but their spreading was not normal. So we cannot really conclude much from these experiments.

Graph showing FLIPPER lifetime changes for 3 individual cells plated on fibronectin-coated glass (shown in blue, magenta and green) and average lifetime of cells from non-illuminated field (cyan, n=7)

Our conclusions are the following:

1) We are able to visualize some change in the lifetime of the probe for osmotic shock experiments, similar to the published results, but with a rather large cell to cell variability.

2) The spreading experiments comparing 30 minutes and 3 hours, in control or drug treated cells did not reproduce the results we observed with tether pulling, with a global effect of the drugs on the measures at both 30 min and 3 hours.

3) Following single cells in time led to too much toxicity and prevented normal spreading.

We think that this technology, which is still in its early developments, especially in terms of the microscope setting that has to be used (and we do not have it in our Institute, so we had to go on a platform in another institute with limited time to experiment), cannot be implemented in the frame of the revision of this article to provide reliable results. We thus consider that these experiments are for further development of the work and are out of the scope of this study. It would be very interesting to study in details the comparison between the oldest and more established method of tether pulling and the novel method of the FLIPPER probe, during cell spreading and in other contexts. To our knowledge this has never been done so far, so it is not in the frame of this study that we can do it. It is not clear from the literature that the two methods would measure the same thing in all conditions even if they might match in some.

Author Response

Reviewer #2 (Public Review):

In this manuscript, the authors performed single-cell RNA sequencing (scRNA-seq) analysis on bone marrow CD34+ cells from young and old healthy donors to understand the age-dependent cellular and molecular alterations during human hematopoiesis. Using a logistic regression classifier trained on young healthy donors, they identified cell-type composition changes in old donors, including an expansion of hematopoietic stem cells (HSCs) and a reduction of committed lymphoid and myeloid lineages. They also identified cell-type-specific molecular alterations between young and old donors and age-associated changes in differentiation trajectories and gene regulatory networks (GRNs). Furthermore, by comparing the single-cell atlas of normal hematopoiesis with that of myelodysplastic syndrome (MDS), they characterized cellular and molecular perturbations affecting normal hematopoiesis in MDS.

The present manuscript provides a valuable single-cell transcriptomic resource to understand normal hematopoiesis in humans and the age-dependent cellular and molecular alterations. However, their main claims are not well supported by the data presented. All results were based on computational predictions, not experimentally validated.

Major points:

1) The authors constructed a regularized logistic regression trained on young donors with manually annotated cell types and predicted cell type labels of cells from old and MDS samples. As the manual annotation of cell types was implicitly assumed as ground truth in this manuscript, I'm wondering whether the predicted cell types in old and MDS samples are consistent with the manual annotation. They should apply the same strategy used in young samples for manual annotation to old and MDS samples, and evaluate how accurate their classifier is.

We performed manual annotation for each MDS sample independently, and for the 3 healthy elderly donors integrated dataset. To do so, we performed unsupervised clustering with Seurat and annotated the clusters using the same set of canonical marker genes that we used for the young data. We then analyzed the correspondences between the annotated clusters and the predictions by GLMnet. Results are shown on Figure 1a. We observe that the biggest disagreements between methods occur between adjacent identities, such as HSC and LMPP, GMP and GMP with more prominent granulocytes profile, or MEP, early and late erythroid. When we explore these disagreements along the erythroid branch, we see that they particularly occur close to the border between subpopulations (Figure 1b). This is consistent with the continuous nature of the differentiation and the difficulty to establish boundaries between cell compartments. However, we observe that miss-labeling between different hematopoietic lineages is rare.

In addition, unsupervised clustering was not always able to directly separate the data in the expected subpopulations. We can see different clusters containing the same cell types (e.g. LMPP1, LMPP2), as well as individual clusters containing cells with different identities (e.g. pDC and monocyte progenitors). This is usually due to sources of variability different to cell identity present in the data Additional, supervised finetuning by local sub clustering and merging would be needed to correct for this. On the contrary, we believe that our GLMnet-based method focusses on gene expression related to identity, resulting in a classification that is better suited for our purpose.

Figure 1 Comparison between GLMnet predictions and manually annotated clusters A) Heatmaps showing percentages of cells in manually annotated clusters (columns) that have been assigned to each of the cell identities predicted by our GLMnet classification method (rows). The analysis was performed independently for the elderly integrated dataset and for every MDS sample. B) UMAP plots showing disagreements in classification between adjacent cell compartments in the erythroid branch. Cells from one erythroid cluster per patient are colored by the identity assigned by the GLMnet classifier. Cells in gray are not in the highlighted cluster, nor labeled as MEP, erythroid early or erythroid late by our classifier.

2) The cell-type composition changes in Figures 1 and 4 were descriptively presented without providing the statistical significance of the changes. In addition, the age-dependent cell-type composition changes should be validated by flow cytometry.

We thank the reviewer for the comment. Significance of the changes is included in Supplementary File 3. In addition, we included the percentage of several cell types we validated by flow cytometry, namely HSCs, GMPs and MEPs, in young and elderly healthy individuals in the manuscript, as Figure 1-figure supplement 3. Similarly to what we detected in our bioinformatic analyses, flow cytometry data demonstrated a significant increase in the percentage of HSCs, as well as an increasing trend in MEPs and a slight decrease in the percentage of GMPs in elderly individuals, corroborating our previous results.

3) In Figure 2, the authors used two different pseudo-time inference methods, STREAM, and Palantir. It is not clear why they used two different methods for trajectory inference. Do they provide the same differentiation trajectories? How robust are the results of trajectory inference algorithms? It seems to be inconsistent that the pseudotime inferred by STREAM was not used for downstream analysis and the new pseudotime was recalculated by using Palantir.

We thank the reviewer for the comment. The reason behind using two different methods to perform similar analyses, is that each of them provides specific outputs that can be used to perform a more robust and comprehensive analysis. STREAM allows to unravel the differentiation trajectories in a single cell dataset with an unsupervised approach. Also the visualization provided by STREAM (Figure 2C and 2D) allows for a simple interpretation of the results to the reader. On the other hand, Palantir provides a more robust analysis to dissect how gene expression dynamics interact and change with differentiation trajectories. For this reason, we decided to use this second method to investigate how specific genes were altered in the monocytic compartment.

As a resource article, the showcase of different methods can be valuable as it provides examples on how each tool can be used to obtain specific results, which can help any reader to decide which might be the best tool for their specific case.

Just to confirm that pseudotime results are similar, we perform a correlation analysis with the pseudotime values obtained from each method. We observed a correlation coefficient of 0.78 (p.val < 2.2e-16) confirming the similarity among both tools.

Figure 2. Correlation analysis of pseudotime values obtained with STREAM and PALANTIR.

4) In Figure 2D, some HSCs seem to be committed to the erythroid lineage. The authors should carefully examine whether these HSCs are genuinely HSCS, not early erythroid progenitors.

We thank the reviewer for the comment. We have performed a deep analysis regarding the classification of HSCs (See Figure 3). Our analyses reveal that none of the cells classified as HSCs express early erythroid progenitor markers. We have also used STREAM to show the expression of these markers along the obtained trajectory and observed that erythroid markers show expression in the erythroid trajectory but not in the HSC compartment (Figure 4).

Figure 3 Expression of marker genes in the HSC compartment. Dot plot depicting the normalized scaled expression of canonical marker genes by HSC of the 5 young and 3 elderly healthy donors. Marker genes are colored by the cell population they characterize. Dot color represents expression levels, and dot size represents the percentage of cells that express a gene.

Figure 4. Expression of erythroid markers in STREAM trajectories. Expression of GATA1 and HBB (erythroid markers) in the predicted differentiation trajectories.

5) It is not clear how the authors draw a conclusion from Figure 3D that the number of common targets between transcription factors is reduced. Some quantifications should be provided.

We thank the reviewer for the comment. We have updated the manuscript to better reflect our findings and emphasize that the predicted regulatory networks of HSCs in elderly donors is displayed as an independent network, compared to the young donors. (Page 6, line 36).

“Overall, we observed that the predicted regulatory network of elderly HSCs (Figure 3d) appeared as an independent network compared to the young GRN. This finding could result in the loss of co-regulatory mechanisms in the elderly donors.”

6) The constructed GRNs and related descriptions were based solely on the SCENIC analysis. By providing the results of an orthogonal prediction method for GRNs, the authors should evaluate how robust and consistent their predictions are.

We thank the reviewer for the comment regarding the method to build gene regulatory networks. As a resource article, our manuscript describes a complete workflow to perform different aspects of single cell analyses. These steps go from automated classification, trajectory inference and GRN prediction. All the selected algorithms have already been benchmarked and compared against other tools that perform similar analysis. SCENIC has already been benchmarked against other algorithms (11) and by others (12).

We do agree with the reviewer that these new predictions could provide strength to our findings, however we believe that these orthogonal predictions would better fit if our article was intended for the Research Article category instead of Tools and Resources.

7) The observed age-dependent cellular and molecular alterations in human hematopoiesis are interesting, but I'm wondering whether the observed alterations are driven by inflammatory microenvironment or intrinsic properties of a subpopulation of HSCs affected by clonal hematopoiesis (CH). To address this, the authors can perform genotyping of transcriptomes (GoT) on old healthy donors with CH. By comparing the transcriptomes of cells with and without CH mutations, we can evaluate the effects of CH on age-associated molecular alterations.

We thank the reviewer for the comment. Unfortunately, in order to perform GoT (genotyping of transcriptomes) on the healthy donors, requires modifying the standard 10x Genomics workflow to amplify the targeted locus and transcript of interest. This would require collecting new samples, optimizing the method and performing new analysis from scratch (from sequencing up to analysis). We believe this is not in the scope of the manuscript. On the other hand, we don’t have enough material to create new single cell libraries, this fact would require the addition of new donors and as a result, a complete new analysis to perform the integration.

Reviewer #3 (Public Review):

The authors have performed a transcriptional analysis of young/aged hematopoietic stem/progenitor cells which were obtained from normal individuals and those with MDS.

The authors generated an important and valuable dataset that will be of considerable benefit to the field. However, the data appear to be over-interpreted at times (for example, GSEA analysis does not have "functionality", as the authors claim). On the other hand, a comparison between normal-aged HSC and HSC from MDS patients appears to be under-explored in trying to understand how this disease (which is more common in the elderly) disrupts HSC function.

A more extensive cross-referencing of other normal HSPC/MDS HSCP datasets from aged humans would have been helpful to highlight the usefulness of the analytical tools that the authors have generated.

Major points

1) The authors detail methodology for identification of cell types from single-cell data - GLMnet. This portion of the text needs to be clarified as it is not immediately clear what it is or how it's being used. It also needs to be explained by what metric the classifier "performed better among progenitor cell types" and why this apparent advantage was sufficient to use it for the subsequent analysis. This is critical since interpretation of the data that follows depends on the validation of GLMnet as a reliable tool.

We thank the review for the comment. We have updated the corresponding section to better describe how GLMnet is used and that the reasoning on why we decided to use GLMnet as our cell type annotation method instead of other available tools such as Seurat, is based on the results of the benchmark described in Figure 1-figure supplement 1. We also described the main differences between our method and Seurat (See Answer to Review 1, Question # 4).

2) The finding of an increased number of erythroid progenitors and decreased number of myeloid cells in aged HPSC is surprising since aging is known to be associated with anemia and myeloid bias. Given that the initial validation of GLMnet is insufficiently described, this result raises concerns about the method. Along the same lines, the authors report that their tool detects a reduced frequency of monocyte progenitors. How does this finding correlate with the published data on aging humans? Is monocytopenia a feature of normal aging?

We thank the reviewer for this comment, as changes in the output of HSCs as a consequence of aging are of high interest. According to the literature, there is clear evidence of the loss of lymphoid progeny with age (13,14), which goes in agreement with our results. However, in the case of the myeloid compartment, the effects of aging are not as clear. Studies in mice have indeed observed that the loss of lymphoid cells is accompanied by increased myeloid output, starting at the level of GMPs (Rossi et al. 2005; Florian et al. 2012; Min et al. 2006). But studies on human individuals have not found changes in numbers of these myeloid progenitors (Kuranda et al. 2011; Pang et al. 2011). In addition, in the mentioned studies, myeloid production was measured exclusively by its white blood cells fraction. More recent studies have focused on the other myeloid compartments: megakaryocyte and erythroid cells. Results point towards the increase of platelet-biased HSC with age (Sanjuan-Pla et al. 2013; Grover et al. 2016) and a possible expansion of megakaryocytic and erythroid progenitor populations (Yamamoto et al. 2018; Poscablo et al. 2021; Rundberg Nilsson et al. 2016), which may represent a compensatory mechanism for the ineffective differentiation towards this lineage in elderly individuals. This goes in line with the accumulation of MEPs we see in our data. Finally, and in accordance with the reduced frequency of monocyte progenitors observed, it has been shown that with increasing age, there is a gradual decline in the monocyte count (15).

Regarding the concerns about our classification method raised by the reviewer, we have performed additional validations that we describe in answers to reviewer 1 comment #4 and reviewer 2 comment #1. To further confirm that the changes in cellular proportions we found are real, we applied two additional classification methods: Seurat transfer and Celltypist (16) to the elderly donors dataset. We obtained a similar expansion in MEPs, together with reduction of monocytic progenitors with the three methods (Figure 5).

Figure 5 Classification of HSPCs from elderly donors. Barplot showing proportions of every cell subpopulation per elderly donor, resulting from three classification methods: GLMnet-based classifier, Seurat transfer and Celltypist. For the three methods, cells with prediction scores < 0,5 were labeled as “not assigned”.

3) The use of terminology requires more clarity in order to better understand what kind of comparison has been performed, i.e. whether global transcriptional profiles are being compared, or those of specific subset populations. Also, the young/aged comparisons are often unclear, i.e. it's not evident whether the authors are referring to genes upregulated in aged HSC and downregulated in young HSC or vice versa. A more consistent data description would make the paper much easier to read.

We thank the reviewer for this comment. We have updated the manuscript to provide more clarity in the description of the different comparisons made in our analyses. Most changes are located in the Transcriptional profiling of human young and elderly hematopoietic progenitor systems sub-section within the Results.

4) The link between aging and MDS is not explored but could be an informative use of the data that the authors have generated. For example, anemia is a feature of both aging and MDS whereas neutropenia and thrombocytopenia only occur in MDS. Are there any specific pathways governing myeloid/platelet development that are only affected in MDS?

Thank you for raising this comment. We believe that discriminating events that take place during healthy aging from those associated to MDS will be helpful to understand this particular disease, as it is so closely related to age. This is why, when analyzing MDS, we have considered young and elderly donors as two separate sets of healthy controls, the eldery donors being the most suitable one for comparisons with MDS samples.

With regards to the comment on myeloid and platelet development, the GSEA analysis gives potentially useful information. MYC targets and oxidative phosphorylation are significantly enriched in the MEP compartment from MDS patients when compared to elderly donors, indicating that these progenitors may recover a more active profile with the disease. Hypoxia related genes, on the other hand, are more active in HSCs and MEPs from healthy elderly donors than in MDS. Hypoxia is known to be implicated in megakaryocyte and erythroid differentiation (17)

5) MDS is a very heterogeneous disorder and while the authors did specify that they were using samples from MDS with multilineage dysplasia, more clinical details (blood counts, cytogenetics, mutational status) are needed to be able to interpret the data.

We thank the reviewer for the comment. All the clinical details for each MDS patient are included in Supplementary File 5.

Author Response

Reviewer #3 (Public Review):

Dysbiosis has a substantial impact on host physiology. Using the nematode C. elegans and E.coli as a model of host-microbe interactions, Yang et al. defined a mechanism by which the host deals with gut dysbiosis to maintain fitness. They found that accumulation of E. coli in the intestine secreted indole, a tryptophan metabolite, and activated the transcription factor DAF-16. DAF-16 induced the expression of lys-7 and lys-8, which in turn limited E. coli proliferation in the gut of worms and maintained the longevity of worms. Finally, these authors demonstrated that indole-activated DAF-16 via TRPA-1 in neurons of worms.

This study revealed a new mechanism of host-microbe interaction. The concept of their work is of broad interest and the results they present are convincing. However, there are some issues that need to be addressed to support the conclusions.

Major issues

1) The authors isolated the crude extract from a high-performance liquid chromatograph (HPLC). A candidate compound was detected by activity-guided isolation and further identified as indole with mass spectrometry and NMR data. The HPLC fractionations and activity-guided isolation experiments should be described in more detail with a schematic figure to reveal how these experiments were performed and how indole was identified. Showing a chemical characterization of indole in Figure 2A is not sufficient for the evaluation of the results. Rather, a figure comparing the fraction 26th with standard indole by MS and NMR is more appealing.

We appreciate the concerns of the reviewer. Activity-guided isolation was performed as follows: The crude extract of E. coli supernatant metabolites was divided into 45 fractions according to polarity using Ultimate 3000 HPLC (Thermofisher, Waltham, MA) coupled with automated fraction collector. After freeze-drying each fraction, 1 mg of metabolites were dissolved in DMSO for DAF-16 nuclear localization assay in worms (Please see new Supplementary Table S2). The 26th fraction with DAF-16 nuclear translocation-inducing activity was then separated on silica gel column (200-300 mesh) with a continuous gradient of decreasing polarity (100%, 70%, 50%, 30%, petroleum ether/acetone) to yield four fractions (26a-d). Only the fraction of 26b could induce DAF-16 nuclear translocation. Then the fraction was further separated using a Sephadex LH-20 column to yield 32 fractions. The 26b-11th fraction with DAF-16 nuclear translocation-inducing activity contained a single compound identified by thin layer chromatography, mass spectrometry and nuclear magnetic resonance (NMR). The compound exhibited a quasimolecular ion peak at m/z 181.0782 [M+H]+ in the positive APCI-MS, and was assigned to a molecular formula of C8H7N. A comparison of these 1H NMR and 13C NMR spectra with the data reported in the literature revealed that the compound was indole (Yagudaev, 1986). The figure shows the comparison of the 26b-11 fraction with the standard indole by MS (Author response image 1).

Author response image 1.

High resolution mass spectrum of the candidate compound and indole.

2) DAF-16::GFP was mainly located in the cytoplasm of the intestine in worms expressing daf-16p::daf-16::gfp fed live E. coli OP50 on Day 1 (Figure 1A and 1B). The nuclear translocation of DAF-16 in the intestine was increased in worms fed live E. coli OP50 on Days 4 and 7, but not in age-matched WT worms fed heat-killed (HK) E. coli OP50 (Figure 1A and 1B). Since DAF-16 functions downstream of DAF-2, have the levels of DAF-2 been tested during aging on OP50 and (HK) OP50, or with and without indole supplementation?

In response to the reviewer’s suggestion, we carried out the RT-PCR experiment in 4-day-old and 7-day-old worms. It has been shown that DAF-2 initiates a kinase cascade that leads to the phosphorylation and cytoplasmic retention of DAF-16. By contrast, a reduction in the DAF-2 signaling leads to the dephosphorylation of DAF-16, allowing its nuclear translocation. In response to the reviewer’s suggestion, we tested the expression of daf-2 in 4-day-old and 7-day-old worms fed with OP50 and (HK) OP50. We found that the mRNA levels of daf-2 were significantly increased in worms on days 4 and 7 in the presence of either live or dead E. coli OP50, compared with those in worms on day 1 (Author response image 2A). In addition, supplementation with indole did not alter the mRNA levels of daf-2 in young adult worms (Author response image 2B). To conclude, the activation of DAF-16 is independent of DAF-2.

Author response image 2.

DAF-16 nuclear translocationisindependent of DAF-2.(A) The mRNA levelsof daf-2weregradually increasedin worms with age.P< 0.01;*P< 0.001; ns, not significant. (B)The mRNA levelsof daf-2were not alteredaftertreatment withindole for 24 hours.ns, not significant.

3) In lines 155-157, the author argued that the increase in the levels of indole in worms results from the intestinal accumulation of live E. coli OP50, rather than exogenous indole produced by E. coli OP50 on the NGM plates. However, the work also showed that supplementation with indole (50-200 μM) could significantly increase the indole levels in young adult worms on Day 1 (Figure 2-figure supplement 3B), which could induce nuclear translocation of DAF-16 in worms (Figure 2B). This result suggested that worms could take in indole from outside culturing environment. The concentration of indole in OP50 and (HK) OP50 could be measured.

We appreciate the concerns of the reviewer. Reviewer #2 also pointed out this problem. In this study, our data showed that the levels of indole were 30.9, 71.9, and 105.9 nmol/g dry weight in worms fed live E. coli OP50 on days 1, 4, and 7, respectively (Figure 2C). This increase in the levels of indole in worms was accompanied by an increase in CFU of live E. coli OP50 in the intestine of worms with age (Figure 2C). In addition, we determined the levels of indole in worms fed HK E. coli OP50, and found that the levels of indole were 28.2, 31.6, and 36.1 nmol/g dry weight in worms fed HK E. coli OP50 on days 1, 4, and 7, respectively (Figure 2-figure supplement 3A). It should be noted that the levels of indole in worms fed dead E. coli OP50 on day 1 were comparable of those in worms fed live E. coli OP50 on day 1 (30.9 vs 28.2 nmol/g dry weight). However, the levels of indole were not increased in worms fed HK E. coli OP50 on days 4 and 7. Furthermore, the observation that DAF-16 was retained in the cytoplasm of the intestine in worms fed live E. coli OP50 on day 1 (Figure 1A and 1B) also indicated that indole produced by E. coli OP50 on the NGM plates is not enough to induce DAF-16 nuclear translocation. By contrast, supplementation with indole (50-200 μM) significantly increased the indole levels in worms on day 1 (Figure 2-figure supplement 3B), which could induce nuclear translocation of DAF-16 in worms (Figure 2B). Thus, the increase in the levels of indole in worms with age results from intestinal accumulation of live E. coli OP50, rather than indole produced by E. coli OP50 on the NGM plates.

4) Recent work showed that the multicopy DAF-16 transgene acts differently from the single copy GFP knock in DAF-16 transgene. Which DAF-16 transgene was used in this work?

The strain we used is TJ356. Its genotype has been described as zIs356 [daf-16p::daf-16a/b::GFP+rol-6(su1006)] (Lee, Hench, & Ruvkun, 2001; Lin, Hsin, Libina, & Kenyon, 2001), from the Caenorhabditis Genetics Center (CGC).

5) In lines 190-193, the author argued that the supplementation with indole (100 M) inhibited the CFU of E. coli K-12 in WT worms, but not daf-16(mu86) mutants, on Days 4 and 7 (Figure 3H and 3I). These results suggest that endogenous indole is involved in maintaining a normal lifespan in worms. This is overstating. The data here more likely suggest that indole could inhibit the proliferation of E. coli through DAF-16.

We really appreciate this reviewer’s preciseness. In response to the reviewer’s suggestion, we had changed "...indole is involved in maintaining a normal lifespan in worms" to "...indole produced by bacteria in the gut could inhibit the proliferation of E. coli via DAF-16 in worms".

6) Sonowal (2017) reported that AHR mediates indole-promoted lifespan extension at 16 C. Yet this work argued that RNAi knockdown of ahr-1 did not affect the nuclear translocation of DAF-16 in worms fed E. coli K12 strain on Day 7 (Figure 4-figure supplement 1A) or young adult worms treated with indole (100 M) for 24 h. The difference between these two works should be discussed.

We really appreciate this reviewer’s preciseness. It has been shown that AHR-1 mediates indole-promoted lifespan extension in worms at 16 C (Sonowal et al., 2017). However, our data show that AHR-1 is not involved in activation of DAF-16 by indole-induced nuclear translocation of DAF-16 at 20 C. This means that AHR-1 and TRPA-1-lifespan extension by indole are essentially different. In our study, indole is added to NGM plates when worms reached the young adult stage. In the study by Sonowal et al., indole is supplemented at the stage of L1 larva. In addition, lifespan of C. elegans varies at different temperatures (Xiao et al., 2013). Thus, indole may promote lifespan extension via different mechanisms, which is dependent on exposure time and temperature.

7) Sonowal (2017) conducted mRNA profiling for worms growing on K12 and K12△tnaA. Is TRPA1 in their de-regulated gene list? Have other de-regulated genes been tested in this work?

We appreciate the concerns of the reviewer. We found that TRPA-1 is not included in the de-regulated gene list. Sonowal et al. focus on the gene expression profiles in worms from L1 larvae to young adults, whereas we pay attention to gene expression profiles in worms from young adults to aged worms. Thus, we did not test the de-regulated genes in their work.

8) How does indole activate TRPA1? In the absence of trpa1, what is the concentration of indole in worms? Since TRPA1 is a channel, is there any possibility that TRPA1 is involved in the transport of indole? It is really interesting and surprising that neuronal TRPA-1, but not intestinal TRPA-1, mediates the beneficial effect of indole. How does indole specifically activate TRPA-1 in neurons to preserve the longevity of worms?

We appreciate the concerns of the reviewer. TRPA1 is a nonselective cation channel permeable to Ca2+, Na+, and K+ (Zygmunt & Hogestatt, 2014). It is unlikely that TRPA1 is capable of transporting heterocyclic organic compounds, such as indole.

In response to the reviewer’s suggestion, we detected the content of indole in trpa-1(ok999) worms. We found that the levels of indole in trpa-1(ok999) worms were slightly increased in worms on days 4 and 7, compared to those in WT worms on days 4 and 7 (Author response image 3).

Recently, Ye et al. have demonstrated that indole and indole-3-carboxaldehyde (IAld) are agonists of TRPA1, which is conserved in vertebrates (Ye et al., 2021). Thus, it is mostly likely that indole acts as an agonist of TRPA-1 in C. elegans by directly binding to TRPA-1. One possibility is that activation of TRPA-1 in neurons by indole could induce a pathway that release a neurotransmitter, which in turn triggers a signaling pathway to extend lifespan of worms via activating DAF-16 in a non-cell autonomous manner. In contrast, the activation of TRPA-1 in the intestine by indole is unable to release such a neurotransmitter. Indeed, TRPA1 induces the releasing of calcitonin gene-related peptide in perivascular sensory nerves, leading to membrane hyperpolarization and arterial dilation on smooth muscle cells (Talavera et al., 2020). Moreover, the activation of TRPA1 by indole and IAld induces the secretion of the neurotransmitter serotonin in zebrafish (Ye et al., 2021).

Author response image 3.

The indole levels in trpa-1 mutants are increased on days 4 and 7, compared with those in WT worms. *P < 0.05.

9) How neuronal- and intestinal-specific knockdown of trpa-1 by RNAi was conducted? And what is the tissue-specific expression pattern of trap-1? Speculating how indole was transported to neuron cells is pretty appealing.

We appreciate the concerns of the reviewer. SID-1 is required cell-autonomously for systemic RNAi (Winston, Molodowitch, & Hunter, 2002). Thus, the sid-1 mutants are resistant to RNAi in the neuronal- and intestinal-specific RNAi strains, sid-1 was expressed under control of the neuronal-specific unc-119 and the intestinal-specific vha-6 promoters, respectively. Although it has been reported that TRPA-1 is expressed in neurons, muscles, hypodermal cells, and the intestine, Xiao et al. proved that only TRPA-1 expressed in the intestine and neurons contributes to life extension at low temperature (Xiao et al., 2013). The transporter of indole has not been identified. In Arabidopsis, ATP-binding cassette (ABC) transporter G family 37(ABCG37) has been reported to transport a range of indole derivatives (Ruzicka et al., 2010). However, all fifteen C. elegans ABC transporters share less than 30% sequence identity with ABCG37. Thus, it is impossible to determine which one is the transport channel for indole and indole derivatives in C. elegans.

10) Supplementation with indole only up-regulated the expression of lys-7 and lys-8 in worms subjected to intestinal-specific (Figure 7-figure supplement 2C), but not neuronal-specific, RNAi of trpa-1 (Figure 7-figure supplement 2D). If this is the case, should the addition of indole specifically induce the expression of lys-7p::gfp or lys-8p::gfp in neurons?

We really appreciate this reviewer’s preciseness. Indeed, lys-7 and lys-8 are expressed in both neurons and the intestine (Author response image 4A and 7B). However, the expression of lys-8p::gfp and lys-7p::gfp in neurons was not altered in worms after treatment with indole or knockdown of trpa-1 by RNAi (Author response image 4C and 4D).

Author response image 4.

The expression of LYS-7 and LYS-8 in neurons is not altered after treatment with indole or knockdown of trpa-1 by RNAi. (A and C) Representative images of lys-7p::gfp (A) and lys-8p::gfp (C). Both lys-7 and lys-8 could be expressed in neurons and the intestine. (B and D) Quantification of fluorescent intensity of lys-7p::gfp (B) and lys-8p::gfp (D) in neurons. These results are means ± SD of three independent experiments. ns, not significant.

11) The authors demonstrated that K-12△tnaA strain had undetectable tnaA mRNA or indole levels. Furthermore, the deletion of tnaA significantly inhibited the nuclear translocation of DAF-16 in worms. However, mutations in E. coli still have non-specific effects as there are several transposon insertions or polar mutations influencing downstream genes. The authors should demonstrate that only disruption of TnaA causes the failure of nuclear translocation of DAF-16.

In response to the reviewer’s suggestion, we rescued the expression of tnaA in the K-12 △tnaA strain. As expected, the indole level of from the supernatant in the K12 △tnaA::tnaA strain cultures was 34.1 μmol/L, which was comparable of that in the K12 strain cultures (42.5 μmol/L)（new Figure 2-figure supplement 4D). In addition, DAF-16 nuclear accumulation was increased in worms grown in the K12 △tnaA::tnaA strain on days 4 and 7 (new Figure 2-figure supplement 4E).

Author Response:

Reviewer #1 (Public Review):

In their manuscript entitled "PBN-PVT projection modulates negative emotions in mice", Zhu et al. combine circuit mapping techniques with behavioral manipulations to interrogate the function of anatomical projections from the parabrachial nucleus (PBN) to the paraventricular nucleus of the thalamus (PVT). The study addresses an important scientific question, since the PVT and particularly the posterior PVT is known to be mostly sensitive to aversive signals, but the neural circuit mechanisms underlying this process remain unknown. Here the authors contribute important evidence that PBN inputs to the PVT may be critical for this process. Specifically, the authors identify that the PVT receives glutamatergic projections from the PBN that promote aversive behavioral responses but do not modulate nociception. The latter finding is intriguing considering that the PBN is an important node in pain processing and that the PVT has recently emerged as a modulator of pain. Overall, the study includes an impressive array of techniques and manipulations and offers insight to an important scientific question. The authors' conclusions will be significantly strengthened by the inclusion of some additional experiments and controls.

It is in my view problematic that the authors used different genetic strategies to target the PBN-PVT pathway. For example, in Figure 1 the authors used Vglut2-cre mice for the anterograde tracings but later on in the same figure used constitutively expressed ChR2 in the PBN to assess functional connectivity with the PVT using ex-vivo patch-clamp electrophysiology. In Figure 2 the authors once again employed Vglut2-Cre mice to target PBN projections to the PVT and manipulate these projections optogenetically during behavioral tests. However, in the following figure (Fig. 3) the authors then use a retro-Cre approach and chemogenetics. The interchangeable use of these different manipulations is not warranted by data presented by the authors. For example it is unclear whether all PBN neurons projecting to the PVT are glutamatergic and express VGLUT2. When using the constitutively expensed ChR2 in the PBN to demonstrate glutamatergic projections to the PVT, the authors may be faced by potential contamination from adjacent brain stem structures like the LC and DRN, which project to the PVT and are known to contain glutamatergic neurons (vglut1 and vglut3, respectively). Another example, for figure 4 why did the authors not use Vglut2-cre mice and inhibited PBN terminals in the PVT as in Figure 2?

We agree with the reviewer. Now we have reframed this manuscript. We first presented the slice recording results from wild-type mice (Figure 1). We recorded both the EPSCs and IPSCs. We found that light-induced EPSCs in 34 of 52 neurons and light-induced IPSCs in 4 of 52 neurons. Please see Page 5 Line 119 to Line 121. We carefully examined the ChR2 virus infection area. Please see the following Fig R1 showcase. We found that there were dense ChR2-mCherry+ neurons in the PBN. We also observed ChR2-mCherry+ neurons in the nearby ventrolateral periaqueductal gray (VLPAG), locus coeruleus (LC), cuneiform nucleus (CnF), and laterodorsal tegmental nucleus (LDTg). And the dorsal raphe nucleus (DR) was not infected. We agreed with the reviewer that there could be potential contamination from the LC, which releases dopamine and norepinephrine to the PVT by LC-PVT projection. We have discussed this on Page 13 Line 375 to Line 380.

Figure R1. AAV-hSyn-ChR2-mCherry virus infection showcase. LPBN, lateral parabrachial nucleus. MPBN, medial parabrachial nucleus; VLPAG: ventrolateral periaqueductal gray; LC, locus coeruleus; CnF, cuneiform nucleus; LDTg, laterodorsal tegmental nucleus; DR, dorsal raphe nucleus; scp, superior cerebellar peduncle, scale bar: 200 μm.

We performed tdTomato staining with VgluT2 mRNA in situ hybridization and found that about 94.4% of tdTomato+ neurons express VgluT2 mRNA. These results indicate that the majority of PVT-projecting PBN neurons are glutamatergic. These new results have been included in Figure 1R−U.

Then we used VgluT2-ires-Cre mice to perform tracing (Figure1−figure supplement 2) and behavioral tests (optogenetic activation in Figure 2, optogenetic inhibition in Figure 4). We also performed the pharmacogenetic activation of PVT-projecting PBN neurons on wild-type mice (Figure 3). We observed that pharmacogenetic activation of the PVT-projecting PBN neurons reduced the center duration in the OFT, similar to the optogenetic activation OFT result. We also observed that pharmacogenetic activation of the PVT-projecting PBN neurons induced freezing behaviors. Our pharmacogenetic activation experiment supported the hypothesis that PBN-PVT projections modulate negative affective states.

Now we have now performed the optogenetic inhibition of the PBN-PVT projections using VgluT2-ires-Cre mice. We found that inhibition of PBN-PVT projections reduces 2-MT-induced aversion-like behaviors and footshock-induced freezing behaviors. These new results have been included in Figure 4, Figure 4−figure supplement 1 and 2, and were described in the text. Please see the text Page 9 Line 254 to Page 10 Line 274.

Related to the previous point, in the retrograde labeling experiment (Fig. 1) it would be useful if the authors determined what fraction of retrogradely label cells are indeed VGLUT2+. For behavioral experiments employing the retro-Cre approach the authors may be manipulating a heterogenous population of PBN neurons which could be influencing their behavioral observations. In general, the authors should ensure that a similar population of PBN-PVT neurons is been assessed throughout the study.

We have now performed tdTomato staining with VgluT2 mRNA in situ hybridization and found that approximately 94.4% of tdTomato+ neurons expressed VgluT2 mRNA. These results indicated that the majority of PVT-projecting PBN neurons are glutamatergic. These new results have been included in Figure 1R−U and were described in the text. Please see Page 5 Line 129 to Line 132.

The authors' grouping of the behavioral data into the first vs the last four minutes of light stimulation in the OF does not seem to be properly justified an appears rather arbitrary. Also related to data analysis, the unpaired t-test analysis in the fear conditioning experiment in Figure 4J seems inappropriate. ANOVA with group comparisons is more appropriate here.

To provide a more detailed profile of the behaviors in the OFT, we further divided the laser ON period (5−10 minutes) into five one-minute periods and analyzed the velocity, non-moving time, travel distance, center time, and jumping. We found that the velocity and non-moving time were increased, and the center time was decreased in the ChR2 mice during most periods. Furthermore, we observed that the travel distance and jumping behaviors were increased only in the first one-minute period in ChR2 mice. These new results have been included in Figure 2−figure supplement 2 and were described in the text. Please see Page 7 Line 179 to Line 189. We also discussed this on Page 14 Line 396 to Line 403.

We now performed the optogenetic inhibition of PBN-PVT projections in footshock-induced freezing behavior on Vglut2-ires-Cre mice (Figure 4J−K). And we revised the statistics (Unpaired student's t-test) and calculated the percentage of freezing behaviors in 10 minutes, which matched the constant optogenetic inhibition. Similar changes have been made in the Figure 4−figure supplement 3K.

Considering the persistency of the effect in the OF following optogenetic stimulation of PBN-PVT afferents, the lack of such persistent effect in the RTPA is hard to reconcile. By performing additional experiments the authors attempt to settle this discrepancy by proposing that the PBN-PVT pathway promotes aversion but does not facilitate negative associations. I find this conclusion to be problematic. If the pathway is critical for conveying aversive signals to the PVT, one expects that at the very least it would be require for the formation of associate memories involving aversive stimuli. However, the authors do not show data to this effect. Instead they show that animals decrease their acute defensive reactions to aversive stimuli (2-MT and fear conditioning), but do not show whether associative memory related to this experience (e.g. fear memory retrieval) is impacted by manipulations of the PBN-PVT pathway.

We have now performed several experiments to examine the effects of the PBN-PVT projections on aversion formation and memory retrieval.

We first performed a prolonged conditioned place aversion that mimics drug-induced place aversion. And we found that optogenetic activation of PBN-PVT projections did not induce aversion in the postconditioning test on Day 4. These new results have been included in Figure 2−figure supplement 2H−I and described in the text. Please see Page 7 Line 196 to Line 199.

Then, we performed the classical auditory fear conditioning test and found that optogenetic inhibition of PBN-PVT projections during footshock in the conditioning period did not affect freezing levels in contextual test or cue test (Laser OFF trials). And inhibition of PBN-PVT projections during contextual test or cue test (Laser On trials) did not affect freezing levels either. These data suggest that PBN-PVT projections are not crucial for associative fear memory formation or retrieval. These new results have been included in Figure 4−figure supplement 2 and described in the text. Please see Page 10 Line 268 to Page Line 274. We also discussed this on Page 15 Line 430 to Page 16 Line 473.

A similar lack of connection between aversive signals within the PVT and the PBN pathway is found in the photometry data presented in Figure 5. While importantly the authors' observation of aversive modulation of the pPVT reproduces data from other recent studies, the question here is whether the increased activity of PVT neurons is mediated by input from the PBN. The cFos experiment included in this figure attempts to draw this connection, but empirical evidence is required.

We have now performed the dual Fos staining experiment and the optoeletrode experiment.

In the dual Fos staining experiment, we found that there was a broad overlap between optogenetic stimulation-activated neurons (expressing the Fos protein) and footshock-activated neurons (expressing the fos mRNA) (Figure 6−figure supplement 1B−E).

In optoelectrode experiment, there was also a broad overlap between laser-activated and footshock-activated neurons. This result was consistent with the dual Fos staining result, suggesting that PVTPBN neurons were activated by aversive stimulation. Next, we analyzed the firing rates of PVT neurons during footshock with laser sweeps and footshock without laser sweeps. We found that the footshock stimulus with laser activated 30 of 40 neurons and increased the overall firing rates of 40 neurons compared with the footshock without laser result (Figure 6I). These results indicated that activation of PBN-PVT projections could enhance PVT neuronal responses to aversive stimulation.

These new results have been included in Figure 6, Figure 6−figure supplement 1, and described in the text. Please see Page 10 Line 295 to Page 11 Line 317. We also discussed these results on Page 15 Line 422 to Line 429.

Reviewer #2 (Public Review):

Zhu et al. investigated the connectivity and functional role of the projections from the parabrachial nucleus (PBN) to the paraventricular nucleus of the thalamus (PVT). Using neural tracers and in vitro electrophysiological recordings, the authors showed the existence of monosynaptic glutamatergic connections between the PBN and PVT. Further behavioral tests using optogenetic and chemogenetic approaches demonstrated that activation of the PVT-PBN circuit induces aversive and anxiety-like behaviors, whereas optogenetic inhibition of PVT-projecting PBN neurons reduces fear and aversive responses elicited by footshock or the synthetic predator odor 2MT. Next, they characterized the anatomical targets of PVT neurons that receive direct innervation from the PBN (PVTPBN). The authors also showed that PVTPBN neurons are activated by aversive stimuli and chemogenetically exciting these cells is sufficient to induce anxiety-like behaviors. While the data mostly support their conclusions, alternative interpretations and potential caveats should be addressed in the discussion.

Strength:

The authors used different behavioral tests that collectively support a role for PBN-PVT projections in promoting fear- and anxiety-like behaviors, but not nociceptive or depressive-like responses. They also provided insights into the temporal participation of the PBN-PVT circuit by showing that this pathway regulates the expression of affective states without contributing for the formation of fear-associated memories. Because previous studies have shown that activation of projection-defined PVT neurons is sufficient to induce the formation of aversive memories, the differences between the present study and previous findings reinforce the idea of functional heterogeneity within the PVT. The authors further explored this functional heterogeneity in PVT by using an anterograde viral construct to selectively label PVT neurons that are targeted by PBN inputs. Together, these results connect two important brain regions (i.e., PBN and PVT) that were known to be involved in fear and aversive responses, and provide new information to help the field to elucidate the complex networks that control emotional behaviors.

Weakness:

The authors should avoid anthropomorphizing the behavioral interpretation of the findings and generalizing their conclusions. In addition, there is a series of potential caveats that could interfere with the interpretation of the results, all of which must be discussed in the article. For example, the long protocol duration of laser stimulation, the possibility of antidromic effects following photoactivation of PBN terminals in PVT, and the existence of collateral PBN projections that could also be contributing for the observed behavioral changes. Additional clarification about the exclusive glutamatergic nature of the PBN-PVT projection should be provided and the present findings should be reconciled with prior studies showing the existence of GABAergic PBN-PVT projections.

We agree with the reviewer. Now we have revised the text carefully to avoid using subjective terms. We showed the light-induced EPSCs and IPSCs results in Figure 1, and we performed RNAscope experiments to clarify the glutamatergic nature of the PVT-projecting PBN neurons (Figure 1 and Figure1−figure supplement 1). We also added discussion about the laser stimulation protocol, the potential possibility of antidromic effects, and collateral projections. Please see Page 14 Line 413 to Page 15 Line 418, and Page 16 Line 449 to Line 457.

We also added several experiments to dissect the effect of manipulation of the PBN-PVT projection in fear memory acquisition and retrieval. These new results have been included in Figure 4−figure supplement 2 and described in the text. Please see Page 10 Line 268 to Line 274. We also discussed this on Page 15 Line 430 to Page 16 Line 473.

Reviewer #3 (Public Review):

Zhu YB et al investigated the functional role of the parabrachial nucleus (PBN) to the thalamic paraventricular nucleus (PVT) in processing negative emotions. They found that PBN send excitatory projection to PVT. The activation of PBN-PVT projection induces anxiety-like and fear-like behaviors, while inhibition of this projection relieves fear and aversion.

Strengths:

The authors dissected anatomic and functional connection between the PBN and the PVT by using comprehensive modern neuroscience techniques including viral tracing, electrophysiology, optogenetics and pharmacogenetics. They clearly demonstrated the significant role of PBN-PVT projection in modulating negative emotions.

Weaknesses:

The PBN contains a variety of neuronal subtypes that expressed distinct molecular marker such as CGRP, Tac1, Pdyn, Nts et al. The PBN also send projections to multiple targets, including VMH, PAG, BNST, CEA and ILN that could mediate distinct function. What's the neuronal identity of PVT-projecting PBN neurons, how is the PVT projection and other projections organized, are they overlapping or relative independent pathway? Those important questions were not examined in this study, which make it hard to relate this finding to other existing literature.

We have now performed the RNAscope experiments detecting VgluT2, Tac1, Tacr1, Pdyn mRNA, and fluorescent immunostaining detecting CGRP protein in the PBN. We found that about 94.4% of tdTomato+ neurons express VgluT2 mRNA. We also found that tdTomato+ neurons were only partially co-labeled with Tacr1, Tac1, or Pdyn mRNA, but not with CGRP. These results indicate that the majority of PVT-projecting PBN neurons are glutamatergic. These new results have been included in Figure 1, Figure 1−figure supplement 1, and were described in the text. Please see Page 5 Line 129 to Line 140.

We also provided the collateral projections from PVT-projecting neurons in Figure 1−figure supplement 3, Page 6 Line 148 to Line 151, and discussed on Page 16 Line 449 to Line 457.

Author Response

Reviewer #1 (Public Review):

“A sample size of 3 idiopathic seems underpowered relative to the many types of genetic changes that can occur in ASD. Since the authors carried out WGS, it would be useful to know what potential causative variants were found in these 3 individuals and even if not overlapping if they might expect to be in a similar biological pathway.

If the authors randomly selected 3 more idiopathic cell lines from individuals with autism, would these cell lines also have altered mTOR signaling? And could a line have the same cell biology defects without a change in mTOR signaling? The authors argue that the sample size could be the reason for lack of overlap of the proteomic changes (unlike the phosphor-proteomic overlaps), which makes the overlapping cell biology findings even more remarkable. Or is the phenotyping simply too crude to know if the phenotypes truly are the same?”

We appreciate these thoughtful comments and also agree that of several models, our studies indicate the possibility of mTOR alteration in multiple forms of ASD. As above, we are currently pursuing this hypothesis with newly acquired DOD support. With regard to the I-ASD population, we agree that there are a large variety of genetic changes that can occur in genetically undefined ASDs. Indeed, this is precisely why we expected to see “personalized” phenotypes in each I-ASD individual when we embarked on this study. At that time, several years ago, we had planned to expand the analyses to more I-ASD individuals to assess for additional personalized phenotypes. However, as our studies progressed, we were surprised to find convergence in our I-ASD population in terms of neurite outgrowth and migration and later proteomic results showing convergence in mTOR. We found it particularly remarkable that despite a sample size of 3 that this convergence was noted. When we had the opportunity to extend our studies to the 16p11.2 deletion population, we were thrilled to conduct the first comparison between I-ASD and a genetically defined ASD and, as such, the scope of the paper turned towards this comparison. We do agree that analyses of the other I-ASD individuals would be a beneficial endeavor, both to understand how pervasive NPC migration and neurite deficits are in autism and to assess the presence of mTOR dysregulation. Furthermore, it would be important to see whether alterations in other pathways could also lead to similar cell biological deficits, though we know that other studies of neurodevelopmental disorders have found such cellular dysregulations without reporting concurrent mTOR dysregulation. Given our current grant funding to extend these analyses, such experiments within this manuscript would not be feasible.

Regarding the phenotyping methods used, we decided to assess neurite outgrowth and migration as they are both cytoskeleton dependent processes that are critical for neurodevelopment and are often regulated by the same genes. Furthermore, similar analyses have been applied to Fragile-X Syndrome, 22q11.2 deletion syndrome, and schizophrenia NPCs (Shcheglovitov A. et al., 2013; Mor-Shaked H. et al., 2016; Urbach A. et al., 2010; Kelley D. J. et al., 2008; Doers M. E. et al., 2014; Brennand K. et al., 2015; Lee I. S. et al., 2015; Marchetto M. C. et al., 2011). As such, it seems that multiple underlying etiologies can lead to similar dysregulated cellular phenotypes that can contribute to a variety of neurodevelopmental disorders. On a more global level, there are only a few different cellular functions a developing neuron can undergo, and these include processes such as proliferation, survival, migration, and differentiation. Thus, to understand neurodevelopmental disorders, it is important to study the more “crude” or “global” cellular functions occurring during neurodevelopment to determine whether they are disrupted in disorders such as ASD. In our studies we find that there are indeed dysregulations in many of these basic developmental processes, indicating that the typical steps that occur for normal brain cytoarchitecture may be disrupted in ASD. To understand why, we then further utilized molecular studies to “zoom” in on potential mechanisms which implicated common dysregulation in mTOR signaling as one driver for these common cellular phenotypes. As suggested, we did complete WGS on all the I-ASD individuals and did not see any overlapping genetic variants between the three I-ASD individuals as mentioned in our manuscript. The genetic data was published in a larger manuscript incorporating the data (Zhou A. et al., 2023). However, there were variants that were unique to each I-ASD individual which were not seen in their unaffected family members, and it is possible these variants could be contributing to the I-ASD phenotypes. We also utilized IPA to conduct pathway analysis on the WGS data utilizing the same approach we did in analysis of p- proteome and proteome data. From WGS data, we selected high read-quality variants that were found only in I-ASD individuals and had a functional impact on protein (ie excluding synonymous variants). The enriched pathways obtained from this data were strikingly different from the pathways we found in the p-proteome analysis and are now included in supplemental Figure 6 in the manuscript. Briefly, the top 5 enriched pathways were: O-linked glycosylation, MHC class 1 signaling, Interleukin signaling, Antigen presentation, and regulation of transcription.

Reviewer #2 (Public Review):

1) I found that interpreting how differential EF sensitivity is connected to the rest of the story difficult at times. First, it is unclear why these extracellular factors were picked. These are seemingly different in nature (a neuropeptide, a growth factor and a neuromodulator) targeting largely different pathways. This limits the interpretation of the ASD subtype-specific rescue results. One way of reframing that could help is that these are pro-migratory factors instead of EFs broadly defined that fail to promote migration in I-ASD lines due to a shared malfunctioning of the intracellular migration machinery or cell-cell interactions (possibly through tight junction signaling, Fig S2A). Yet, this doesn't explain the migration/neurite phenotypes in 16p11 lines where EF sensitivity is not altered, overall implying that divergent EF sensitivity independent of underlying mTOR state. What is the proposed model that connects all three findings (divergent EF sensitivity based on ASD subtypes, 2 mTOR classes, convergent cellular phenotypes)?

We thank you for the kind assessment of our manuscript and for the thought-provoking questions posed. In terms of extracellular factors, for our study, we defined extracellular factor as any growth factor, amino acid, neurotransmitter, or neuropeptide found in the extracellular environment of the developing cells. The EFs utilized were selected due to their well-established role in regulation of early neurodevelopmental phenotypes, their expression during the “critical window” of mid-fetal development (as determined by Allan Brain Atlas), and in the case of 5-HT, its association with ASD (Abdulamir H. A. et al., 2018; Adamsen D. et al., 2014; Bonnin A. et al., 2011; Bonnin A. et al., 2007; Chen X. et al., 2015; El Marroun H. et al., 2014; Hammock E. et al., 2012; Yang C. J. et al., 2014; Dicicco-Bloom E. et al., 1998; Lu N. et al., 1998; Suh J. et al., 2001; Watanabe J. et al., 2016; Gilmore J. H. et al., 2003; Maisonpierre P. C. et al., 1990; Dincel N. et al., 2013; Levi- Montalcini R., 1987). Lastly, prior experiments in our lab with a mouse model of neurodevelopmental disorders, had shown atypical responses to EFs (IGF-1, FGF, PACAP). As such, when we first chose to use EFs in human NPCs we wanted to know 1) whether human NPCs even responded to these EFs, 2) whether EFs regulated neurite outgrowth and migration and 3) would there be a differential response in NPCs derived from those with ASD. Our studies were initiated on the I-ASD cohort and given the heterogeneity of ASD we had hypothesized we would get “personalized” neurite and migration phenotypes. Due to this reason, we also wanted to select multiple types of EFs that worked on different signaling pathways. Ultimately, instead of personalized phenotypes we found that all the I-ASD NPCs did not respond to any of the EFs tested whereas the 16p11.2 deletion NPCS did – this was therefore the only difference we found between these two “forms” of ASD. As noted, in I-ASD the lack of response to EFs can be ameliorated by modulating mTOR. However, in the 16p11.2 deletion, despite similar mTOR dysregulation as seen in I-ASD, there is no EF impairment. We do not have a cohesive model to explain why the 16pDel individuals differ from the I-ASD model other than to point to the p- proteomes which do show that the 16pDel NPCs are distinct from the I-ASD NPCs. It seems that mTOR alteration can contribute to impaired EF responsiveness in some NPCs but perhaps there is an additional defect that needs to be present in order for this defect to manifest, or that 16p11.2 deletion NPCs have specific compensatory features. For example, as noted in the thoughtful comment, the p-proteome canonical pathway analysis shows tight junction malfunction in I-ASD which is not present in the 16pDel NPCs and it could be the combination of mTOR dysregulation + dysregulated tight junction signaling that has led to lack of response to EFs in I-ASD. Regardless, we do not think the differences between two genetically distinct ASDs diminish the convergent mTOR results we have uncovered. That is, regardless of whatever defects are present in the ASD NPCs, we are able to rescue it with mTOR modulation which has fascinating implications for treatment and conceptualization for ASD. Lastly, we see our EF studies as an important inclusion as it shows that in some subtypes of ASD, lack of response to appropriate EFs could be contributing to neurodevelopmental abnormalities. Moreover, lack of response to these EFs could have implications for treatment of individuals with ASD (for example, SSRI are commonly used to treat co-morbid conditions in ASD but if an individual is unresponsive to 5- HT, perhaps this treatment is less effective). We have edited the manuscript to include an additional discussion section to address the EFs more thoroughly and have included a few extra sentences in the introduction as well!

2) A similar bidirectional migration phenotype has been described in hiSPC-derived human cortical interneurons generated from individuals with Timothy Syndrome (Birey et al 2022, Cell Stem Cell). Here, authors show that the intracellular calcium influx that is excessive in Timothy Syndrome or pharmacologically dampened in controls results in similar migration phenotypes. Authors can consider referring to this report in support of the idea that bimodal perturbations of cardinal signaling pathways can converge upon common cellular migration deficits.

We thank you for pointing out the similar migration phenotype in the Timothy Syndrome paper and have now cited it in our manuscript. We have also expanded on the concept of “too much or too little” of a particular signaling mechanism leading to common outcomes.

3) Given that authors have access to 8 I-ASD hiPSC lines, it'd very informative to assay the mTOR state (e.g. pS6 westerns) in NPCs derived from all 8 lines instead of the 3 presented, even without assessing any additional cellular phenotypes, which authors have shown to be robust and consistent. This can help the readers better get a sense of the proportion of high mTOR vs low- mTOR classes in a larger cohort.

We have already addressed this in response to reviewer 1 and the essential revisions section, providing our reasoning for not expanding the study to all 8 I-ASD individuals.

4) Does the mTOR modulation rescue EF-specific responses to migration as well (Figure 7)

We did not conduct sufficient replicates of the rescue EF specific responses to migration due to the time consuming and resource intensive nature of the neurosphere experiments. Unlike the neurite experiments, the neurosphere experiments require significantly more cells, more time, selection of neurospheres based on a size criterion, and then manual trace measurements. We did one experiment in Family-1 where we utilized MK-2206 to abolish the response of Sib NPCs to PACAP. Likewise, adding SC-79 to I-ASD-1 neurospheres allowed for response to PACAP.

Author response image 1.

Author response image 2.

Reviewer #3: Public Review

We appreciate the kind, detailed and very thorough review you provided for us!

The results on the mTOR signaling pathway as a point of convergence in these particular ASD subtypes is interesting, but the discussion should address that this has been demonstrated for other autism syndromes, and in the present manuscript, there should be some recognition that other signaling pathways are also implicated as common factors between the ASD subtypes.

With regards to the mTOR pathway, we had included the other ASD syndromes in which mTOR dysregulation has been seen including tuberous sclerosis, Cowden Syndrome, NF-1, as well as Fragile-X, Angelman, Rett and Phelan McDermid in the final paragraph of the discussion section “mTOR Signaling as a Point of Convergence in ASD”. We have now expanded our discussion to include that other signaling pathways such as MAPK, cyclins, WNT, and reelin which have also been implicated as common factors between the ASD subtypes.

The conclusions of this paper are mostly well supported by data, but for the cell migration assay, it is not clear if the authors control for initial differences in the inner cell mass area of the neurospheres in control vs ASD samples, which would affect the measurement of migration.

Thank you for this thoughtful comment! When we first started our migration data, inner cell mass size was indeed a major concern for which we controlled in our methods. First, when plating the neurospheres, we would only collect spheres when a majority of spheres were approximately a diameter of 100 um. Very large spheres often could not be imaged due to being out of focus and very small spheres would often disperse when plated. Thus, there were some constraints to the variability of inner cell mass size.

Furthermore, when we initially collected data, we conducted a proof of principal test to see if initial inner cell mass area (henceforth referred to as initial sphere size or ISS) influenced migration data. To do so, we obtained migration and ISS data from each diagnosis (Sib, NIH, I-ASD, 16pASD). Then we utilized R studio to see if there is a relationship between Migration and ISS in each diagnosis category using the equation (lm(Migration~ISS, data=bydiagnosis). In this equation, lm indicates linear modeling and (~) is a term used to ascertain the relationship between Migration and ISS and the term data=bydiagnosis allows the data to be organized by diagnosis

The results were expressed as R-squared values indicating the correlation between ISS and Migration for each diagnosis and the p-value showing statistical significance for each comparison. As shown in Author response table 1, for each data set, there is minimal correlation between Migration and ISS in each data set. Moreover, there are no statistically significant relationships between Migration and ISS indicating that initial sphere size DOES NOT influence migration data in any of our data-sets.

Author response table 1.

Lastly, utilizing R, we modeled what predicted migration would be like for Sib, NIH, I-ASD, and 16pASD if we accounted for ISS in each group. Raw migration data was then plotted against the predicted data as in Author response image 3.

Author response image 3.

As shown in the graph, there are no statistical differences between the raw migration data (the data that we actually measured in the dish) and the modeled data in which ISS is accounted for as a variable. As such, we chose not to normalize to or account for ISS in our other experiments. We have now included the above R studio analyses in our supplemental figures (Figure S1) as well.

Also, in Fig 5 and 6, panels I and J omit the effects of drug on mTOR phosphorylation as shown for other conditions.

Both SC-79 and MK2206 were selected in our experiments after thorough analysis of their effects on human epithelial cells and other cultured cells (citations in manuscript). However, initially, we did not know whether either of these drugs would modulate the mTOR pathway in human NPCs, thus, in Figures 5A,5D, 6A and 6D we chose to focus on two of our data-sets to establish the effect of these drugs in human NPCs. Our experiments in Family-1 and Family-2 showed us that SC-79 increases PS6 in human NPCs while MK-2206 downregulates it. Once this was established, we knew the drugs would have similar effects in the NPCs from the other families. Thus, we only conducted a proof of principle test to confirm the drug does indeed have the intended effect in I-ASD-3 and 16pDel. We have included these proof of principle westerns in Figure 5I, 5K, 6I and 6K to show that the effects of these drugs are reproducible across all our NPC lines. We did not include quantification since the data is only from our single proof of principle western.

Author Response

Reviewer #1 (Public Review):

Zhu et al. found that human participants could plan routes almost optimally in virtual mazes with varying complexity. They further used eye movements as a window to reveal the cognitive computations that may underly such close-to-optimal performance. Participants’ eye movement patterns included: (1) Gazes were attracted to the most task-relevant transitions (effectively the bottleneck transitions) as well as to the goal, with the share of the former increasing with maze complexity; (2) Backward sweeps (gazes moving from goal to start) and forward sweeps (gazes from start to goal) respectively dominated the pre-movement and movement periods, especially in more complex mazes. The authors explained the first pattern as the consequence of efficient strategies of information collection (i.e., active sensing) and connected the second pattern to neural replays that relate to planning.

The authors have provided a comprehensive analysis of the eye movement patterns associated with efficient navigation and route planning, which offers novel insights for the area through both their findings and methodology. Overall, the technical quality of the study is high. The "toggling" analysis, the characterization of forward and backward sweeps, and the modeling of observers with different gaze strategies are beautiful. The writing of the manuscript is also elegant.

I do not see any weaknesses that cannot be addressed by extended data analysis or modeling. The following are two major concerns that I hope could be addressed.

We thank the reviewer for their positive assessment of our work!

First, the current eye movement analysis does not seem to have touched the core of planning-evaluating alternative trajectories to the goal. Instead, planning-focused analyses such as forward and backward sweeps were all about the actually executed trajectory. What may participants’ eye movements tell us about their evaluation of alternative trajectories?

This is an important point that we previously overlooked because our experimental design did not incorporate mutually exclusive alternative trajectories. Nonetheless, there are many trials in which participants had access to several possible trajectories to the goal. Some of those alternatives may be trivially suboptimal (e.g. highly convoluted trajectory, taking a slightly curved instead of straight trajectory, or setting out on the wrong path and then turning back). Using two simple constraints described in the Methods (no cyclic paths, limited amount of overlap between alternatives), we algorithmically identified the number of non-trivial alternative trajectories (or options) on each trial that were comparable in length to the chosen trajectory (within about 1 standard deviation). A few examples are shown below for the reviewer.

The more plausible trajectory options there were, the more time participants spent gazing upon these alternatives during both pre-movement and movement (Figure 4 – figure supplement 1D – left). This is not a trivial effect resulting from the increase in surface area comprising the alternative paths because the time spent looking at the chosen trajectory also increased with the number of alternatives (Figure S8D – middle). Instead, this suggests that participants might be deliberating between comparable options.

Consistent with this, the likelihood of gazing alternative trajectories peaked early on during pre-movement and well before performing sweeping eye movements (Figure 5D). During movement, the probability of gazing upon alternatives increases immediately before participants make a turn, suggesting that certain aspects of deliberation may also be carried out on the fly just before approaching choice points. Critically, during both pre-movement and movement epochs, the fraction of time spent looking at the goal location decreased with the number of alternatives (Figure 4 – figure supplement 1D – right), revealing a potential trade-off between deliberative processing and looking at the reward location. Future studies with more structured arena designs are needed to better understand the factors that lead to the selection of a particular trajectory among alternatives, and we mention this in the discussion (line 445):

"Value-based decisions are known to involve lengthy deliberation between similar alternatives. Participants exhibited a greater tendency to deliberate between viable alternative trajectories at the expense of looking at the reward location. Likelihood of deliberation was especially high when approaching a turn, suggesting that some aspects of path planning could also be performed on the fly. More structured arena designs with carefully incorporated trajectory options could help shed light on how participants discover a near-optimal path among alternatives. However, we emphasize that deliberative processing accounted for less than onefifth of the spatial variability in eye movements, such that planning largely involved searching for a viable trajectory."

Second, what cognitive computations may underly the observed patterns of eye movements has not received a thorough theoretical treatment. In particular, to explain why participants tended to fixate the bottleneck transitions, the authors hypothesized active sensing, that is, participants were collecting extra visual information to correct their internal model about the maze. Though active sensing is a possible explanation (as demonstrated by the authors’ modeling of "smart" observers), it is not necessarily the only or most parsimonious explanation. It is possible that their peripheral vision allowed participants to form a good-enough model about the maze and their eye movements solely reflect planning. In fact, that replays occur more often at bottleneck states is an emergent property of Mattar & Daw’s (2018) normative theory of neural replay. Forward and backward replays are also emergent properties of their theory. It might be possible to explain all the eye movement patterns-fixating the goal and the bottleneck transitions, and the forward and backward replays-based on Mattar & Daw’s theory in the framework of reinforcement learning. Of course, some additional assumptions that specify eye movements and their functional roles in reinforcement learning (e.g., fixating a location is similar to staying at the corresponding state) would be needed, analogous to those in the authors’ "smart" observer models. This unifying explanation may not only be more parsimonious than the author’s active sensing plus planning account, but also be more consistent with the data than the latter. After all, if participants had used fixations to correct their internal model of the maze, they should not have had little improvements across trials in the same maze.

We thank the reviewer for this reference. We note the strong parallels between our eye movement results and that study in the discussion, in addition to proposing experimental variations that will help crystallize the link. Below, we included our response that was incorporated into the Discussion section (beginning at line 462).

"In [a] highly relevant theoretical work, Mattar and Daw proposed that path planning and structure learning are variants of the same operation, namely the spatiotemporal propagation of memory. The authors show that prioritization of reactivating memories about reward encounters and imminent choices depends upon its utility for future task performance. Through this formulation, the authors provided a normative explanation for the idiosyncrasies of forward and backward replay, the overrepresentation of reward locations and turning points in replayed trajectories, and many other experimental findings in the hippocampus literature. Given the parallels between eye movements and patterns of hippocampal activity, it is conceivable that gaze patterns can be parsimoniously explained as an outcome of such a prioritization scheme. But interpreting eye movements observed in our task in the context of the prioritization theory requires a few assumptions. First, we must assume that traversing a state space using vision yields information that has the same effect on the computation of utility as does information acquired through physical navigation. Second, peripheral vision allows participants to form a good model of the arena such that there is little need for active sensing. In other words, eye movements merely reflect memory access and have no computational role. Finally, long-term statistics of sweeps gradually evolve with exposure, similar to hippocampal replays. These assumptions can be tested in future studies by titrating the precise amount of visual information available to the participants, and by titrating their experience and characterizing gaze over longer exposures. We suspect that a pure prioritization-based account might be sufficient to explain eye movements in relatively uncluttered environments, whereas navigation in complex environments would engage mechanisms involving active inference. Developing an integrative model that features both prioritized memory-access as well as active sensing to refine the contents of memory, would facilitate further understanding of computations underlying sequential decision-making in the presence of uncertainty."

In the original manuscript, we referred to active sensing and planning in order to ground our interpretation in terminology that has been established in previous works by other groups, which had investigated them in isolation. Although the role active sensing could be limited, we are unable to conclude that eye movements solely reflect planning. Even if peripheral vision is sufficient to obtain a good-enough model of the environment, eye movements can further reduce uncertainty about the environment structure especially in cluttered environments such as the complex arena used in this study. This reduction in uncertainty is not inconsistent with a lack of performance improvement across trials. This is because the lack of improvement could be explained by a failure to consolidate the information gathered by eye movements and propagate them across trials, an interpretation that would also explain why planning duration is stable across trials (Figure 2 – figure supplement 2B). Furthermore, participants gaze at alternative trajectories more frequently when more options are presented to them. However we acknowledge that this is a fundamental question, and identified this as an important topic for follow up studies and outline experiments to delineate the precise extent to which eye movements reflect prioritized memory access vs active sensing. Briefly, we can reduce the contribution of active sensing by manipulating the amount of visual information – ranging from no information (navigating in the dark) to partial information (foveated rendering in VR headset). Likewise, we can increase the contribution of memory by manipulating the length of the experiment to ensure participants become fully familiar with the arena. Yet another manipulation is to use a fixed reward location for all trials such that experimental conditions would closely match the simulations of the prioritization model. We are excited about performing these follow up experiments.

Reviewer #2 (Public Review):

In this study the authors sought to understand how the patterns of eye-movements that occur during navigation relate to the cognitive demands of navigating the current environment. To achieve this the authors developed a set of mazes with visible layouts that varied in complexity. Participants navigated these environments seated on a chair by moving in immersive virtual reality.

The question of how eye-movements relate to cognitive demands during navigation is a central and often overlooked aspect of navigating an environment. Study eye-movements in dynamic scenarios that enable systematic analysis is technically challenging, and hence why so few studies have tackled this issue.

The major strengths of this study are the technical development of the set up for studying, recording and analysing the eye-movements. The analysis is extensive and allows greater insight than most studies exploring eye-movements would provide. The manuscript is also well written and argued.

A current weakness of the manuscript is that several other factors have not been considered that may relate to the eye-movements. More consideration of these would be important.

We thank the reviewer for their positive assessment of the innovative aspects of this study. We have tried to address the weaknesses by performing additional analyses described below.

1. In the experimental design it appears possible to separate the length of the optimal path from the complexity of the maze. But that appears not to have been done in this design. It would be useful for the authors to comment on this, as these two parameters seem critically important to the interpretation of the role of eye-movements - e.g. a lot of scanning might be required for an obvious, but long path, or a lot of scanning might be required to uncover short path through a complex maze.

This is a great point. We added a comment to the Discussion at line 489 to address this:

"Future work could focus on designing more structured arenas to experimentally separate the effects of path length, number of subgoals, and environmental complexity on participants’ eye movement patterns."

To make the most of our current design, we performed two analyses. First, we regressed trial-specific variables simultaneously against path length and arena complexity. This analysis revealed that the effect of complexity on behavior persists even after accounting for path length differences across arenas (Figure 4 – figure supplement 3). Second, path length is but one of many variables that collectively determine the complexity of the maze. Therefore, we also analyzed the effects of multiple trial-specific variables (number of turns, length of the optimal path, and the degree to which participants are expected to turn back the initial direction of heading to reach the goal, regardless of arena complexity) on eye movements. This revealed fine-grained insights on which task demands most influenced each eye movement quality that was described. More complex arenas posed, on average, greater challenges in terms of longer and more winding trajectories, such that eye movement qualities which increased with arena complexity also generally increased with specific measures of trial difficulty, albeit to varying degrees. We added additional plots to the main/supplementary figures and described these analyses under a new heading (“Linear mixed effects models”) in the Methods section.

1. Similarly, it was not clear how the number of alternative plausible paths was considered in the analysis.It seems possible to have a very complex maze with no actual required choices that would involve a lot of scanning to determine this, or a very simple maze with just two very similar choices but which would involve significant scanning to weight up which was indeed the shortest.

Thank you for the suggestion. In conjunction with our response to the first comment from Reviewer #1, we used some constraints to identify non-trivial alternative trajectories – trajectories that pass through different locations in the arena but are roughly similar in length (within about 1 SD of the chosen trajectory). In alignment with your intuition, the most complex maze, as well as the completely open arena, did not have non-trivial alternative trajectories. For the three arenas of medium complexity, the more open arenas had more non-trivial alternative trajectories.

When we analyzed the relative effect of the number of alternative trajectories on eye movement, we found that both possibilities you suggested are true. On trials with many comparable alternatives, participants indeed spend more time scanning the alternatives and less time looking at the goal (Figure S8D). Likewise, in the most complex maze where there are no alternatives, participants still spent much more time (than simpler mazes) learning about the arena structure at the expense of looking at the goal (Figure 3E-F). This analysis yielded interesting new insights into how participants solved the task and opens the door for investigating this trade-off in future work. More generally, because both deliberation and structure learning appear to drive eye movements, they must be factored into studies of human planning.

1. Can the affordances linked to turning biases and momentum explain the error patterns? For example,paths that require turning back on the current trajectory direction to reach the goal will be more likely to cause errors, and patterns of eye-movements that might be related to such errors.

Thank you for this question. In conjunction with the trial-specific analyses on the effect of the length of the trajectory (Point #1) on errors and eye movement patterns, we also looked into how the number of turns and the relative bearing (angle between the direction of initial heading and the direction of target approach) affected participants’ behavior. Turns and momentum do not affect the relative error (distance of the stopping location to the target) as much as the trajectory length does, which was unexpected (Figure 1 – figure supplement 1F). This supports that errors were primarily caused by forgetting the target location, and this memory leak gets worse with distance (or time). However, turns have an influence on eye movements in general. For example, more turns generally result in an increase in the fraction of time that participants spend gazing upon the trajectory (Figure 4 – figure supplement 1A) and sweeping (Figure 4D). Furthermore, the number of turns decreased the fraction of time participants spent gazing at the target during movement (Figure 2D).

1. Why were half the obstacle transitions miss-remembered for the blind agent? This seems a rather arbitrary choice. More information to justify this would be useful.

We tested out different percentages and found qualitatively similar results. The objective was to determine the patterns of eye movements that would be most beneficial when participants have an intermediate level of knowledge about the arena configuration (rather than near-zero or near-perfect), because during most trials, participants can also use peripheral vision to assess the rough layout, but they do not precisely remember the location of the obstacles. We added this explanation to Appendix 1, where the simulation details have been made in response to a suggestion by another reviewer.

1. The description of some of the results could usefully be explained in more simple terms at various pointsto aid readers not so familiar with the RL formation of the task. For example, a key result reported is that participants skew looking at the transition function in complex environments rather than the reward function. It would be useful to relate this to everyday scenarios, in this case broadly to looking more at the junctions in the maze than at the goal, or near the goal, when the maze is complex.

This is a great suggestion. We added an everyday analogy when describing the trade-off on line 258.

"The trade-off reported here is roughly analogous to the trade-off between looking ahead towards where you’re going and having to pay attention to signposts or traffic lights. One could get away with the former strategy while driving on rural highways whereas city streets would warrant paying attention to many other aspects of the environment to get to the destination."

1. The authors should comment on their low participant sample size. The sample seems reasonable giventhe reproducibility of the patterns, but it is much lower than most comparable virtual navigation tasks.

Thank you for the recommendation. We had some difficulties recruiting human participants who were willing to wear a headset which had been worn by other participants during COVID-19, and some participants dropped out of the study due to feeling motion sickness. To ameliorate the low sample size, we collected data on four more participants and performed analyses to confirm that the major findings may be observed in most individual participants. Participant-specific effects are included in the new plots made in response to Points # 1-3, and the number of participants with a significant result for each figure/panel has been included as Appendix 2 – table 3.

Reviewer #3 (Public Review):

In this article, Zhu and colleagues studied the role of eye movements in planning in complex environments using virtual reality technology. The main findings are that humans can 1) near optimally navigate in complex environments; 2) gaze data revealed that humans tend to look at the goal location in simple environments, but spend more time on task relevant structures in more complex tasks; 3) human participants show backward and forward sweeping mostly during planning (pre-movement) and execution (movement), respectively.

I think this is a very interesting study with a timely question and is relevant to many areas within cognitive neuroscience, notably decision making, navigation. The virtual reality technology is also quite new for studying planning. The manuscript has been written clearly. This study helps with understanding computational principles of planning. I enjoyed reading this work. I have only one major comment about statistical analyses that I hope authors can address.

We thank the reviewer for the accurate description and positive assessment of our work.

Number of subjects included in analyses in the study is only nine. This is a very small sample size for most human studies. What was the motivation behind it? I believe that most findings are quite robust, but still 9 subjects seems too low. Perhaps authors can replicate their finding in another sample? Alternatively, they might be able to provide statistics per individual and only report those that are significant in all subjects (of course, this only works if reported effects are super robust. But only in such a case 9 subjects are sufficient.)

Thank you for the suggested alternatives. Due to the pandemic, we had some difficulties recruiting human participants who were willing to wear a headset which had been worn by other participants. We collected data on four more participants and included them in the analyses, and also confirmed that the major findings are observed in most individuals. The number of participants with a significant result for each analysis has been included in Figure 1 – figure supplement 3 and Appendix 2 – table 3.

Somewhat related to the previous point, it seems to me that authors have pooled data from all subjects (basically treating them as 1 super-subject?) I am saying this based on the sentence written on page 5, line 130: "Because we are interested in principles that are conserved across subjects, we pooled subjects for all subsequent analyses." If this is not the case, please clarify that (and also add a section on "statistical analyses" in Methods.) But if this is the case, it is very problematic, because it means that statistical analyses are all done based on a fixed-effect approach. The fixed effect approach is infamous for inflated type I error.

Your interpretation is correct and we acknowledge your concern about pooling participants. We had done this after observing that our results were consistent across participants but this was not demonstrated. We have now performed analyses sensitive to participant-specific effects and find that all major results hold for most participants, and we included additional main and supplementary bar plots (and tables in Appendix 2) showing per-participant data. The new plots/table show the effect of independent variables (mainly trial/arena difficulty) on dependent variables for each participant, as well as general effects conserved across participants. A new paragraph was added to the Methods section to describe the “Linear mixed effects models” which we used.

Again, quite related to the last two points: please include degrees of freedom for every statistical test (i.e. every reported p-value).

Degrees of freedom (df) are now included along with each p-value.

Author Response

Reviewer #1 (Public Review):

Using fMRI-based univariate and multivariate analyses, Root, Muret, et al. investigated the topography of face representation in the somatosensory cortex of typically developed two-handed individuals and individuals with a congenital and acquired missing hand. They provide clear evidence for an upright face topography in the somatosensory cortex in all three groups. Moreover, they find that one-handers, but not amputees, show shorter distances from lip representations to the hand area, suggesting a remapping of the lips. They also find a shift away of the upper face from the deprived hand area in one-handers, and significantly greater dissimilarity between face part representations in amputees and one-handers. The authors argue that this pattern of remapping is different to that of cortical neighborhood theories and points toward a remapping of face parts which have the ability to compensate for hand function, e.g., using the lips/mouth to manipulate an object.

These findings provide interesting insights into the topographic organization of face parts and the principles of cortical (re)organization. The authors use several analytical approaches, including distance measures between hand- and face-part-responsive regions and representational similarity analysis (RSA). Particularly commendable is the rigorous statistical analysis, such as the use of Bayesian comparisons, and careful interpretation of absent group differences.

We thank the reviewer for their positive and constructive feedback.

Reviewer #2 (Public Review):

After amputation, the deafferented limb representation in the somatosensory cortex is activated by stimulation of other body parts. A common belief is that the lower face, including the lips, preferentially "invades" deafferented cortex due to its proximity to cortex. In the present study, this hypothesis is tested by mapping the somatosensory cortex using fMRI as amputees, congenital one-handers, and controls moved their forehead, nose, lips or tongue. First, they found that, unlike its counterpart in monkeys, the representation of the face in the somatosensory cortex is right-side up, with the forehead most medial (and abutting the hand) and the lips most lateral. Second, there was little evidence of "reorganization" of the deafferented cortex in amputees, even when tested with movements across the entire face rather than only the lips. Third, congenital one-handers showed significant reorganization of deafferented cortex, characterized principally by the invasion of the lower face, in contrast to predictions from the hypothesis that proximity was the driving factor. Fourth, there was no relationship between phantom limb pain reports and reorganization.

As a non-expert in fMRI, I cannot evaluate the methodology. That being said, I am not convinced that the current consensus is that the representation of the face in humans is flipped compared to that of monkeys. Indeed, the overwhelming majority of somatosensory homunculi I have seen for humans has the face right side up. My sense is that the fMRI studies that found an inverted (monkey-like) face representation contradict the consensus.

Thank you for point this out. As we tried to emphasise in the introduction, very few neuroimaging studies actually investigated face somatotopy in humans, with inconsistent results. We agree the default consensus tends to be dominated by the up-right depiction of Penfield’s homunculus (recently replicated by Roux et al, 2018). However, due to methodological and practical constraints, alignment across subjects in the case of intracortical recordings is usually difficult to achieve, and thus makes it difficult to assess the consistency in topographical organisation. Moreover, previous imaging studies did not manage to convincingly support Penfield’s homunculus. For these two key reasons, the spatial orientation of the human facial homunculus is still debated. A further limiting factor of previous studies in humans is that the vast majority of human studies investigating face (re)mapping in humans focused solely on the lip representation, using the cortical proximity hypothesis to interpret their results. Consequently, as we highlight above in our response to the Editor, there is a wide-spread and false representation in the human literature of the lips neighbouring the hand area.

To account for the reviewer’s critic and convey some of this context, we changed our title from: Reassessing face topography in primary somatosensory cortex and remapping following hand loss; to: Complex pattern of facial remapping in somatosensory cortex following congenital but not acquired hand loss. This was done to de-emphasise the novelty of face topography relative to our other findings.

We also rewrote our introduction (lines 79-94) as follows:

“The research focus on lip cortical remapping in amputees is based on the assumption that the lips neighbour the hand representation. However, this assumption goes against the classical upright orientation of the face in S126–30, as first depicted in Penfield’s Homunculus and in later intracortical recordings and stimulation studies26–29, with the upper-face (i.e., forehead) bordering the hand area. In contrast, neuroimaging studies in humans studying face topography provided contradictory evidence for the past 30 years. While a few neuroimaging studies provided partial evidence in support of the traditional upright face organisation31, other studies supported the inverted (or ‘upside-down’) somatotopic organisation of the face, similar to that of non-human primates32,33. Other studies suggested a segmental organisation34, or even a lack of somatotopic organisation35–37, whereas some studies provided inconclusive or incomplete results38–41. Together, the available evidence does not successfully converge on face topography in humans. In line with the upright organisation originally suggested by Penfield, recent work reported that the shift in the lip representation towards the missing hand in amputees was minimal42,43, and likely to reside within the face area itself. Surprisingly, there is currently no research that considers the representation of other facial parts, in particular the upper-face (e.g., the forehead), in relation to plasticity or PLP.”

We also updated the discussion accordingly (lines 457, 469-477, 490-492).

Similarly, it is not clear to me how the observations (1) of limited reorganization in amputees, (2) of significant reorganization in congenital one-handers, and (3) of the lack of relationship between PLP and reorganization is novel given the previous work by this group. Perhaps the authors could more clearly articulate the novelty of these results compared to their previous findings.

Thank you for giving us the opportunity to clarify on this important point. The novelty of these results can be summarised as follow:

(1) Conceptually, it is crucial for us to understand if deprivation-triggered plasticity is constrained by the local neighbourhood, because this can give us clues regarding the mechanisms driving the remapping. We provide strong topographic evidence about the face orientation in controls, amputees and one-handers.

(2) The vast majority of previous research on brain plasticity following hand loss (both congenital and acquired) in humans has exclusively focused on the lower face, and lips in particular. We provide systematic evidence for stable organisation and remapping of the neighbouring upper face, as well as the lower face. We also study topographic representation of the tongue (and nose) for the first time.

(3) The vast majority of previous research on brain remapping following hand loss (both congenital and acquired, neuroimaging and electrophysiological) was focused on univariate activity measures, such as the spatial spread of units showing a similar feature preference, or the average activity level across individual units. We are going beyond remapping by using RSA, which allows us to ask not only if new information is available in the deprived cortex (as well as the native face area), but also whether this new information is structured consistently across individuals and groups. We show that representational content is enhanced in the deprived cortex one-handers whereas it is stable in amputees relative to controls (and to their intact hand region).

(4) Based on previous studies, the assumption was that reorganisation in congenital one-handers was relatively unspecific, affecting all tested body parts. Here, we provide evidence for a more complex pattern of remapping, with the forehead representation seemingly moving out of the missing hand region (and the nose representation being tentatively similar to controls). That is, we show not just “invasion” but also a shift of the neighbour away from the hand area which has never been documented (or in fact suggested).

(5) Using Bayesian analyses we provide definitive evidence against a relationship between PLP and forehead remapping, providing first and conclusive evidence against the remapping hypothesis, based on cortical neighbourhood.

Our inclination is not to add a summary paragraph of these points in our discussion, as it feels too promotional. Instead, we have re-written large sections of the introduction and discussion to better emphasise each of these points separately throughout the text, where the context is most appropriate. Given the public review strategy taken by eLife, the novelty summary provided above will be available for any interested reader, as part of the public review process. However, should the reviewer feel that a novelty summary paragraph is required (or an emphasis on any of the points summarised above), we will be happy to revise the manuscript accordingly.

Finally, Jon Kaas and colleagues (notably Niraj Jain) have provided evidence in experiments with monkeys that much of the observed reorganization in the somatosensory cortex is inherited from plasticity in the brain stem. Jain did not find an increased propensity for axons to cross the septum between face and hand representations after (simulated) amputation. From this perspective, the relevant proximity would be that of the cuneate and trigeminal nuclei and it would be critical to map out the somatotopic organization of the trigeminal and cuneate nuclei to test hypotheses about the role of proximity in this remapping.

Thank you for highlighting this very relevant point, which we are well aware of. We fully agree with the reviewer that this is an important goal for future study, but functional imaging of the brainstem in humans is particularly challenging and would require ultra high field imaging (7T) and specialised equipment. We have encountered much local resistance due to hypothetical issues for MRI safety for scanning amputees in this higher field strength, meaning we are unable to carry out this research ourselves. Our former lab member Sanne Kikkert, who is now running her independent research programme in Zurich, has been working towards this goal for the past 4 years. So we can say with confidence that this aim is well beyond the scope of the current study. In response to your comment, we mentioned this potential mechanism in the introduction (lines 98-101), we ensured that we only referred to “cortical proximity” throughout our manuscript, and we circle back to this important point in the discussion.

Lines 539-543: “Moreover, even if the remapping we observed here goes against the theory of cortical proximity, it can still arise from representational proximity at the subcortical level, in particular at the brainstem level44,45. While challenging in humans, mapping both the cuneate and trigeminal nuclei would be critical to provide a more complete picture regarding the role of proximity in remapping.”

Reviewer #3 (Public Review):

In their study, the authors set up to challenge the long-held claim that cortical remapping in the somatosensory cortex in hand deprived cortical territories follows somatotopic proximity (the hand region gets invaded by cortical neighbors) as classically assumed. In contrast to this claim, the authors suggest that remapping may not follow cortical proximity but instead functional rules as to how the effector is used. Their data indeed suggest that the deprived hand area is not invaded by the forefront which is the cortical neighbor but instead by the lips which may compensate for hand loss in manipulating objects. Interestingly the authors suggest this is mostly the case for one-handers but not in amputees for who the reorganization seems more limited in general (but see my comments below on this last point).

This is a remarkably ambitious study that has been skilfully executed on a strong number of participants in each group. The complementarity of state-of-the-art uni- and multi-variate analyses are in the service of the research question, and the paper is clearly written. The main contribution of this paper, relative to previous studies including those of the same group, resides in the mapping of multiple face parts all at once in the three groups.

We are grateful to the reviewer for appreciating the immense effort that this study involved.

In the winner takes all approach, the authors only include 3 face parts but exclude from the analyses the nose and the thumb. I am not fully convinced by the rationale for not including nose in univariate analyses - because it does not trigger reliable activity - while keeping it for representational similarity analyses. I think it would be better to include the nose in all analyses or demonstrate this condition is indeed "noisy" and then remove it from all the analyses. Indeed, if the activity triggered by nose movement is unreliable, it should also affect multivariate.

Following this comment, we re-ran all univariate analyses to include the nose, and updated throughout the main text and supplemental results and related figures. In short, adding the nose did not change the univariate results, apart from a now significant group x hemisphere interaction for the CoG of the tongue when comparing amputees and controls, matching better the trends for greater surface coverage in the deprived hand ROI of amputees. Full details are provided in our response to Reviewer 1 above.

The rationale for not including the hand is maybe more convincing as it seems to induce activity in both controls and amputees but not in one-handers. First, it would be great to visualize this effect, at least as supplemental material to support the decision. Then, this brings the interesting possibility that enhanced invasion of hand territory by lips in one-handers might link to the possibility to observe hand-related activity in the presupposed hand region in this population. Maybe the authors may consider linking these.

Thank you for this comment. As we explain in our response to Reviewer 1 above, we did not intent the thumb condition in one-handers for analysis, as the task given to one-handers (imagine moving a body part you never had before) is inherently different to that given to the other groups (move - or at least attempt to move - your (phantom) hand). As such, we could not pursuit the analysis suggested by the reviewer here. To reduce the discrepancy and following Reviewer 1’s advice, we decided to remove the hand-face dissimilarity analysis which we included in our original manuscript, and might have sparked some of this interest. Upon reflection we agreed that this specific analysis does not directly relate to the question of remapping (but rather of shared representation), in addition to making the paper unbalanced. We will now feature this analysis in another paper that appears more appropriate in the context of referred sensations in amputees (Amoruso et al, 2022 MedRxiv).

The use of the geodesic distance between the center of gravity in the Winner Take All (WTA) maps between each movement and a predefined cortical anchor is clever. More details about how the Center Of Gravity (COG) was computed on spatially disparate regions might deserve more explanations, however.

We are happy to provide more detail on this analysis, which weights the CoG based on the clusters size (using the workbench command -metric-weighted-stats). Let’s consider the example shown here (Figure 1) for a single control participant, where each CoG is measured either without weighting (yellow vertices) or with cluster weighting (forehead CoG=red, lip CoG=dark blue, tongue CoG=dark red). When the movement produces a single cluster of activity (the lips in the non-dominant hemisphere, shown in blue), the CoG’s location was identical for both weighted (red) and unweighted (yellow) calculations. But other movements, such as the tongue (green), produced one large cluster (at the lateral end), with a few more disparate smaller clusters more medially. In this case, the larger cluster of maximal activity is weighted to a greater extent than the smaller clusters in the CoG calculation, meaning the CoG is slightly skewed towards it (dark red), relative to the smaller clusters.

Figure 1. Centre-of-gravity calculation, weighted and unweighted by cluster size, in an example control participant. Here the winner-takes-all output for each facial movement (forehead=red, lips=blue, tongue=green) was used to calculate the centre-of-gravity (CoG) at the individual-level in both the dominant (left-hand side) and non-dominant (right-hand side) hemisphere, weighted by cluster size (forehead CoG=red, lip CoG=dark blue, tongue CoG=dark red), compared to an unweighted calculation (denoted by yellow dots within each movements’ winner-takes-all output).

This is now explained in the methods (lines 760-765) as follows:

“To assess possible shifts in facial representations towards the hand area, the centre-of-gravity (CoG) of each face-winner map was calculated in each hemisphere. The CoG was weighted by cluster size meaning that in the event of multiple clusters contributing to the calculation of a single CoG for a face-winner map, the voxels in the larger cluster are overweighted relative to those in the smaller clusters. The geodesic cortical distance between each movement’s CoG and a predefined cortical anchor was computed.”

Moreover, imagine that for some reason the forefront region extends both dorsally and ventrally in a specific population (eg amputees), the COG would stay unaffected but the overlap between hand and forefront would increase. The analyses on the surface area within hand ROI for lips and forehead nicely complement the WTA analyses and suggest higher overlap for lips and lower overlap for forehead but none of the maps or graphs presented clearly show those results - maybe the authors could consider adding a figure clearly highlighting that there is indeed more lip activity IN the hand region.

We agree with you on this limitation of the CoG and this is why we interpret all cortical distances analyses in tandem with the laterality indices. The laterality indices correspond to the proportion of surface area in the hand region for a given face part in the winner-maps.

Nevertheless, to further convince the Reviewer, we extracted activity levels (beta values) within the hand region of congenitals and controls, and we ran (as for CoGs) a mixed ANOVA with the factors Hemisphere (deprived x intact) and Group (controls x one-handers).

As expected from the laterality indices obtained for the Lips, we found a significant group x hemisphere interaction (F(1,41)=4.52, p=0.040, n2p=0.099), arising from enhanced activity in the deprived hand region in one-handers compared to the non-dominant hand region in controls (t(41)=-2.674, p=0.011) and to the intact hand region in one-handers (t(41)=-3.028, p=0.004).

Since this kind of analysis was the focus of previous studies (from which we are trying to get away) and since it is redundant with the proportion of face-winner surface coverage in the hand region, we decided not to include it in the paper. But we could add it as a Supplementary result if the Reviewer believes this strengthens our interpretation.

In addition to overlap analyses between hand and other body parts, the authors may also want to consider doing some Jaccard similarity analyses between the maps of the 3 groups to support the idea that amputees are more alike controls than one-handers in their topographic activity, which again does not appear clear from the figures.

We thank the reviewers for this clever suggestion. We now include the Jaccard similarity analysis, which quantified the degree of similarity (0=no overlap between maps; 1=fully overlapping) between winner-takes-all maps (which included the nose; akin to the revised univariate results) across groups. For each face part/amputee, the similarity with the 22 controls and 21 one-handers respectively was averaged. We utilised a linear mixed model which included fixed factors of Group (One-handers x Controls), Movement (Forehead x Nose x Lips x Tongue) and Hemisphere (Intact x Deprived) on Jaccard similarity values (similar to what we used for the RSA analysis). A random effect of participant, as well as covariates of ages, were also included in the model.

Results showed a significant group x hemisphere interaction (F(240.0)=7.70, p=0.006; controlled for age; Fig. 5), indicating that amputees’ maps showed different similarity values to controls’ and one-handers’ depending on the hemisphere. Post-hoc comparisons (corrected alpha=0.025; uncorrected p-values reported) revealed significantly higher similarity to controls’ than to one-handers’ maps in the deprived hemisphere (t(240)=-3.892, p<.001). Amputees’ maps also showed higher similarity to controls’ maps in the deprived relative to the intact hemisphere (t(240)=2.991, p=0.003). Amputees, therefore, displayed greater similarity of facial somatotopy in the deprived hemisphere to controls, suggesting again fewer evidence for cortical remapping in amputees.

We added these results at the end of the univariate analyses (lines 335-351) and in the discussion (lines 464-465 and 497-500).

This brings to another concern I have related to the claim that the change in the cortical organization they observe is mostly observed in one-handers. It seems that most of this conclusion relies on the fact that some effects are observed in one-handers but not in amputees when compared to controls, however, no direct comparisons are done between amputees and one-handers so we may be in an erroneous inference about the interaction when this is actually not tested (Nieuwenhuis, 11). For instance, the shift away from the hand/face border of the forehead is also (mildly) significant in amputees (as observed more strongly in one-handers) so the conclusion (eg from the subtitle of the results section) that it is specific to one-hander might not fully be supported by the data. Similar to the invasion of the hand territory from the lips which is significant in amputees in terms of surface area. All together this calls for toning down the idea that plasticity is restricted to congenital deprivation (eg last sentence of the abstract). Even if numerically stronger, if I am not wrong, there are no stats showing remapping is indeed stronger in one-handers than in amputees and actually, amputees show significant effects when compared to controls along the lines as those shown (even if more strongly) in one-handers.

Thank you for this very important comment. We fully agree – the RSA across-groups comparison is highly informative but insufficient to support our claims. We did not compare the groups directly to avoid multiple comparisons (both for statistical reasons and to manage the size of the results section). But the reviewer’s suggestion to perform a Jaccard similarity analysis complements very nicely the univariate and multivariate results and allows for a direct (and statistically lean) comparison between groups, to assess whether amputees are more similar to controls or to congenital one-handers, taking into account all aspects of their maps (both spatial location/CoG and surface coverage). We added the Jaccard analysis to the main text, at the end of the univariate results (lines 335-385). The Jaccard analysis suggests that amputees’ maps in the deprived hemisphere were more similar to the maps of controls than to the ones of congenital one-handers. This allowed us to obtain significant statistical results to support the claim that remapping is indeed stronger in one-handers than in amputees (lines 346-351). We also compared both amputees and one-handers to the control group. In line with our univariate results, this revealed that the only face part for which controls were more similar to one-handers than to amputees was the tongue (lines 379-381). And that the forehead remapping observed at the univariate level in amputees (surface area), is likely to arise from differences in the intact hemisphere (lines 381-383).

Finally, we also added the post-hoc statistics comparing amputees to congenitals in the RSA analysis (lines 425-427): “While facial information in the deprived hand area was increased in one-handers compared with amputees, this effect did not survive our correction for multiple comparisons (t(70.7)=-2.117, p=0.038).”

Regarding the univariate results mentioned by the reviewer, we would like to emphasise that we had no significant effect for the lips in amputees, though we agree the surface area appears in between controls and one-handers. But this laterality index was not different from zero. This test is now added lines 189-190. Regarding the forehead, we fully agree with the Reviewer, and we adjusted the subtitle accordingly (lines 241-242). For consistency, we also added the t-test vs zero for the forehead surface area (non-significant, lines 251-253).

Also, maybe the authors could explore whether there is actually a link between the number of years without hand and the remapping effects.

To address this question, we explored our data using a correlation analysis. The only body part who showed some suggestive remapping effects was the tongue, and so we explored whether we could find a relationship (Pearson’s correlation) between years since amputation and the laterality index of the Tongue in amputees (r = 0.007, p=0.980, 95% CI [-0.475, 0.475]). We also explored amputees’ global Jaccard similarity values to controls in the deprived hemisphere (r = -0.010, p=0.970, 95% CI [-0.488, 0.473]), and could not find any relationship. Considering there was no strong remapping effect to explain, we find this result too exploratory to include in our manuscript.

One hypothesis generated by the data is that lips remap in the deprived hand area because lips serve compensatory functions. Actually, also in controls, lips and hands can be used to manipulate objects, in contrast to the forehead. One may thus wonder if the preferential presence of lips in the hand region is not latent even in controls as they both link in functions?

We agree with the reviewer’s reasoning, and we think that the distributed representational content we recently found in two-handers (Muret et al, 2022) provides a first hint in this direction. It is worth noting that in that previous publication we did not find differences across face parts in the activity levels obtained in the hand region, except for slightly more negative values for the tongue. But we do think that such latent information is likely to provide a “scaffolding” for remapping. While the design of our face task does not allow to assess information content for each face part (as done for the lips in Muret et al, 2022), this should be further investigated in follow-up studies.

We added a sentence in the discussion to highlight this interesting notion: Lines 556-559: “Together with the recent evidence that lip information content is already significant in the hand area of two-handed participants (Muret et al, 2022), compensatory behaviour since developmental stages might further uncover (and even potentiate) this underlying latent activity.”

Author Response

Reviewer #1 (Public Review):

The authors used data from extracellular recordings in mouse piriform cortex (PCx) by Bolding & Franks (2018), they examined the strength, timing, and coherence of gamma oscillations with respiration in awake mice. During "spontaneous" activity (i.e. without odor or light stimulation), they observed a large peak in gamma that was driven by respiration and aligned with the spiking of FBIs. TeLC, which blocks synaptic output from principal cells onto other principal cells and FBIs, abolishes gamma. Beta oscillations are evoked while gamma oscillations are induced. Odors strongly affect beta in PCx but have minimal (duration but not amplitude) effects on gamma. Unlike gamma, strong, odor-evoked beta oscillations are observed in TeLC. Using PCA, the authors found a small subset of neurons that conveyed most of the information about the odor (winner cells). Loser cells were more phase-locked to gamma, which matched the time course of inhibition. Odor decoding accuracy closely follows the time course of gamma power.

We thank the reviewer for the accurate summary of our work.

I think this is an interesting study that uses a publicly available dataset to good effect and advances the field elegantly, especially by selectively analyzing activity in identified principal neurons versus inhibitory interneurons, and by making use of defined circuit perturbations to causally test some of their hypotheses.

We thank the reviewer for the positive appraisal.

Major:

• The authors show odor-specificity at the time of the gamma peak and imply that the gamma coupling is important for odor coding. Is this because gamma oscillations are important or because gamma is strongest when activity in PCx is strongest (i.e. both excitatory and inhibitory activity, which would cancel each other in the population PSTH, which peaks earlier)? To make this claim, the authors could show that odor decoding accuracy - with a small (~10 ms sliding window) - oscillates at approx. gamma frequencies. As is, Fig. 5 just shows that cells respond at slightly different times in the sniff cycle. What time window was used for computing the Odor Specificity Index? Put another way, is it meaningful that decoding is most accurate when gamma oscillations are strongest, or is this just a reflection of total population activity, i.e., when activity is greatest there is more gamma power, and odor decoding accuracy is best?

We thank the reviewer for the critical comment. Please note that the employed decoding strategy (supervised learning with cross-validation) prevents us from quantifying a time series of decoding accuracy. Nevertheless, to overcome this difficulty, we divided the spike data (0-500 ms following the inhalation start) according to the gamma cycle into four non-overlapping gamma phase bins. Then we tested whether odor decoding accuracy varied as a function of the gamma cycle phase. Using this approach, we found that decoding depended on the gamma phase, as shown below:

(The bottom plot shows the modulation of decoding accuracy within the gamma cycle [Real MI] compared to a surrogate distribution [Surr MI, obtained by circularly shifting the gamma phases by a random amount]).

We interpret this new result as indicative that gamma influences decoding accuracy directly and that our previous result was not only a reflection of total population activity. Moreover, please note that we only use the principal cell activity for computing the odor specificity index (Fig 5E) and decoding accuracy (Fig 7B). Both peak at ~150 ms following inhalation start, at a time window where the net principal cell activity is roughly similar to baseline levels (Fig 5A bottom panel).

These new panels were added to revised Figure 7 and mentioned in the revised manuscript (page 8); we now also discuss the above considerations about maximal decoding not coinciding with the peak firing rate (page 10).

Regarding the Odor Specificity Index computation, we apologize for not describing it appropriately in the corresponding Methods subsection. We employed the same sliding time window as in the population vector correlation and the decoding analyses (i.e., 100 ms window, 62.5 % overlap). This information has been added to the revised manuscript (page 15).

• The authors say, "assembly recruitment would depend on excitatory-excitatory interactions among winner cells occurring simultaneously during gamma activity." Can the authors test this prediction by examining the TeLC recordings, in which excitatory-excitatory connections are abolished?

We thank the reviewer for the relevant comment. We followed the reviewer's suggestion and analyzed odor assemblies in TeLC recordings. Interestingly, we found a greater increase in the firing rate of winner cells in TeLC recordings (see figure below), which therefore does not support our previous interpretation that assembly recruitment would depend on excitatory-excitatory local interactions.

Thus, this new result suggests a much more critical role than we previously considered for the OB projections in determining winner neurons.

Moreover, we found significant differences in the properties of loser cells. In particular, the TeLC-infected piriform cortex showed a decreased number of losing cells, which were significantly less inhibited than their contralateral counterparts:

Furthermore, the reduced inhibition of losing cells was associated with an increased correlation of assembly weights across odors for the affected hemisphere:

Therefore, we believe these results highlight the role of gamma oscillations in segregating cell assemblies and generating a sparse orthogonal odor representation in the piriform cortex. These findings are now included as new panels of Figure 6 and discussed on page 8. Noteworthy, to conform with them, we modified our speculative sentence (page 9) "assembly recruitment would depend on excitatory-excitatory interactions among winner cells occurring simultaneously during gamma activity" to “(…) the assembly recruitment would depend on OB projections determining which winner cells “escape” gamma inhibition, highlighting the relevance of the OB-PCx interplay for olfaction (Chae et al., 2022; Otazu et al., 2015).”

• The authors show that gamma oscillations are abolished in the TeLC condition and use this to claim that gamma arises in the PCx. However, PCx neurons also project back to the OB, where they form excitatory connections onto granule cells. Fukunaga et al (2012) showed that granule cells are essential for generating gamma oscillations in the bulb. Can the authors be sure that gamma is generated in the PCx, per se, rather than generated in the bulb by centrifugal inputs from the PCx, and then inherited from the bulb by the PCx?

We thank the reviewer for the pertinent comment regarding gamma generation in the PCx. To address this point, we have performed current source density (CSD) analysis, which showed sink and sources of low-gamma oscillations within the PCx and also a phase reversal:

This result – shown as panel F in Figure 1 – suggests a local generation of gamma within the PCx. Along with the fact that PCx gamma tightly correlates with piriform FBI firing and that PCx gamma disappears in the TeLC ipsi hemisphere, which has intact OB projections, we deem it more parsimonious to assume that gamma does originate in the piriform circuit during feedback inhibition acting on principal cells and is not directly inherited from OB (though it depends on its drive). We have edited our text to incorporate the figure above panel (page 4). We now also relate our results with those of Fukunaga and colleagues for the OB gamma generation and discuss the alternative interpretation of inherited gamma (page 9).

Reviewer #2 (Public Review):

This is a very interesting paper, in which the authors describe how respiration-driven gamma oscillations in the piriform cortex are generated. Using a published data set, they find evidence for a feedback loop between local principal cells and feedback interneurons (FBIs) as the main driver of respiration-driven gamma. Interestingly, odour-evoked gamma bursts coincide with the emergence of neuronal assemblies that activate when a given odour is presented. The results argue in favour of a winner-take-all mechanism of assembly generation that has previously been suggested on theoretical grounds.

We thank the reviewer for his/her work and accurate summary of our results.

The article is well-written and the claims are justified by the data. Overall, the manuscript provides novel key insights into the generation of gamma oscillations and a potential link to the encoding of sensory input by cell assemblies. I have only minor suggestions for additional analyses that could further strengthen the manuscript:

We thank the reviewer for the positive appraisal.

1) The authors' analysis of firing rates of FFIs and FBIs combined with TeLC experiments make a compelling case for respiration-driven gamma being generated in a pyramidal cell-FBI feedback mechanism. This conclusion could be further strengthened by analyzing the gamma phase-coupling of the three neuronal populations investigated. One would expect strong coupling for FBIs but not FFIs (assuming that enough spikes of these populations could be sampled during the respiration-triggered gamma bursts). An additional analysis to strengthen this conclusion could be to extract FBI- and FFI spike-triggered gamma-filtered signals. One might expect an increase in gamma amplitude following FBI but not FFI spiking (see e.g., Pubmed ID 26890123).

We thank the reviewer for the comment. To address this point, we first computed spike-coupling strength (by means of the Mean Vector Length – MVL) for each neuronal subtype. As shown below, we did not find major differences in MVL values across subtypes (if anything, the FBIs actually displayed the lowest MVL, though it should be cautioned that this metric is sensible to sample size, which differed among subtypes):

Of note, this result also translated to spike-triggered gamma-filtered signals, with FBIs having the lowest average. We don’t however believe these findings speak against a major role of FBIs in giving rise to field gamma, since it is expected that inhibited neurons will highly phase-lock to gamma (while more active neurons during gamma would show lower phase-locking). Nevertheless, we also computed the spike-triggered gamma amplitude envelope for all three neuronal subtypes. This analysis showed that gamma envelopes closely followed FBI spikes (and not FFIs or EXC cells), and thus this new result reinforces the idea that FBIs trigger gamma oscillations. This plot is now part of an inset of Figure 1G (described on page 5).

2) The authors utilize the neurons' weight in the first PC to assign them to odour-related assemblies. This method convincingly extracts an assembly for each odour (when odours are used individually), and these seem to be virtually non-overlapping. It would be informative to test whether a similar clear separation of the individual assemblies could be achieved by running the analysis on all odours simultaneously, perhaps by employing a procedure of assembly extraction that allows to deal with overlapping assembly membership better than a pure PCA approach (as used for instance in the work cited on page 11, including the authors' previous work)? I do not doubt the validity of the authors' approach here at all, but the suggested additional analysis might allow the authors to increase their confidence that individual neurons contribute mostly to an assembly related to a single odour.

We thank the reviewer for the pertinent comment. In order to address it, we ran the ICA-based approach to detect cell assemblies (Lopes-dos-Santos et al., 2013) using the spike time series of all odors concatenated. The concatenation included time windows around the gamma peak (100-400 ms after inhalation start). We chose this window to prevent the ICA from picking temporal features of the response as different ICs instead of the spiking variations caused by the different odors. As a reference, we also calculated ICA for each odor independently during the gamma peak.

We found that the results obtained from ICA computed using concatenated data from all odors show important resemblances to those from the single ICA per odor approach. For instance, we get similar sparsity and cell assembly membership (Figure 6-figure supplement 1A), orthogonality (Figure 6-figure supplement 1B), and odor specificity (Figure 6-figure supplement 1C) in the ICs loadings through both approaches. Noteworthy, the average absolute IC correlation between the six odors (computed separately) and the six first ICs (computed from the combined odor responses) were similar across animals and showed no significant differences (Figure 6-figure supplement 1C).

We also directly tested odor selectivity and separation in the concatenated data approach by computing each odor’s mean assembly activity (i.e., “IC projection”). Regarding the former, we found that most assemblies coded for 1 or 2 odors (Figure 6-figure supplement 1D). Regarding the diversity of representations for the sampled neurons, we assessed odor separation by examining to which odor each IC is activated the most. Under this framework, we get that, on average, the first 6 ICs encode three to five different odors (Figure 6-figure supplement 1E).

We have included this result as a new Figure 6-figure supplement 1 and mention it on page 8. Of note, we have also performed all of our previous assembly analyses (i.e., Figure 6) using ICA instead of PCA to be consistent throughout the manuscript and allow the reader to compare with the new supplementary figure. This led to a new and enhanced version of Figure 6.

3) Do the authors observe a slow drift in assembly membership as predicted from previous work showing slowly changing odour responses of principal neurons (Schoonover et al., 2021)? This could perhaps be quantified by looking at the expression strengths of assemblies at individual odour presentations or by running the PCA separately on the first and last third of the odour presentations to test whether the same neurons are still 'winners'.

We thank the reviewer for calling our attention to this point. We note, however, that the representation drift observed by Schoonover et al. occurred along several days of recordings, i.e., at a much slower time scale than the single-day recordings we analyzed here (of note, Schoonover et al. observed no drift within the same day [their Fig 2a]). But irrespective of this, we believe that the data at hand does not allow for a confident analysis of possible drifts. This is because each odor was only presented ~12 times; so, further subdividing the data into subsets of only 4 trials would not render a reliable analysis, unfortunately.

4) Does the winner-take-all scenario involve the recruitment of specific sets of FBIs during the activation of the individual odour-selective assemblies? The authors could address this by testing whether the rate of FBIs changes differently with the activation of the extracted assemblies.

Within each recording session, the number of recorded FBIs is very low, on average 3.6 FBIs per recording session. Thus, unfortunately such interesting analysis cannot be confidently performed.

5) Given the dependence on local gamma oscillations, one might expect that odour-selective assemblies do not emerge in the TeLC-expressing hemisphere. This could be directly tested in the existing data set.

We are thankful for the comment. We followed the reviewer's suggestion and analyzed odor assemblies in TeLC recordings, comparing the ipsilateral hemisphere (infected) with the contralateral one. Interestingly, we find an increased correlation of assembly weights across odors, suggesting that the formation/segregation of odor-selective assemblies is hindered when the principal cell synapses are abolished. This assembly selectivity reduction co-occurred as the number of losing neurons decreased, and the inhibition of the latter was also reduced. Consequently, decoding accuracy significantly decreased during the 150-250 ms window in the infected TeLC hemisphere compared to the contralateral cortex.

Therefore, we believe these new results support the role of gamma oscillations in segregating cell assemblies and generating a sparse orthogonal odor representation. These findings are now included as new panels of Figure 6 and Figure 7 and discussed on page 8.

Author Response

Reviewer #1 (Public Review):

By studying the effect of Treg depletion in a CD8+ T cell-dependent diabetes model the group around Ondrej Stepanek described that in the absence of Treg cells antigen-specific CD8+ OT-I T cells show an activated phenotype and accelerate the development of diabetes in mice. These cells - termed KILR cells - express CD8+ effector and NK cell gene signatures and are identified as CD49d- KLRK1+ CD127+ CD8+ T cells. The authors suggest that the generation of these cells is dependent on TCR stimulation and IL-2 signals, either provided due to the absence of Treg cells or by injection of IL-2 complexed to specific antiIL-2 mAbs. In vivo, these cells show improved target cell killing properties, while the authors report improved anti-tumor responses of combination treatments with doxorubicin combined with IL-2/JES6 complexes. Finally, the authors identified a similar human subset in publicly available scRNAseq datasets, supporting the translational potential of their findings.

The conclusions are mostly well supported, except for the following two considerations:

We are happy for the positive overall evaluation of our manuscript by both reviewers and we are thankful for their specific insightful comments, which helped us to improve the manuscript.

1) From Fig. 4A and B it is not conclusively shown, that Tregs limit IL-2 necessary for the expansion of OT-I cells and subsequent induction of diabetes. An IL-2 depletion experiment (e.g. with combined injection of the S4B6 and JES6-1 antibodies) would further strengthen this claim. Along these lines, the authors claim "IL-2Rα expression on T cells can be induced by antigen stimulation or by IL-2 itself in a positive feedback loop [20]. Accordingly, downregulation of IL-2Rα in OT-I T cells in the presence of Tregs might be a consequence of the limited availability of IL-2.". The cited reference 20 did observe CD25 upregulation by IL-2 on T cells but the observed effect might only be caused by upregulation of CD25 on Treg cells, which increases the MFI for the whole T cell population. Did the authors observe significant upregulation of CD25 on effector CD4+ and CD8+ T cells in their experiments with IL-2/S4B6 or IL-2/JES6 treatment?

We added another reference to support our claim (Sereti, I., et al., Clin Immunol, 2000. 97(3): p. 266-76.). Along this line, we also observed that addition of IL-2 in vitro leads to IL-2Rα upregulation on CD8+ T cells (shown in Fig. 4C), which was IL-2Rα level was lower if Tregs were present. We also observed upregulation of IL-2Rα in vivo upon the stimulation of OT-I T cells with OVA and IL-2ic, which is now shown in the Fig. S6C of the revised manuscript.

To further explore if Tregs limit expansion of OT-I and diabetes progression via IL-2 limitations, we performed the proposed experiment using a combined injection of S4B6 and JES6-1 anti-IL-2 antibodies. At the beginning, we were skeptical that we could completely block the IL-2 using this approach for the following reasons. First, IL-2 is produced locally in the spleen and lymph nodes and might not be easily accessible for the antibodies for a complete block. Second, IL-2 has a relatively short turnover and is continuously produced, but the half-life of the injected antibodies is unknown, which questions the duration of such a block. Third, it is possible that some IL-2 molecules would bound only to one of the two antibodies, which will make it a hyper-stimulating immune-complex, instead of neutralizing it.

Anyway, we were curious enough to perform this experiment. We used a condition that based on our experience leads to diabetes manifestation in Tregs depleted, but not in Treg replete mice (10 k OT-I T cells, OVA + LPS immunization). One additional group of Treg-depleted mice received a single dose of S4B6 and JES6-1 anti-IL-2 (200 µg of each antibody per mouse). We observed that this IL-2 blocking delayed, but not prevented the development of diabetes in most animals (Fig. 1 below).

Overall, we believe that this experiment is rather supporting our conclusions concerning the importance of IL-2, although the effect is only partial. However, we decided not to include this experiment in the manuscript, because we do not have the evidence about how efficient the IL-2 blocking was (see above), which makes the interpretation difficult. Because the reviews and the point-by-point response is public in eLife, we believe that showing the data here is appropriate.

Figure 1. Role of IL-2 blocking on the development of experimental diabetes. Two independent experiments were performed. Statistical significance was calculated using Log-rank (Mantel-Cox) test for survival, and Kruskal-Wallis test for blood glucose (p-value is shown in italics).

2) The anti-tumor efficacy of KILR cells is intriguing but currently, it is unclear if it is indeed mediated by KILR cells. Have KILR cells been identified by flow cytometry in the BCL1 and B16F10 models treated with doxorubicin and IL-2/JES6? Were specific KILR cell depletion studies conducted, e.g. with an anti-KLRK1 depleting antibody? Additional experiments addressing these questions would be desirable to further support the authors' claims.

We are thankful to both reviewers for their similar comments concerning the analysis of CD8+ T cells in the tumor model. Addressing these comments lead to very useful data and significantly improved our manuscript.

We performed the analysis of splenic CD8+ T cells in the BCL1 leukemia model (spleen is the major site of the leukemic cells in this model). We observed that KLRK1+ T cells represented almost half of CD8+ T cells in mice treated with DOX+IL-2, which was much higher frequency than in the control and DOX-only treated mice. Although not all KLRK1+ cells were bona fide KILR cells, the frequencies of KLRK1+ IL-7R+ and KLRK1+ CD49d- cells were also strongly elevated in the Dox+IL-2ic treated mice. Overall, the survival of DOX+IL-2ic treated mice correlated with the frequencies of KILR T cells and KLRK1+ T cells. Moreover, GZMB was almost exclusively expressed by KLRK1+ T cells. We are showing these data in Fig. 7C and Fig. S7B in the revised manuscript.

In the B16 melanoma model, we analyzed CD8+ T cells in the spleens and also in the tumors. We observed a huge population of KLRK1+ GZMB+ CD8+ T-cell population in the spleen of DOX+IL-2ic-treated mice, but not in the untreated or DOX-only treated mice (Fig. 7F). Both KLRK1+ CD49d+ and KLRK1+ CD49d- CD8+ T cells were substantially more frequent in the DOX+IL-2ic-treated, but not in the untreated or DOX-only treated mice (Fig. S7F). In the tumor, the KLRK1+ CD49d- CD8+ T cells were found at large numbers only in the DOX+IL-2ic-treated mice (Fig. 7G). Moreover, these KLRK1+ CD49d- CD8+ T cells expressed high levels of IL-7R and GZMB only in DOX+IL-2ic-treated, but not in untreated and DOX-only treated mice (Fig. 7H).

We believe that these new data provide evidence that the combination of immunogenic chemotherapy with IL-2 treatment induced KILR cells in the spleens and in the tumors and that this correlates with the better survival.

Because the majority of non-naïve CD8+ T cells (and vast majority of GZMB+ CD8+ T cells) in the spleens and tumors of the tumor-bearing mice treated with DOX+IL-2ic were KLRK1+ and because we have shown that the protective effect of the DOX+IL-2ic therapy is largely CD8+ T cell-dependent, we did not find it essential to perform the depletion of KLRK1+ T-cells. We believe that it is almost inevitable that the depletion of KLRK1+ T cells would lead to increased tumor growth as it would probably deplete the majority of antigenspecific CD8+ T cells, mimicking the overall CD8+ T cell depletion. Moreover, we do not have this protocol established.

Reviewer #2 (Public Review):

In this study, the authors determine the superior cell killing abilities of KLRK1+ IL7R+ (KILR) CD8+ effector T cells in experimental diabetes and tumor mouse model. They also provide evidence that Tregs suppress the formation of this previously uncharacterized subset of CD8+ effector T cells by limiting IL-2.

Strength and Limitation

This study focuses on the relationship between Tregs and CD8+ T cells. They used different experimental diabetes mouse models to reveal that Tregs suppress the CD8+ effector T cells by limiting IL-2. They also found a unique subset of KLRK1+ IL7R+ (KILR) CD8+ effector T cells with superior cell killing abilities through single-cell sequencing, but killing abilities could be inhibited by Tregs. They also tested their theory in in vivo tumor model. The data, in general, support the conclusions; however, some issues need to be fully addressed, as detailed below.

We are happy for the positive overall evaluation of our manuscript by both reviewers and we are thankful for their specific insightful comments, which helped us to improve the manuscript.

1) This study used the concentration of urine glucose as the standard for diabetes ({greater than or equal to} 1000 mg/dl for two consecutive days). However, multiple reasons may lead to a high level of urine glucose. As a type I diabetes mouse model, authors could use immunohistological analysis of islet to show the proportion of T cells and islet cells in islet, which can display the geographic distribution of immune cells, severity and histology structure of damaged pancreas islet directly. If possible, different subsets of immune cells, especially CD4 vs CD8+ cells should be stained for their location.

We added the histological examination of the pancreas in control, DEREG-, and DEREG+ mice using contrast H&E staining and immuno-fluorescence (Fig. 1D-E in the revised manuscript). We observed that the high glucose and blood levels are preceded by the destruction of the pancreatic islets (morphology and decreased insulin production) as well as by the infiltration of the islets with immune cells including CD4+ and CD8+ T cells.

2) This article shows that KILR effector CD8+ T cells have strong cytotoxic properties. However, they do not describe the potential proliferation ability vs apoptosis of this subset from islets.

We analyzed the proliferation (KI67 expression) and apoptosis (Annexin V, cleaved Caspase 3) in T cells isolated from the pancreas of DEREG- and DEREG+ mice on day 4 after the induction of diabetes using flow cytometry (Figure 2 below). We did not observe any differences between DEREG- and DEREG+ mice or among different subsets of OT-I T cells in the DEREG+ mice. Essentially, all T cells were proliferative (KI67+) and there was a very low percentage of Annexin V or cleaved Caspase 3 positive cells.

Figure 2. Lymphocytes were isolated from the pancreas of DEREG- RIP.OVA and DEREG+ RIP.OVA mice on day 4 after the induction of diabetes, and analyzed using flow cytometry. Two independent experiments were performed. Gated on OT-I T cells. Top: proliferation rate based on Ki-67 staining. Representative histogram and MFI (median is shown). Middle: Apoptosis rate based on Annexin V staining. Representative histogram shows Annexin V staining in three populations of OT-I T cells from DEREG+ mouse (“AE” - CD49d+ KLRK1-, “++” - CD49d+ KLRK1+, KILR - CD49d- KLRK1+), total OT-I T cells from DEREG-, and a positive control: WT CD8+ T cells treated with hydrogen peroxide. Middle right: Percentage of Annexin V+ cells and MFI (median is shown). Bottom: Apoptosis rate based on cleaved Caspase 3 staining. Representative dot plots show cleaved Caspase 3 staining of OT-I T cells from DEREG+, DEREG-, and a positive control: WT CD8+ T cells treated with hydrogen peroxide. Bottom right: percentage of cleaved Caspase 3+ cells (median is shown).

However, we found question concerning proliferation and apoptosis of KILR cells interesting and worth further investigation. For this reason, we assessed the proliferation, survival, and phenotypic stability of naïve, KILR, and effector T cells by their competitive transfer into CD3ε-/- mice. The phenotype of all these three subsets remained stable for 4 days (Fig. 6F), documenting that KILR cells are not just a very transient stage. Moreover, the KILR cells were ~2 fold more abundant then effector cells 3 days after their 1:1 cotransfer into CD3ε-/- mice (Fig. 6G, Fig. 6SE). This was probably caused by their slight advantages in both proliferation and survival (Fig. 6SF-G).

3) Figure 7 shows that the antitumor efficacy of IL-2 depends on CD8+ T cells. But in this part, there is no data to show the change of KLRK1+ IL7R+ CD8+ effector T cells in tumor tissue. Therefore, the article needs to add more data to verify that IL-2 enhances antitumor ability via KLRK1+ IL7R+ CD8+ effector T cells.

We are thankful to both reviewers for their similar comments concerning the analysis of CD8+ T cells in the tumor model. Addressing these comments lead to very useful data and significantly improved our manuscript.

We performed the analysis of splenic CD8+ T cells in the BCL1 leukemia model (spleen is the major site of the leukemic cells in this model). We observed that KLRK1+ T cells represented almost half of CD8+ T cells in mice treated with DOX+IL-2, which was much higher frequency than in the control and DOX-only treated mice. Although not all KLRK1+ cells were bona fide KILR cells, the frequencies of KLRK1+ IL-7R+ and KLRK1+ CD49d- cells were also strongly elevated in the Dox+IL-2ic treated mice. Overall, the survival of DOX+IL-2ic treated mice correlated with the frequencies of KILR T cells and KLRK1+ T cells. Moreover, GZMB was almost exclusively expressed by KLRK1+ T cells. We are showing these data in Fig. 7C and Fig. S7B in the revised manuscript.

In the B16 melanoma model, we analyzed CD8+ T cells in the spleens and also in the tumors. We observed a huge population of KLRK1+ GZMB+ CD8+ T-cell population in the spleen of DOX+IL-2ic-treated mice, but not in the untreated or DOX-only treated mice (Fig. 7F). Both KLRK1+ CD49d+ and KLRK1+ CD49d- CD8+ T cells were substantially more frequent in the DOX+IL-2ic-treated, but not in the untreated or DOX-only treated mice (Fig. S7F). In the tumor, the KLRK1+ CD49d- CD8+ T cells were found at large numbers only in the DOX+IL-2ic-treated mice (Fig. 7G). Moreover, these KLRK1+ CD49d- CD8+ T cells expressed high levels of IL-7R and GZMB only in DOX+IL-2ic-treated, but not in untreated and DOX-only treated mice (Fig. 7H).

We believe that these new data provide evidence that the combination of immunogenic chemotherapy with IL-2 treatment induced KILR cells in the spleens and in the tumors and that this correlates with the better survival.

4) It is unclear why the authors chose Dox to combine with IL-2/JES6. The authors should provide a more rational introduction to bridge such a combination. Authors should also explain the reason why there is no antitumor effect of IL-2/JES6 treatment alone.

The experiments with OT-I mice showed that the formation of KILR cells required both the antigenic stimulation and IL-2 signals. We believe that there is only very week antigenic stimulation by the tumor itself. For this reason, we combined the treatment with the chemotherapy Doxorubicin, which is known to induce immunogenic cell death of the tumor cells (e.g., Casares et al. 2005, PMID: 16365148). We believe that doxorubicin induces the death of (some) tumor cells and the release and presentation of their tumorspecific antigens. Without it, the tumor are simply too “cold” to induce sufficient T-cell response. We emphasized this in the revised version of the manuscript.

Importantly, some of us observed a similar effect of IL-2ic in a combination with check-point blockade therapy (without chemotherapy) in a different tumor model, which documents that the chemotherapy is not essential for this effect (unpublished data).

Author Response

Reviewer #1 (Public Review):

Point 1: Many of the initial analyses of behavior metrics, for instance predicting reaction times, number of fixations, or fixation duration, use value difference as a regressor. However, given a limited set of values, value differences are highly correlated with the option values themselves, as well as the chosen value. For instance, in this task the only time when there will be a value difference of 4 drops is when the options are 1 and 5 drops, and given the high performance of these monkeys, this means the chosen value will overwhelmingly be 5 drops. Likewise, there are only two combinations that can yield a value difference of 3 (5 vs. 2 and 4 vs 1), and each will have relatively high chosen values. Given that value motivates behavior and attracts attention, it may be that some of the putative effects of choice difficulty are actually driven by value.

To address this question, we have adapted the methods of Balewski and colleagues (Neuron, 2022) to isolate the unique contributions of chosen value and trial difficulty to reaction time and the number of fixations in a given trial (the two behaviors modulated by difficulty in the original paper). This new analysis reveals a double dissociation in which reaction time decreases as a function of chosen value but not difficulty, while the number of fixations in a trial shows the opposite pattern. Our interpretation is that reaction time largely reflects reward anticipation, whereas the number of fixations largely reflects the amount of information required to render a decision (i.e., choice difficulty). See lines 144-167 and Figure 2.

Point 2: Related to point 1, the study found that duration of first fixations increased with fixated values, and second (middle) fixation durations decreased with fixated value but increased with relative value of the fixated versus other value. Can this effect be more concisely described as an effect of the value of the first fixated option carrying over into behavior during the second fixation?

This is a valid interpretation of the results. To test this directly, we now include an analysis of middle fixation duration as a function of the not-currentlyviewed target. Note that the vast majority of middle fixations are the second fixation in the trial, and therefore the value of the unattended target is typically the one that was viewed first. The analysis showed a negative correlation between middle fixation duration and the value of the unattended target which is consistent with the first fixated value carrying over to the second fixation. See lines 243-246.

Point 3: Given that chosen (and therefore anticipated) values can motivate responses, often measured as faster reaction times or more vigorous motor movements, it seems curious that terminal non-decision times were calculated as a single value for all trials. Shouldn't this vary depending at least on chosen values, and perhaps other variables in the trial?

In all sequential sampling model formulations we are aware of, nondecision time is considered to be fixed across trial types. Examples can be found for perceptual decisions (e.g., Resulaj et al., 2009) and in the “bifurcation point” approach used in the recent value-based decision study by Westbrook et al. (2020).

To further investigate this issue, we asked whether other post-decision processes were sensitive to chosen value in our paradigm. To do so, we measured the interval between the center lever lift and the left or right lever press, corresponding to the time taken to perform the reach movement in each trial (reach latency). We then fit a mixed effects model explaining reach latency as a function of chosen value. While the results showed significantly faster reach latencies with higher chosen values, the effect size was very small, showing on average a ~3ms decrease per drop of juice. In other words, between the highest and lowest levels of chosen value (5 vs. 1), there is only a difference of approximately 12ms. In contrast, the main RT measure used in the study (the interval between target onset and center lever lift) is an order of magnitude more sensitive to chosen value, decreasing ~40ms per drop of juice. These results are shown in Author response image 1.

Author response image 1.

This suggests that post-decision processes (NDT in standard models and the additive stage in the Westbrook paper) vary only minimally as a function of chosen value. We are happy to include this analysis as a supplemental figure upon request.

Point 4: The paper aims to demonstrate similarities between monkey and human gaze behavior in value-based decisions, but focuses mainly on a series of results from one group of collaborators (Krajbich, Rangel and colleagues). Other labs have shown additional nuance that the present data could potentially speak to. First, Cavanaugh et al. (J Exp Psychol Gen, 2014) found that gaze allocation and value differences between options independently influence drift rates on different choices. Second, gaze can correlate with choice because attention to an option amplifies its value (or enhances the accumulation of value evidence) or because chosen options are attended more after the choice is implicitly determined but not yet registered. Westbrook et al. (Science, 2020) found that these effects can be dissociated, with attention influencing choice early in the trial and choice influencing attention later. The NDTs calculated in the present study allot a consistent time to translating a choice into a motor command, but as noted above don't account for potential influences of choice or value on gaze.

The two-stage model of gaze effects put forth by Westbrook et al. (2020) is consistent with other observations of gaze behavior and choice (i.e., Thomas et al., 2019, Smith et al., 2018, Manohar & Husain, 2013). In this model, gaze effects early in the trial are best described by a multiplicative relationship between gaze and value, whereas gaze effects later in the trial are best described with an additive model term. To test the two-stage hypothesis, Westbrook and colleagues determined a ‘bifurcation point’ for each subject that represented the time at which gaze effects transitioned from multiplicative to additive. In our data, trial durations were typically very short (<1s), making it difficult to divide trials and fit separate models to them. We therefore took at different approach: We reasoned that if gaze effects transition from multiplicative to additive at the end of the trial, then the transition point could be estimated by removing data from the end of each trial and assessing the relative fit of a multiplicative vs. additive model. If the early gaze effects are predominantly multiplicative and late gaze effects are additive, the relative goodness of fit for an additive model should decrease as more data are removed from the end of the trial. To test this idea, we compared the relative model fit of an additive vs. multiplicative models in the raw data, and for data in which successively larger epochs were removed from the end of the trial (50, 100, 150, 200, 300, and 400ms). The relative fit was assessed by computing the relative probability that each model accurately reflects the data. In addition, to identify significant differences in goodness of fit, we compared the WAIC values and their standard errors for each model (Supplemental File 3). As shown in Figure 4, the relative fit probability for both models is nonzero in the raw data 0 truncation), indicating that a neither model provides a definitive best fit, potentially reflecting a mixture of the two processes. However, the relative fit of the additive model decreases sharply as data is removed, reaching zero at 100ms truncation. 100ms is also the point at which multiplicative models provide a significantly better fit, indicated by non-overlapping standard error intervals for the two models (Supplemental File 3). Together, this suggested that the transition between early- and late-stage gaze effects likely occurs approximately 100ms before the RT.

To minimize the influence of post-decision gaze effects, the main results use data truncated by 100ms. However, because 100ms is only an estimate, we repeated the main analyses over truncation values between 0 and 400ms, reported in Figure 6 - figure supplement 1 & Figure 7 - figure supplement 1. These show significant gaze duration biases and final gaze biases in data truncated by up to 200ms.

Reviewer #2 (Public Review):

Recommendation 1: The only real issue that I see with the paper is fairly obvious: the authors find that the last fixations are longer than the rest, which is inconsistent with a lot of the human work. They argue that this is due to the reaching required in this task, and they take a somewhat ad-hoc approach to trying to correct for it. Specifically, they take the difference between final and non-final, second fixations, and then choose the 95th percentile of that distribution as the amount of time to subtract from the end of each trial. This amounts to about 200 ms being removed from the end of each trial. There are several issues with this approach. First, it assumes that final and non-final fixations should be the same length, when we know from other work that final fixations are generally shorter. Second, it seems to assume that this 200ms is "the latency between the time that the subject commits to the movement and the time that the movement is actually detected by the experimenter". However, there is a mismatch between that explanation and the details of the task. Those last 200ms are before the monkey releases the middle lever, not before the monkey makes a left/right choice. When the monkey releases the middle lever, the stimuli disappear and they then have 500ms to press the left or right lever. But, the reaction time and fixation data terminate when the monkey releases the middle lever. Consequently, I don't find it very likely that the monkeys are using those last 200ms to plan their hand movement after releasing the middle lever.

Thanks for the opportunity to clarify these points. There are three related issues:

First, with regards to fixation durations, in the updated Figure 3 we now show durations as a function of both the absolute order in the trial (first, second, third, fourth, etc.) and the relative order (final/nonfinal). We find that durations decrease as a function of absolute order in the trial, an effect also seen in humans (see Manohar & Husain, 2013). At the same time, while holding absolute order constant, final fixations are longer than non-final fixations. To explain the discrepancy with human final fixation durations, we note that monkeys make many fewer fixations per trial (~2.5) than humans do (~3.7, computed from publicly available data from Krajbich et al., 2010.) This means that compared to humans, monkeys’ final fixations occur earlier in the trial (e.g., second or third), and are therefore comparatively longer in duration. Note that studies with humans have not independently measured fixation durations by absolute and relative order, and therefore would not have detected the potential interaction between the two effects.

Second, the comment suggests that the final 200ms before lever lift is not spent planning the left/right movement, given that the monkeys have time after the lever lift in which to execute the movement (400 or 500ms, depending on the monkey). The presumption appears to be that 400/500ms should be sufficient to plan a left/right reach. However, we think that these two suggestions are unlikely, and that our original interpretation is the most plausible. First, the 400/500ms deadline between lift and left/right press was set to encourage the monkeys to complete the reach as fast as possible, to minimize deliberations or changes of mind after lifting the lever. More specifically, these deadlines were designed so that on ~0.5% of trials, the monkeys actually fail to complete the reach within the deadline and fail to obtain a reward. This manipulation was effective at motivating fast reaches, as the average reach latency (time between lift and press) was 165 SEM 20ms for Monkey K, and 290 SEM 100ms for Monkey C.

Therefore, given the time pressure imposed by the task, it is very unlikely that significant reach planning occurs after the lever lift. In addition to these empirical considerations, the idea that the final moments before the RT are used for motor planning is a standard assumption in many theoretical models of choice (including sequential sampling models, see Ratcliff & McKoon 2008, for review), and is also well-supported by studies of motor control and motor system neurophysiology. Based on these, we think the assumption of some form of terminal NDT is warranted.

Third, we have changed our method for estimating the NDT interval. In brief we sweep through a range of NDT truncation values (0-400ms) and identify the smallest interval (100ms) that minimizes the contribution of “additive” gaze effects, which are thought to reflect late-stage, post-decision gaze processes. See the response to Point 4 for Reviewer 1 above, Figure 4 and lines 267-325 in the main text. In addition, we report all of the major study results over a range of truncation values between 0 and 400ms.

Author Response

Reviewer #1 (Public Review):

This paper describes the neural activity, measured by intrinsic optical imaging in reach-to-grasp, and reach-only conditions in relation to the Intra-cortical micro stimulation maps. The paper mostly describes a relatively unique and potentially useful data set. However, in the current version, no real hypotheses about the organization of M1 and PMd are tested convincingly. For example, the claim of "clustered neural activity" is not tested against any quantifiable alternative hypothesis of non-clustered activity, and support for this idea is therefore incomplete.

The combination of intrinsic optical imaging and intra-cortical micro-stimulation of the motor system of two macaque monkeys promised to be a unique and highly interesting dataset. The experiments are carefully conducted. In the analysis and interpretation of the results, however, the paper was disappointing to me. The two main weaknesses in my mind were:

a) The alternative hypotheses depicted in Figure 1B are not subjected to any quantifiable test. When is an activity considered to be clustered and when is it distributed? The fact that the observed actions only activate a small portion of the forelimb area (Figure 5G, H) is utterly unconvincing, as this analysis is highly threshold-dependent. Furthermore, it could be the case that the non-activated regions simply do not give a good intrinsic signal, as they are close to microvasculature (something that you actually seem to argue in Figure 6b). Until the authors can show that the other parts of the forelimb area are clearly activated for other forelimb actions (as you suggest on line 625), I believe the claim of cluster neural activity stands unsupported.

We appreciate the reviewer’s concerns and we have made several revisions.

(1) The two panels in Fig 1B should have been presented as potential outcomes as opposed to hypotheses in need of quantifiable testing. We revised the Introduction (line 105-111) and the Results (line 149-152) accordingly.

(2) We agree that the thresholding procedure adopted in the original submission could have impacted the spatial measurements of cortical activity (i.e., Fig 5G-H in original submission). We have completely revised the thresholding procedure and it is now based on statistical comparisons that include all trials (instead of thresholding by number of sessions in the original submission). Thus, the thresholded maps in Fig 5G & 5J are now obtained from pixel-by-pixel comparisons (t-tests, p<1e-4) between frames acquired post-movement and frames acquired before movement. Nevertheless, even with this relatively relaxed threshold, the largest activity maps overlapped <40% of the forelimb representations.

It is important to note that major vessels were excluded from the thresholded map and from the motor map. Thus, uncertainty about imaging in and around vessels was likely not a factor in the calculated overlap between thresholded maps and the motor map.

(3) We agree that showing activation in other parts of the forelimb representations in response to action other than reach-to-grasp would have supported some of the arguments that we previously put forth. Unfortunately, we do not have the supporting data and obtaining it would take months/years. We have therefore expanded the Discussion to include limitations of the behavioral task (line 439-443).

b) The most interesting part of the study (which cannot be easily replicated with human fMRI studies) is the correspondence between the evoked activity and intra-cortical stimulation maps. However, this is impeded by the subjective and low-dimensional description of the evoked movement during stimulation (mainly classifying the moving body part), and the relatively low-dimensional nature (4 conditions) of the evoked activity.

We agree with the reviewer on all accounts. We expanded the Discussion to consider the low dimensionality of the motor maps and the behavioral task (line 439-449).

Measuring cortical activity in a variety of motor tasks would likely have provided additional insight about movement-related cortical activity. Nevertheless, including additional tasks, even if it were possible to do so in the same monkeys, would have delayed study completion by months/years. The hidden challenge of the experimental design is that each monkey is trained to not move for many seconds to minimize contamination of ISOI signals. For example, from trial initiation to Go Cue, the monkey must hold its hand in the start position for 5 seconds. Similarly, after movement completion, the monkey must hold its hand in the start position for another 5 seconds. In between successful trials, a monkey must wait for ~12 seconds before it can initiate a new trial. These durations are >1 order of magnitude longer than in electrophysiological studies in comparable tasks. Achieving consistent task performance with the long durations used here, took months of daily training. Moreover, our monkeys typically run out of steam after ~60-70 min of working on the task. This forces us to limit the overall number of task conditions tested in a session, to obtain a large enough number of trials from each condition.

c) Many details about the statistical analysis remain unclear and seem not well motivated.

We address the reviewer’s specific concerns.

Reviewer #2 (Public Review):

Chehade and Gharbawie investigated motor and premotor cortex in macaque monkeys performing grasping and reaching tasks. They used intrinsic signal optical imaging (ISOI) covering an exceedingly large field-of-view extending from the IPS to the PS. They compared reaching and fine/power-grip grasping ISOI maps with "motor" maps which they obtained using extensive intracranial microstimulation. The grasping/reaching-induced activity activated relatively isolated portions of M1 and PMd, and did not cover the entire ICM-induced 'motor' maps of the upper limbs. The authors suggest that small subzones exist in M1 and PMd that are preferentially activated by different types of forelimb actions. In general, the authors address an important topic. The results are not only highly relevant for increasing our basic understanding of the functional architecture of the motor-premotor cortex and how it represents different types of forelimb actions, but also for the development of brain-machine interfaces. These are challenging experiments to perform and add to the existing yet complementary electrophysiology, fMRI, and optical imaging experiments that have been performed on this topic - due to the high sensitivity and large coverage of the particular IOSI methods employed by the authors. The manuscript is generally well written and the analyses seem overall adequate - but see below for some additional analyses that should be done. Although I'm generally enthusiastic about this manuscript, there are two major issues that should be clarified. These major questions relate mainly to potential thresholding issues and clustering issues.

Major:

1) The main claim of the authors is that specific forelimb actions activate only a small fraction of what they call the motor map (i.e., those parts of M1/PMd that evoke muscle contractions upon ICM). The action-related activity is measured by ISOI. When looking a the 'raw' reflectance maps, it is rather clear that relatively wide portions of the exposed cortex are activated by grasping/reaching, especially at later time points after the action. In fact, another reading of the results may be that there are two zones of 'deactivation' that split a large swath of motor-premotor cortex being activated by the grasping/reaching actions. (e.g. at 6 seconds after the cue in Fig 3A, 5A). At first sight, the 'deactivated' regions seem to be located in the cortex representing the trunk/shoulder/face - hence regions not necessarily activated (or only weakly) during the grasping/reaching actions. If true, this means that most of the relevant M1/PMd cortex IS activated during the latter actions - opposing the 'clustering' claims of the authors. This raises the question of whether the 'granularity' claimed by the authors is

a. threshold dependent. In this context, the authors should provide an analysis whereby 'granularity' is shown independent of statistical thresholds of the ISOI maps.

We appreciate the reviewer’s concerns and have completely revised the analyses central to Fig 5. We believe that the figure now contains evidence from both thresholded and unthresholded ISOI data in support of limited spatial extent of cortical activation (i.e., “granularity” in the reviewer’s comments).

For evidence from unthresholded ISOI data, we examined reflectance change time courses from different size ROIs (line 764-768). (A) Small circular ROIs (0.4 mm radius), which we placed in the M1 hand, M1 arm, and PMd arm, zones (Fig 5B). (B) Large ROI inclusive of the M1 and PMd forelimb representations (Fig 5B). We reasoned that if cortical activity is spatially widespread, then the small and large ROIs would report similar time courses. In contrast, if cortical activity is spatially focal, then activity would be detected in the small ROI time courses but would washed out in the large ROI time courses. Our results support the second possibility (Fig 5C-F). Thus, in the movement conditions, time courses from the small ROIs had a large negative peak after movement completion (Fig C-E). In contrast, the characteristic negative peak was absent in the time courses obtained from the large ROI (Fig 5F).

Separately, we revised our thresholding approach to make those results less sensitive to thresholding effects (more details in our response to the first major point from Reviewer 1). The revised results – thresholded/ binarized maps – are consistent with focal cortical activity. Fig 5G & 5J show activity maps thresholded (t-test, p<0.0001) without correction for multiple comparisons, and therefore represent the least restrictive estimate of the spatial extent of cortical activity. Measurements from these maps showed that significantly active pixels overlapped <40% of the M1 & PMd forelimb representations. We interpret the thresholded results as evidence in support of focal cortical activity.

This raises the question of whether the 'granularity' claimed by the authors is

b. dependent on the time-point one assesses the maps. Given the sluggish hemodynamic responses, it is unclear which part of the ISOI maps conveys the most information relative to the cue and arm/hand movements. I suspect that timepoints > 6 s will reveal even larger 'homogeneous' activations compared to the maps < 6s.

We agree with the reviewer that the lag in hemodynamic signals complicates frame selection. Nevertheless, it is unlikely that cortical activity maps would have been larger at time points >6s from Cue. We provide three supporting arguments.

(1) In the imaging sessions used in Fig 4, we acquired images for 9s per trial and systematically varied Cue onset time. The time courses in Fig 4A-B show that for all Cue onset conditions, the negative peak occurred <6s from Cue. This observation from unthresholded results does not support the notion of greater cortical activity at time points >6s from Cue.

(2) From the same experiment, Fig 4C shows 9 thresholded/binarized maps generated from different time points in relation to Cue. We measured the size of each map (i.e., overlap with the M1/PMd forelimb representations). We present the results in Author response image 1. The largest maps came from an average frame captured +5.8-6.0s from Cue. Those maps are on the diagonal in Fig 4E (top left to bottom right). This result from thresholded data therefore does not support the notion of greater cortical activity at time points >6s from Cue.

Author response image 1.

(3) In all other sessions, we acquired images for 7s per trial (-1.0 to +6.0 s from Cue) without varying Cue onset time. At every time point (100 ms), we measured the size of the thresholded/binarized map in relation to the size of the M1 and PMd forelimb representations. The results are presented in Fig 5I & 5L and indicate that thresholded maps plateau in size by 5.0-5.5 s from Cue. At peak size, the maps overlapped <50% of the M1 and PMd forelimb representations. These result indicates that it is unlikely that we underreported the size of activity maps by not measuring map size beyond 6s from Cue.

In fact, Fig 5F (which is highly thresholded) shows a surprisingly good match between the different forelimb actions, which argues against the existence of small subzones that are preferentially activated by different types of forelimb actions -the main claim of the authors.

Our original proposal should have been more clearly stated. We were proposing that the thresholded maps, which had similar spatial organizations across conditions as the reviewer suggested, reported on subzones tuned for reach-to-grasp actions. Adjacent to those subzones could be other subzones that are preferentially active during other types of forelimb actions (e.g., pulling, pushing, grooming). We could not test this possibility in our study because the behavioral task examined a narrow range of arm and hand actions. We therefore revised the Discussion to state the limitations of our task and to lean more on published work that supports the present proposal (439-443 and 504-508).

2) Related to the previous point, the ROI selections/definitions for the time course analyses seem highly arbitrary. As indicated in the introduction, the clustering hypothesis dictates that "an arm function would be concentrated in subzones of the motor arm zones. Neural activity in adjacent subzones would be tuned for other arm functions." To test this hypothesis directly in a straightforward manner, the authors could use the results from the ICM experiment to construct independent ROIs and to evaluate the ISOI responses for the different actions. In that case, the authors could do a straightforward ANOVA (if the data permits parametric analyses) with ROI, action, and time point (and possibly subject) as factors.

We agree with the reviewer, and we now leverage the ICMS map for guiding ROI placement. All time courses are now derived from 1 of 2 types of ROIs. (1) Small ROIs (0.4 mm radius) placed in zones defined from ICMS (e.g., M1 hand zone). (2) Large ROIs that include the entire forelimb representations in M1 or in PMd (Fig 5B).

Author Response:

Reviewer #1 (Public Review):

The authors interrogated an underexplored feature of CRISPR arrays to enhance multiplexed genome engineering with the CRISPR nuclease Cas12a. Multiplexing represents one of the many desirable features of CRISPR technologies, and use of highly compact CRISPR arrays from CRISPR-Cas systems allows targeting of many sites at one time. Recent work has shown though that the composition of the array can have a major impact on the performance of individual guide RNAs encoded within the array, providing ample opportunities for further improvements. In this manuscript, the authors found that the region within the repeat lost through processing, what they term the separator, can have a major impact on targeting performance. The effect was specifically tied to upstream guide sequences with high GC content. Introducing synthetic separator sequences shorter than their natural counterparts but exhibiting similarly low GC content boosted targeted activation of a reporter in human cells. Applying one synthetic separator to a seven-guide array targeting chromosomal genes led to consistent though more modest targeted activation. These findings introduce a distinct design consideration for CRISPR arrays that can further enhance the efficacy of multiplexed applications. The findings also suggest a selective pressure potentially influencing the repeat sequence in natural CRISPR arrays.

Strengths:

The portion of the repeat discarded through processing normally has been included or discarded when generating a CRISPR-Cas12a array. The authors clearly show that something in between-namely using a short version with a similarly low GC content-can enhance targeting over the truncated version. A coinciding surprising result was that the natural separator completely eliminated any measurable activation, necessitating the synthetic separator.

The manuscript provides a clear progression from identifying a feature of the upstream sequences impacting targeting to gaining insights from natural CRISPR-Cas12a systems to applying the insights to enhance array performance.

With further support, the use of synthetic separators could be widely adopted across the many applications of CRISPR-Cas12a arrays.

Weaknesses:

The terminology used to describe the different parts of the CRISPR array could better align with those in the CRISPR biology field. For one, crRNAs (abbreviated from CRISPR RNAs) should reflect the final processed form of the guide RNA, whereas guide RNAs (gRNAs) captures both pre-processed and post-processed forms. Also, "spacers" should reflect the natural spacers acquired by the CRISPR-Cas system, whereas "guides" better capture the final sequence in the gRNA used for DNA target recognition.

We thank the reviewer for this correction. We have now changed most uses of “crRNA” to “gRNA”. We decided to retain the use of the word “spacer” for the target recognition portion of the gRNA rather than changing it to “guide” as the reviewer suggests, because we think there is a risk that the reader would confuse “guide” with the non-synonymous “guide-RNA”. We have added a remark explaining our use of “spacer” (“A gRNA consists of a repeat region, which is often identical for all gRNAs in the array, and a spacer (here used synonymously with “guide region”)”)

A running argument of the work is that the separator specifically evolved to buffer adjacent crRNAs. However, this argument overlooks two key aspects of natural CRISPR arrays. First, the spacer (~30 nts) is normally much longer than the guide used in this work (20 nts), already providing the buffer described by the authors. This spacer also undergoes trimming to form the mature crRNA.

If we understand this comment correctly, the argument is that, in contrast to a ~20-nt spacer, a 30-nt spacer would provide a buffer between adjacent guides even if a separator is not present. However, even a 30-nt spacer may have high GC content and form secondary structures that would interfere with processing of the subsequent gRNA. Our hypothesis is that the separator is AT-rich and so insulates gRNAs from one another regardless of the length or GC composition of spacers. Please let us know if we have misunderstood this comment.

Second, the repeat length is normally fixed as a consequence of the mechanisms of spacer acquisition. At most, the beginning of each repeat sequence may have evolved to reduce folding interactions without changing the repeat length, although some of these repeats are predicted to fold into small hairpins.

We agree with this comment. Indeed, we propose that the separator, which is part of the repeat sequence, has evolved to reduce folding interactions. We now clarify this at the end of the Results section: “Taken together, the results from our study suggest that the CRISPR-separator has evolved as an integral part of the repeat region that likely insulates gRNAs from the disrupting effects of varying GC content in upstream spacers.”

Prior literature has highlighted the importance of a folded hairpin with an upstream pseudoknot within the repeat (Yamano Cell 2016), where disrupting this structure compromises DNA targeting by Cas12a (Liao Nat Commun 2019, Creutzburg NAR 2020). This structure is likely central to the authors' findings and needs to be incorporated into the analyses.

We thank the reviewer for this important insight. We have now performed experiments exploring the involvement of the pseudoknot in the disruptive effects of high-GC spacers.

First, we used our 2-gRNA CRISPR array design (Fig. 1D) where the second gRNA targets the GFP promoter and the first gRNA contains a non-targeting dummy spacer. We generated several versions of this array where we iteratively introduced targeted point mutations in the dummy spacer to either form a hairpin restricted to the dummy spacer, or a hairpin that would compete with the pseudoknot in the GFP-gRNA’s repeat region (new Fig. S3). We found that both of these modifications significantly reduced performance of the GFP-targeting gRNA. These results suggest that interfering with the pseudoknot indeed disrupts gRNA performance, but that also hairpins that presumably don’t interfere directly with the pseudoknot are detrimental – perhaps by sterically hindering Cas12a from accessing its cleavage site. Interestingly, the AAAT synSeparator largely rescued performance of the worst-performing of these constructs. These results are displayed in the new Fig. S3 and discussed in the related part of the Results section.

Second, we have now performed a computational analysis using RNAfold where we correlated the performance of all dummy spacers with their predicted secondary structure (Fig. 1M). The correlation between predicted RNA structure and array performance was higher when the structural prediction included both the dummy spacer and the entire GFP-targeting gRNA (R2 = 0.57) than when it included only the dummy spacer (R2 = 0.27; new figure panel S1C). This higher correlation suggests that secondary structures that involve the GFP-targeting gRNA play a more important role in our experiment than secondary structures that only involve the dummy spacer. These results are described in the Results section and in the Fig. 1 legend.

Third, we now also performed secondary structure analysis (RNAfold) of two of our worst-performing dummy spacers (50% and 70% GC), which indicated that these spacers are likely to form secondary structures that involve both the repeat and spacer of the downstream GFP-targeting gRNA (Fig. 3G-H). Interestingly, this analysis suggested that the AAAT synSeparator improves performance of these spacers by loosening up these secondary structures or creating an unstructured bulge at the Cas12a cleavage site. These results are presented in Fig. 3G-H and the accompanying portion of the Results section.

To conclude, our analyses suggest that the secondary structure in the spacer and its interference with the pseudoknot in the repeat hairpin play a role in gRNA performance, wherein the inclusion of the AAAT synSeparator can partly rescue the performance, likely by restoring the Cas12a accessibility to the gRNA cleavage site.

Many claims could better reflect the cited literature. For instance, Creutzburg et al. showed that adding secondary structures to the guide to promote folding of the repeat hairpin enhanced rather than interfered with targeting.

We thank the reviewer for this comment. Creutzburg et al. report the interesting finding that a carefully designed 3’ extension of the spacer can counteract secondary structures that disrupt the repeat. In this way, the extension rescues disruptive secondary structures that involve the repeat and any upstream sequence. Relevant to this finding, it is conceivable that the synSeparator (AAAT) exerts its beneficial effect at the 3’ end of the GFP spacer by folding back onto the GFP spacer and in this way blocking secondary structures caused by a GC-rich dummy spacer located upstream of the GFP gRNA, according to the mechanism reported by Creutzburg et al. However, we used structural prediction of the GFP-targeting gRNA with and without the AAAT synSeparator and did not find evidence that the AAAT extension would cause this spacer to fold back onto itself (data not shown). Moreover, our experimental data (Fig. 3E) demonstrate that the synSeparator exerts its main beneficial effect when located upstream of the GFP-targeting gRNA, which would not be the case if the main mechanism was the one demonstrated by Creutzburg et al. We already had a paragraph discussing the Creutzburg paper in the Discussion, but we have now added a sentence specifying the mechanism that Creutzburg et al. demonstrated: “RNA secondary structure prediction (RNAfold) did not indicate that the GFP-targeting spacer would fold back on itself when an AAAT extension is added to the 3’ end, which would have been the case for the mechanism demonstrated by Creutzburg et al. (data not shown).”

Liu et al. NAR 2019 further showed that the pre-processed repeat actually enhanced rather than reduced performance compared to the processed repeat.

The experiment referenced by the reviewer (Fig. 2 in Liu et al., Nucleic Acids Research, 2019) in fact nicely supports our findings. In Liu et al., the pre-processed repeat only shows improved performance if it is located upstream of the targeting gRNA, and the gRNA is not followed by an additional pre-processed repeat (DRf-crRNA in their Fig. 2B & C). In this situation, the pre-processed repeat (containing the natural separator) may serve to enhance gRNA processing, as would be expected based on our results. At the same time, the absence of a full-length repeat downstream of the gRNA means that after gRNA processing, there will not remain any piece of RNA attached to the 3’ end of the spacer, which might disrupt gRNA performance. In contrast, when Liu et al. added an additional pre-processed repeat downstream of their gRNA (DRf-crRNA-DRf in the same panel), this construct performed the worst of all tested variants. This is consistent with our conclusion that the full-length separator reduces performance of gRNAs if it remains attached to the 3’ end of spacers. We have added a paragraph in the Discussion about this (Line 376).

Finally, the complete loss of targeting with the unprocessed repeat appears represent an extreme example given multiple studies that showed effective targeting with this repeat (e.g. Liu NAR 2019, Zetsche Nat Biotechnol 2016).

We acknowledge that our CRISPR array containing the full, natural separator (Fig. 3B) appears to be completely non-functional in contrast to the studies mentioned by the reviewer. We think this difference may have a few possible explanations. First, this array is in fact not entirely non-functional. Re-running the same experiment with a stronger dCas12a-activator (dCas12a-VPR, full length VPR, also used in Fig. 5) shows some modest GFP activation even with the full separator (1.4% vs 20.8% GFP+ cells; see the Appendix Figure 1). But for consistency, we have used the same, slightly less effective, dCas12a-activator (dCas12a-miniVPR) for all GFP-targeting experiments. Second, both the Liu et al. and Zetsche et al. studies used CRISPR editing rather than CRISPRa. We speculate that this might explain their relatively high indel frequency: Only a single cleavage event needs to take place for an indel to occur, whereas gene activation presumably requires the dCas12a-activator to be present on the promoter for extended periods of time. Thus, any inefficiency in DNA binding caused by the separator remaining attached to the spacer might disfavor CRISPRa activity more than CRISPR-editing activity. We have added these considerations to the Discussion and referenced the suggested papers (Line 376).

Appendix Figure 1: Percentage of GFP+ cells without or with a full-length separator using dCas12a-VPR (full length) gene activation.

Relating to the above point, the vast majority of the results relied on a single guide sequence targeting GFP. While the seven-guide CRISPR array did involve other sequences, only the same GFP targeting guide yielded strong gene activation. Therefore, the generalizability of the conclusions remains unclear.

We have now performed several experiments that address the generalizability of our conclusions:

First, we now include data demonstrating that the beneficial effect of adding a synSeparator is not limited to the AAAT sequence derived from the Lachnospiraceae bacterium separator. We now include three other 4-nt, AT-rich synSeparators derived from Acidaminococcus s. (TTTT), Moraxella b. (TTTA) and Prevotella d. (ATTT) (Fig. 3I). All these synSeparators rescued the poor GFP activation caused by an upstream spacer with high GC content, though not equally effectively. The quantitative difference between the synSeparators could either be due to the intrinsic “insulation capacity” of these sequences, or the way they interact with the Lb-Cas12a protein, or to sequence-specific interactions with this particular CRISPR array. We discuss these possibilities in the Discussion (Line 437).

Second, we now include data demonstrating that nuclease-deactivated, enhanced-Cas12a from Acidaminococcus species (enAsdCas12a; Kleinstiver et al., 2019) is also sensitive to the effects of high-GC spacers (Fig. 3J). This poor performance was largely rescued by including a TTTT synSeparator derived from the natural AsCas12a separator.

Furthermore, we have now included a paragraph in the Discussion where we speculate on why the effect of adding the synSeparator was more modest for the endogenous genes than for GFP: 1) Our GFP-expressing cell line has multiple GFP insertions in its genome, and each copy has seven protospacers in its promoter. This may amplify the effect of the synSeparator. 2) The gRNAs used for endogenous activation were taken from the literature or had been pre-tested by us. These guides had thus already proven to be successful and might not be particularly disruptive (e.g., they were not selected by us for having high GC content). Therefore, researchers might experience the greatest benefit from the synSeparator with newly designed spacers that have not already proven to be effective even without the synSeparator.

Reviewer #3 (Public Review):

Magnusson et al., do an excellent job of defining how the repeated separator sequence of Wild Type Cas12a CRISPR arrays impacts the relative efficacy of downstream crRNAs in engineered delivery systems. High-GC content, particularly near the 3' end of the separator sequence appears to be critically important for the processing of a downstream crRNA. The authors demonstrated naturally occurring separators from 3 Cas12a species also display reduced GC content. The authors use this important new information to construct a synthetic small separator DNA sequence which can enhance CRISPR/Cas12a-based gene regulation in human cells. The manuscript will be a great resource for the synthetic biology field as it shows an optimization to a tool that will enable improved multi-gene transcriptional regulation.

Strengths:

• The authors do an excellent job in citing appropriate references to support the rationale behind their hypotheses.
• The experiments and results support the authors' conclusions (e.g., showing the relationship between secondary structure and GC content in the spacers).
• The controls used for the experiments were appropriate (e.g., using full-length natural separator vs single G or 1 to 4 A/T nucleotides as synthetic separators).
• The manuscript does a great job assessing several reasons why the synthetic separator might work in the discussion section, cites the relevant literature on what has been done and restates their results to argument in favor or against these reasons.
• This paper will be very useful for research groups in the genome editing and synthetic biology fields. The data presented (specially the data concerning the activation of several genes) can be used as a comparison point for other labs comparing different CRISPR-based transcriptional regulators and the spacers used for targeting.
• This paper also provides optimization to a tool that will be useful for regulating several endogenous genes at once in human cells thus helping researchers studying pathways or other functional relationships between several genes.

Opportunities for Improvement:

• The authors have performed all the experiments using LbCas12a as a model and have conclusively proven that the synSeparator enhances the performance of Cas12a based gene activation. Is this phenomenon will be same for other Cas12a proteins (such as AsCas12a)? The authors should perform some experiments to test the universality of the concept. Ideally, this would be done in HEK293T cells and one other human cell type.

We thank the reviewer for these suggestions. We have now addressed the generalizability of our findings with several new experiments. First, we now include data demonstrating that nuclease-deactivated, enhanced Cas12a from Acidaminococcus species (denAsCas12a; Kleinstiver et al., 2019) is also sensitive to the effects of high-GC spacers (Fig. 3J). This poor performance was largely rescued by including a TTTT synSeparator derived from the natural AsCas12a separator.

Second, we now include data demonstrating that the beneficial effect of adding a synSeparator is not limited to the AAAT sequence derived from the Lachnospiraceae b. separator. We now include three other 4-nt, AT-rich synSeparators derived from Acidaminococcus s. (TTTT), Moraxella b. (TTTA) and Prevotella d. (ATTT) (Fig. 3I). All these synSeparators rescued the poor GFP activation caused by an upstream spacer with high GC content, though not equally effectively. The quantitative difference between the synSeparators could either be due to the intrinsic “insulation capacity” of these sequences, or the way they interact with the Lb-Cas12a protein, or to sequence-specific interactions with this particular CRISPR array. We discuss these possibilities in the Discussion.

Third, as described above, we have now performed an in vitro Cas12a cleavage assay and present the data in a new figure (Fig. 4). We found that a CRISPR array containing a 70%-GC dummy spacer was processed less efficiently than an array containing a 30%-GC spacer, but that addition of a synSeparator could to a large extent rescue this processing defect (Fig. 4E). The fact that this result was observed even in a cell-free in vitro setting demonstrates that it is a general feature of Cas12a CRISPR arrays that is likely to work the same way in many cell types rather than being specific to HEK293T cells.

Fourth, we attempted to investigate the effect of the synSeparator in different cell types. However, either due to poor transfection efficiency or poor expression of the Cas12a activator construct, CRISPRa activity was consistently poor in these cell types, both with and without the synSeparator (e.g., we did not visually observe fluorescence from the mCherry gene fused to the dCas12a activator, which we always see in HEK293T cells). Because of the low general efficiency of CRISPRa, it was not possible to evaluate the performance of the synSeparator. Many cell types are difficult to transfect and dCas12a-VPR-mCherry is a big construct (>6 kb). To our knowledge, there have not been many reports using dCas12a-VPR in cell types other than HEK293T. While we think that it will be important to optimize CRISPRa in many cell types (e.g., by optimizing transfection conditions, Cas12a variants, promoters, expression vectors, etc.), the focus of our study has been to show the separator’s mechanism and general function; we believe that optimizing general CRISPRa for different cell types is beyond the scope of this paper. We acknowledge that this is a limitation of our study and we have added a paragraph about this in the Discussion (line 355). We nevertheless hypothesize that the negative influence of high-GC spacers and the insulating effect of synSeparators are generalizable across cell types. That is because we could observe improved array processing with the synSeparator even in the cell-free context of an in vitro expression system, as described above (Fig. 4). This suggests that the sensitivity to spacer GC content is determined only by the interaction between Cas12a and the array, rather than being dependent on a particular cellular context.

Author Response

Reviewer #1 (Public Review):

However, the authors are cautioned to tone down some of the sentences with the human diabetic samples as they rely heavily on extrapolation rather experimental tests.

Thank you for this feedback. We have added an experimental test to support the CellChat results. We found that, in accordance with the CellChat analysis, more macrophage Gas6 expression is observed in diabetic wounds via IF. These data are now included in Figures 3C-D. We have additionally edited the text relating to Figure 3 to indicate that these results are not fully conclusive.

For instance, the antibody inhibition of Axl had minimal effect on the clearance of apoptotic cells in the wound and this would be expected with the redundancy endowed by other TAM receptors.

Thank you for this point. We have made a note of this in the text in lines 289-291.

For instance, in Figure 6, the number of TUNEL+ cells seem to be higher in the IgG samples compared to the anti-Timd4 treatment, but this is not the case in the quantification

Thank you for this comment. We have replaced these with more representative images, which appear in Figure 6A. We also repeated the staining with antibodies for cleaved caspase 3, which appear in Fig. 6 – Fig. supplement 1A, which showed similar results.

Reviewer #2 (Public Review):

I suggest to repeat the quantification of cells containing active caspase-3 with an anticleaved caspase-3 antibody. Here the authors use an antibody recognizing phospho S150 antibody, which is far from generally accepted to be a marker for active caspase-3. It would also be good to quantify the apoptotic cells observed in the sections (Fig 1 I and J) and compare to control treatment on sections. It is not clear from the data presented whether the number of apoptotic cells increases or not in the time frame analyzed since the controls are lacking.

Thank you for this important suggestion. We have repeated the IF staining using an antibody for cleaved caspase 3 (Cell Signaling 9661S) and quantified the apoptotic cells present. We found that apoptotic cells were rare but present at both 24h and 48h after injury, and that significantly more cleaved caspase 3+ cells were present in 48h wounds than 24h wounds. These data are now included in Figure 1H-J and Fig. 1 – Fig. supplement 1F. We have also used this antibody in IF staining in Fig. 5 – Fig. supplement 1B and Fig. 6 – Fig. supplement 1A.

In a FACS analysis (Fig S1 H), the authors show that there is no increase in dead cells in a time frame of 48 hrs. Could it be that the majority of the cells that may have died in vivo, were lost during the procedure of tissue digestions. Dead cells tend to aggregate.

Based on these comments and the inconsistency in these data due to potential technical challenges, we have removed the FACS data quantifying Annexin V. We now include the quantification of cleaved caspase 3 and an efferocytosis assay to analyze the kinetics of efferocytosis.

On line 104 the authors refer to the apoptosis-inducing activity of G0s2. Please, realize that there is little or no in vivo evidence for a role of G0s2 in apoptosis.

Thank you for this helpful comment. We have removed this gene from our analysis and text.

The authors state that Axl is uniquely expressed in DC and fibroblasts (Fig 2). Are the Axlcells positive in panel G (red, Fig 2) that do not stain for the Pdgfra marker (green) then all DCs? Please clarify or show with a triple staining that these cells are indeed DCs.

Thank you for this comment. To clarify, our intention was to show that both DCs and fibroblasts express Axl, not to say conclusively that only DCs and fibroblasts express Axl. Indeed, in Figure 5, we show that a portion of macrophages also express Axl (at day 3), so some of the Axl+ cells in 2G may be macrophages rather than DCs. We have made this more clear in the text in lines 163-166.

In addition, it is not clear to me to what reference level exactly the expression levels are compared in Fig 2A. Is this between the 24 and 48h time points after wounding (as mentioned in the legend)? If so, the analysis may indicate up or down regulation but not necessarily expression or no expression.

Thank you for making this point. The heatmaps display scaled log-normalized mRNA counts for the entire dataset, not a comparison between the two timepoints. We have clarified this in the figure legends.

2) Human diabetic wounds display increased and altered efferocytosis signaling via Axl. This conclusion is solely based on CellChat analysis and should be tuned down or validated.

Thank you for this suggestion. We have experimentally validated this conclusion using IF staining for Gas6. We found that more Gas6 staining in CD68+ macrophages in diabetic foot ulcers when compared to nondiabetic foot wounds. These data are now included in Figure 3C-D.

The authors conclude that anti-Axl treatment leads to healing defects based on lack of granulation tissue and larger scabs, a reduction of fibroblast repopulation and revascularization. The differences in the last two parameters mentioned above are obvious, however the other parameters, as granulation tissue and scabs are less clear to me. Is this quantified in any way? In Fig S4 D there is also a large scab visible in the control treatment image. Therefore, it would be good if these parameters could be better substantiated.

Thank you for this comment. We have edited the text in lines 301-304 to de-emphasize these qualitative changes.

In view of the lack of revascularization, are there differences in the mRNA expression levels of angiogenic factors such as VEGF and others at this time point? Does revascularization occur at later stages?.

Thank you for this helpful suggestion. We have used qPCR to measure Vegfa mRNA expression, and these data are now included in Figure 5I. We found no significant difference in Vegfa expression 5 days after injury.

Based on the FACS analysis the authors claim that there are no differences at the level of DCs. However, the plots shown in Fig 5C do not convincingly show the detection of DC (as boxed in the lower panel). Based on the density plots one would presume this is just the continuation of the CD11b+ population and not a separate CD11c+ population. To get a better view of that, it would be better to show dot plots instead of density plots.

Thank you for this insightful comment. We have created new plots as suggested to demonstrate that this is not exactly the case. In the wound bed, contrary to what we see in blood isolates many times the full separation of populations is elusive and to ensure that we use single stain controls to set the gates. Nonetheless, we provide in Author response image 1 the same data as dot-plots as requested to show that that is not the case, alongside the single stain control to show that the gating strategy is adequate. We do understand and acknowledge that in dissociated tissues sometimes the outlines are not as perfect as what is obtained in immunological samples.

Author response image 1.

Finally, the authors state (line 265-266) that anti-Axl treatment leads to non-significantly increased expression of IL1alpha and IL6 after one day of injury (Fig S4C). If the difference between the control-treated and the anti-Axl-treated group is statistically not significant I would not conclude there is an increase. Please adapt phrasing or include more mice in the experiment (now only 4) to substantiate the observation and clarify whether it is increased or not.

Thank you for this comment. We have altered the text in lines 286-289 to better reflect this.

The authors conclude that overall healing was not affected but that the wound beds appeared more fragile. What is meant with 'appeared more fragile' is not clear. In addition, this seems to me a quite subjective interpretation. What are the objective parameters to come this conclusion?

Thank you for this point. We have altered the text to remove this subjective language.

Similar to inhibition of Axl, inhibition of Timd4 led to a defect in revascularization as witnessed by the absence of CD31 staining. Also in this experiment one can raise similar questions as in the anti-Axl experiment: 1) does revascularization occur at a later timepoint; 2) what about the expression of angiogenic factors?

Thank you for this helpful suggestion. To further investigate the impact of Axl inhibition of angiogenesis, we have assayed for Vegfa by qPCR. We found no significant difference in Vegfa expression 5 days after injury. These data are now included in Figure 5I.

In the anti-Timd4 treated wounds the authors observe more TUNEL-positive cells and conclude that this is due to a defect in efferocytosis. However, the formal experimental proof for this in the current model is lacking. How do the authors exclude the possibility that anti-Timd4 treatment attracts more infiltrating cells that then undergo treatment, or that the treatment with anti-Timd4 leads to more apoptosis of certain cells in the wound bed. What is the nature of these apoptotic cells (neutrophils, T cells, others)? It has been shown that Timd4 can have stimulatory effects on other cells, such as T cells. Could deprivation of Timd4 signaling in certain conditions lead to more dying cells in this model?

Thank you for this insightful comment. To investigate this, we have repeated this experiment with IF staining for cleaved caspase 3 and found similar results, indicating the increase in apoptosis upon Timd4 inhibition (Fig. 6 – Fig. supplement 1A). We have also included text to acknowledge the possibility of an increase in apoptosis in lines 326-327.

Reviewer #3 (public Review)):

They never do show that there is an increase in apoptotic cells in the wounds, which then go down (which would be a sign that the cells are being cleared via efferocytosis. In addition, they are looking for apoptotic cells at very early time points (24-48 hours), times at which large numbers of apoptotic cells would not be expected. As an example, neutrophil infiltration peaks at 24-48 hours and efferocytosis of apoptotic neutrophils would be expected after that. Other types of apoptotic cells would likely be cleared even later. Finally, several of the panels showing apoptotic cells were done with a very small number of samples (1-3 per group) in some cases so it is unclear how rigorous the data are. I would recommend that the authors at the very least soften the wording related to these conclusions and discuss the limitations of their experimental design; ideally data from more samples would be included to provide clear support those statements.

Thank you for raising this important point. In order to support these claims, we have undertaken two additional experiments. Firstly, we have repeated the immunofluorescence staining with a new antibody for activated caspase 3 and quantified the number of apoptotic cells present in 24h and 48h wound beds. We found that apoptotic cells significantly increased in 48h wound beds compared to 24h wounds (Figures 1H and Fig. 1 – Fig. supplement 1F).

We have also undertaken a new experiment to show the temporal regulation of efferocytosis. We injected stained apoptotic neutrophils into 1D, 3D, and 5D wound beds and quantified the stained cells remaining after 1 hour in order to quantify the clearance of cells from the wound bed at different timepoints. We found that significantly more stained cells undergoing efferocytosis remained in 5D wounds, and that the rate of efferocytosis was approximately constant over this timeline. These data are now included in Figures 2H-M.

While we would be interested to determine the identities of cells engaging in efferocytosis of the labeled apoptotic neutrophils, we found that co-staining for additional cell markers was impossible while maintaining the fluorescent labeling on the injected neutrophils.

2) The human RNA-seq data is also quite limited, as non-diabetic wound tissue was all from one patient. Again, this limitation should be acknowledged.

Thank you for this feedback. We have analyzed new data sets that include 5 individuals with diabetic foot ulcers and 4 individuals with non-diabetic wounds. These data are now included in Figure 3.

Also, there are some important published papers by Sashwati Roy's group indicating that there are defects in efferocytosis in diabetic wounds, which may go against what the authors are showing here to some degree. Discussion of the authors' work in relation to these other studies should be discussed.

Thank you for this suggestion. We have included discussion of this work to the text in lines 192193.

3) For anti-Axl and anti-Timd4 experiments, the authors conclude that inhibition of Axl does not affect TUNEL+ cells and that Timd4 does not affect reepithelialization. However, in some cases the sample size was only 3 mice per group when measuring these parameters. That is a very small number of samples to draw conclusions about apoptotic cells or reepithelialization since these parameters are key for the overall conclusions of the experiments. Given that these are key data, it would be important to include more than n=3. Additionally, as stated above, a time point later than 24 h may be necessary to actually see changes in apoptotic cells.

Thank you for this suggestion. We have repeated the staining for apoptotic cells using a new antibody for cleaved caspase 3 and stained wound beds from additional mice. In the anti-Axl experiments, we now show data for cleaved caspase 3 staining of 3- and 5-day wound beds with N=4 (Fig. 5 – Fig. supplement 1B). In the anti-Timd4 experiments, we now have N=6-11 for the TUNEL staining at 5 days after injection and injury (Figure 6B).

4) In Fig 6, there look to be many more TUNEL+ cells in the wound bed of IgG control samples compared to anti-Timd4-treated samples, which contradicts the graph. Perhaps the authors could clarify where they were taking their measurements for panels with image analysis results.

Thank you for this helpful point. We have updated this figure to be more representative of the quantification (Figure 6A-B), as well as repeated the staining with antibodies for cleaved caspase 3 (Fig. 6 – Fig. supplement 1A).

Another question related to this experiment is how it is possible that efferocytosis is so drastically different yet there are no changes in wound healing (this is one reason why a larger sample size for reepithelialization may be critical) - this would seem to suggest that efferocytosis is not important in wound healing, which is confusing. Further discussion on this might be useful.

Thank you for this point. Indeed, we see that there is a defect to revascularization when Timd4 is inhibited (Figure 6E-F), which indicates that efferocytosis is important to normal healing. This is discussed in lines 333-335.

Author Response:

Reviewer #1:

In this ms, Voroslakos et al., describe a customizable and versatile microdrive and head cap system for silicon probe recordings in freely moving rodents (mice and rats). While there are similar designs elsewhere, the added value here is: a) a carefully designed solution to facilitate probe recovery, thus reducing experimental costs and favoring reproducibility; b) flexibility to accommodate several microdrives and additional instrumentation; c) open access design and documentation to favor customization and dissemination. Authors provide detailed description to faccilitate building the system.

Personally, I found this resource very useful to democratize multi-site recordings, not only for standard silicon probes, but also more novel integrated optoelectrodes and neuropixels. While there are other solutions, this design is quite simple and versatile. A potential caveat is whether it could be perceived as just an upgrade, given some similitudes with previous designs (e.g. Chung et al., Sci Rep 2017 doi: 10.1038/s41598-017-03340-5) and concepts (Headley et al., JNP doi: 10.1152/jn.00955.2014). However, the system presented in this paper provides added value and knowledge-based solutions to make silicon probe recordings more accessible.

We thank the reviewer for carefully reading our manuscript and providing useful and constructive comments.

Reviewer #2:

This manuscript provides an updated guide on the procedures for performing chronic recordings with silicon probes in mice and rats in the lab of the senior author, who is one of the leaders in the use of this experimental method. The new set of procedures relies on metal and plastic 3D printed parts, and represents a major improvement over the older methodology (i.e. Vandecasteele et al. 2012).

The manuscript is clearly written and the technical instructions (in the Methods section) seem rather detailed. The main concerns I had are as follows.

We thank the reviewer for carefully reading our manuscript and providing useful and constructive comments.

1) The present design is an improvement over Chung et al. (the most similar previously published explantable microdrive design, as far as I am aware) in terms of the footprint and travel distance. However, a main disadvantage of the system in its present form is that (apparently) it does not support Neuropixels probes. While such probes might not be suitable for some uses (e.g. to record from large populations in dorsal hippocampus), Neuropixels probes are of considerable interest to many labs.

Our microdrive and head cap system can also support Neuropixels probes. Since our initial submission, we have implanted a Neuropixels probe in the intermediate hippocampus of a rat using our recoverable, plastic microdrive. At the end of the experiment, the Neuropixels probe was successfully recovered, cleaned, and implanted again in a new rat. In addition, we designed a new arm for our metal microdrive which can support Neuropixels probes (Figure 2) and implanted another rat (Figure 3 and 4). We have also created a video showing how to attach Neuropixels probe to a metal microdrive (Suppl. Video 3).

Figure 2. Metal microdrive adapter for Neuropixels probe. A Arm design for 64-channel silicon probes. 45o, front, side and top views are shown (from left to right). All dimensions are in mm. B Changing the overall length (from 7.35 mm to 10 mm) and width (from 4 mm to 5.4 mm) of the 64-channel arm makes our metal microdrive compatible with Neuropixels probe. Note, that only three dimensions of the 64-channel arm were modified (red numbers). 45-degree, front, side and top views are shown (from left to right). All dimensions are in mm. C Photograph of the different arm designs of the metal, recoverable microdrive (top shows an arm designed for a 64-ch silicon probe, bottom shows an arm designed for Neuropixels probe).

Figure 3. Recording of unit firing with Neuropixels probe attached to a metal microdrive in freely moving rat. A Metal microdrive for Neuropixels probe (a – stereotax attachment, b – drive holder, c – metal microdrive, d – Neuropixels probe and e – Neuropixels headstage). B Photo of Neuropixels probe attached to a metal microdrive (a-e same as in A). C Location of probe implantation (Bregma - 4.8 mm, mediolateral + 4.6 mm, 11-degree angle). D High pass filtered traces (1s) from a freely moving rat implanted with Neuropixels probe. Note the single unit activity in the cellular layer of cortex (top) and hippocampus (bottom).

Figure 4. Implantation of Neuropixels probe in a rat using metal microdrive and rat cap system. A The base of the rat cap is attached to the skull. Reference (ref) and ground (gnd) screws are placed over the cerebellum. Neuropixels probe is mounted on a metal microdrive. The microdrive is held by the drive holder and attached to a stereotax arm using the stereotax attachment. For more details, see video: Neuropixels_attachment.mp4. B Once the probe is inserted to its final depth (left), the base of the microdrive is cemented to the skull (zoomed in photograph on the right). C The surface of the brain is kept wet using saline during probe insertion and during cementing the base of the microdrive. D After the base is cemented, the craniotomy is sealed with bone wax. E Releasing the drive from the drive holder. Once it is released the stereotax arm is moved upwards. F Neuropixels headstage is removed from the male header of the stereotax attachment (soldering joint) and placed on the animals back. G The walls of the cap system are attached to the base. Ground and reference wires are soldered to the probe (not shown). H The male header of the headstage is secured to the walls. The headstage and its cable are oriented to allow easy access to the screw head of the microdrive. Note, that there is enough room for custom connectors inside the rat cap.

2) The total weight of the mouse implant seems quite high (together with the headstage, I estimate it is >= 4gr). Could the authors provide the exact value, and describe whether this has any impact on the way the animal moves? Also, the authors should describe how the animals are housed (e.g. do they carry the headstage even when not being recorded). The authors say that a mouse can be implanted with more than one microdrive. The authors should clarify whether they actually have an experience with such implants, or is this just a suggestion based on their educated estimate?

The total weight of the metal microdrive, including the base, body and arm is 0.87 gram. Additional weight is the metabond and dental acrylic cement. The amount of cement that is used during surgery can vary between researchers and the type of surgery. The overall weight of the assembly also depends on the silicon probe with Omnetics connector(s) that is used for the surgery, e.g.: 32-channel micro-LED probe is 1.11g (NeuroLight Technologies LTD.), 64-channel 4-shank probe is 0.96g (ASSY E-1, Cambridge NeuroTech), 64-channel 5-shank probe is 1.05g (A5x12- 16-Buz-Lin-5mm, NeuroNexus Ltd.) and a 128-channel 4-shank probe with integrated Intan chips is 0.94g (P128-5, Diagnostic Biochips). In addition, the overall weight of the entire assembly can change if optic fibers are used in optogenetic studies or if any custom connectors are implanted (e.g., connector and wires for brain stimulation). That is the reason why we reported the overall weight of each system (metal microdrive, mouse cap and rat cap) individually.

The implanted mice are single housed, and they do not carry the headstage while in the vivarium. During recordings, the headstage is attached and a counterbalanced pulley system ensures that the animal is not carrying the extra weight of the headstage. We have quantitatively compared running speed with traditional and the new head caps in both rats and mice (Fig. 6).

The small footprint of the metal microdrive enables researchers to perform more than one silicon probe implantation in freely moving mice. For this purpurse, larger mice (>35 g) are selected (Figure 5).

Figure 5. Metal microdrive enables double silicon probe recordings in freely moving mice. A Intraoperative photograph of double silicon probe implantation. Note that the metal microdrive on the left had been secured to the skull and the second drive is being implanted using the stereotaxic attachment and drive holder. The probe PCBs are placed on the copper mesh. B Photograph focused on the metal microdrives.

3) There is no information in the results section on the number of implants performed, the duration the animals were implanted, the quality of the recordings obtained, number of successes or failures failures. The figures merely provide examples of one successful recording in a mouse and in a rat. All these details should be provided, along with details of how many probes were reused and how many times (a brief mention of one case, lines 252-253 and 359-360, is not sufficient).

We have added a Supplementary Table explaining all the details of our implants. We would like to refer the Reviewer to response #1 to Reviewer 1.

Adapting new technology is challenging. To date, we have extensive experience with the rat cap system only (n=3 users in the lab, n = 25 rats implanted). Two lab members have started to adapt our mouse cap and implanted 3 mice since our submission. We included their maze running behavioral data for comparison between the copper mesh and cap system.

Prior to the development of the metal microdrive, we have conducted an internal lab survey comparing the hand-made microdrive (Vandecasteele et al., 2012) and our recoverable, plastic microdrive. Six lab members who had extensive experience with both types participated (Figure 6). Our questions were:

1) On a scale 1-10, how would you compare the plastic, recoverable drive to the Vandecasteele et. al. 2012 one in terms of: a) ease of building a drive, b) size and c) ease of recovery.

Figure 6. Internal lab survey using recoverable, plastic microdrives. A User feedback based on four criteria: ease of building, ease of implantation, size, ease of recovery. The 3D printed microdrive surpasses the manually built drive (Vandecasteele et. al., 2012) on every parameter except the size. B 24 silicon probes were used with the recoverable plastic microdrive. On average each probe was recovered two times. Out of these 48 recovery attempts 5 failed only. There were 2 total losses during recovery and in three cases different number of shanks broke during the recovery process making the recovery partially successful. One major limitation of reusability is the sudden increase in impedance over time (we have to discard 30% of the successfully recovered probes due this reason). Researchers in our lab spend on average 30 minutes to recover a silicon probe.

Overall, the success rate of recovery is much higher using a recoverable microdrive system, but the size of the plastic, recoverable microdrive is limits certain experiments. This was one of the main motivations to develop the metal, recoverable microdrive.

4) In fig. 2, spike waveforms are classified as pyramidal, wide or narrow interneurons. I did not find any description of how this classification was performed.

We have removed the single cell putative cell types from the manuscript as this issue is not relevant to the current manuscript. Figure 2 has been simplified and a new figure 5 is dedicated to the single cell quantification.

5) Also in fig. 2, refractory period violations are reported in percent (permille in fact). First, it is not clear how refractory period was defined. Second, such quantification is incorrect in principle: we use refractory period violations to infer the rate of false positives. Yet the relationship between fraction of ISI violations and false positive rate depends on the firing rate of the neuron. For example, 0.1% of ISI violations is quite good for a unit spiking at 10 spikes/s, is so so for a unit spiking at 1 spike/s, and is very bad if the firing rate is 0.1 spike/s (see Hill et al. JNeurosci. 2011 for derivation). Alternatively, the authors can follow an approach described in an old paper by the same lab (Harris et al., JNeuropsysiol. 2000), quantifying the violations in spike autocorrelogram relative to its asymptotic height.

We have removed this panel from Fig. 2 and dedicated a new figure (Fig. 5) to the single cell quantification. Refractory violations can be used as an alarm for poor cluster quality. Absence of refractory violations alone does not guarantee good separation for the reasons the Reviewer mentioned.

6) Line 477: the authors write that the probes were mounted on a plastic microdrive. This seems to contradict the key claim of the manuscript (namely that the microdrives were from stainless steel).

We apologize if this description was not clear in the original manuscript. In the revised version, we have added a table (Suppl. Table 1) explaining all details of each animal subject (species, strain, weight, cap type), type of silicon probe and microdrive used. As we explained in Response 3, our main goal was to test each system individually and once all components have been verified, we combined everything into one surgery.

The plastic and metal microdrives are based on the same principles. The implantation/recovery tools are also identical in design concepts. Based on our own experience, users dol not recognize any changes in terms of ease of use, ease of implantation and ease of recovery when changing from plastic recoverable microdrives to metal ones. The advantage of metal drives is size reduction, their multiple reusability and stability.

7) I believe that the work of Luo & Bondy et al. (eLife 2020) and should be references and compared to.

We reference Luo et. al. (2020) in our revised manuscript. One of the main advantages of using a microdrive system is the ability to move the recording probe inside the brain tissue and sample new sets of neurons. This is not the case in Luo & Bondy et al. (eLife 2020).

Author Response:

Reviewer #1 (Public Review):

Summary

The authors have discovered and characterized a novel genetic pathway responsive to hypoxia, which acts in parallel to the canonical response through activation of Hypoxia-Inducible Factor (HIF). Specifically, the authors discovered that the Caenorhabditis elegans nuclear hormone receptor NHR-49, ortholog to mammalian PPAR-alpha, is essential for survival under hypoxic conditions and regulates target gene expression that is hif-1-independent; identifying an essential role of autophagy. Further the authors discover both positive and negative regulators of NHR-49 and a putative feedback loop.

Overall analysis

The genetic analysis conducted by the authors is outstanding. However, the study is lacking in a few key areas and the authors may have over-interpreted results in a few places, which diminishes my overall enthusiasm. These concerns are addressable and doing so would greatly strengthen the manuscript. I highlight individual major concerns below, and save minor concerns and specific suggestions for private recommendations for the authors.

Major concerns

1 The authors have provided strong genetic evidence for a parallel mechanism to canonical HIF-1 activity in response to hypoxia. The authors should more rigorously test whether there is evidence for cross-talk between the two mechanisms. In the discussion the authors' highlight findings in mammals that support this possibility. For example, does loss of one lead to hyperactivation of the other in an attempt to compensate for hypoxia?

We thank the reviewer for suggesting these interesting experiments to examine cross-talk!

Specific examples:

• In regards to lines 425-426, does loss of hpk-1 stabilize HIF-1 (or does hpk-1(oe) repress hif-1)?

We attempted to study HPK-1–HIF-1 cross talk via GFP imaging of the UL1447 HIF-1::GFP strain after hpk-1 RNAi (Figure R4, below). However, although we did observe an increase in GFP levels in hypoxia (vs. normoxia), we did not observe nuclear localization, possibly due to the rapid degradation of HIF-1 in normoxia, which occurs inevitably during our experimental procedure. We therefore opted not to include these data in the manuscript.

Figure R4: Regulation of HIF-1::GFP. Quantification of GFP levels in UL1447 (unc-119(ed3) III; leEx1447 [hif-1::GFP + unc-119(+)) adult animals expressing HIF-1::GFP. Animals were fed EV RNAi or nhr-49, hif-1, hpk-1, or nhr-67 RNAi as indicated and exposed to 4 hr of 0.5% O2 without recovery (three repeats totalling >30 individual animals per strain). X/, XXX,**** p <0.05, 0.001, 0.0001 (two-way ANOVA corrected for multiple comparisons using the Tukey method).

• Does loss of hif-1 or nhr-49 alter the expression, stability, or activity of the other (either under normoxic or hypoxic conditions)?

We appreciate the reviewer’s interest in examining the interaction between nhr-49 and hif-1. To address this, we generated an NHR-49::GFP;hif-1(-) strain and analysed it by imaging after exposure to normoxia or hypoxia. Although loss of hif-1 does result in a slight whole-body up-regulation of NHR-49::GFP, this increase was not significant (new Figure 2—figure supplement 1C, D). Higher magnification images did not show a tissue-specific effect in NHR-49::GFP increase in the hif-1(-) background either (new Figure 2D, Figure 2—figure supplement 1E, F). For reasons mentioned above, the HIF-1::GFP;nhr-49(RNAi) experiment was inconclusive.

• Can overexpression of either hif-1 or nhr-49 rescue the developmental defects caused by loss of the other (i.e. overexpress hif-1 in nhr-49 mutant animals, and vice versa).

With the new NHR-49::GFP;hif-1(-) strain, we were able to study compensatory effects of overexpressing NHR-49 in hif-1 mutants by performing embryo hypoxia survival experiments (new Figure 2E). Excitingly, while NHR-49 overexpression does not provide enhanced hypoxia survival at baseline (vs. non-GFP siblings), NHR-49 overexpression rescued the deficiency of hif-1 mutants. This suggests that nhr-49 can partially compensate for loss of the hif-1 pathway. Testing whether HIF-1::GFP overexpression rescues nhr-49 loss requires non-GFP sibling controls. Although the UL1447 strain expresses HIF-1::GFP from an extrachromosomal array, in our hands, we never observed non-GFP worms (i.e. 100% HIF-1::GFP offspring), and therefore were unable to test whether HIF-1 overexpression compensates for nhr-49 loss.

• Does NHR-67 negatively regulate hif-1 (specificity to NHR-49)?

As noted above, we were unfortunately unable to conclusively assessed HIF-1::GFP levels, likely due to rapid degradation during the normoxia that occurs during animal harvest.

2 The role of autophagy in hypoxia should be explored in greater detail. While the evidence presented by the authors clearly demonstrates autophagy is essential for hypoxic survival, autophagy is an important component of many biological processes. Thus, it's critical to distinguish whether autophagy is merely required (perhaps for very indirect reasons) or whether autophagy is a part of an adaptive response to hypoxia. The authors (Miller lab) previously failed to find a role for autophagy in hypoxia (Fawcett et al. 2015 Aging Cell), which should be addressed. Has autophagy been previously linked to hypoxia in C. elegans? The novelty of this discovery should be discussed in greater detail.

We appreciate that the link of autophagy to hypoxia survival needed to be examined further. We now provide substantial new evidence showing that not only are autophagy genes and autophagosome formation induced in hypoxia, but also that mutations in autophagy genes result in hypoxia sensitivity. In our opinion, this strongly supports a key role for autophagy in hypoxia adaptation.

We note that the study by Fawcett et al., 2015 studied only two genes in hypoxia, bec-1 and unc-51, none of which were found to be regulated by hypoxia in our RNA-seq analysis. Another study from the Miller lab found that an 18-hour anoxia exposure of L2/L3 stage C. elegans results in a significant induction of autophagy in the intestine (Chapin et al., 2015; Fig 4B, C). Although the conditions in this study are different than in ours (anoxia vs. hypoxia, exposure time, animal developmental stage), this study, like ours, thus finds that that low oxygen availability induces autophagy. Besides the Miller lab, there are several other publications that show an important role for autophagy in hypoxia adaptation across species (Samokhvalov et al., 2008; Zhang et al., 2008). Especially relevant to our manuscript is a recent paper published while we were revising our manuscript, which shows that autophagy gene induction is HIF-1 independent in Drosophila melanogaster (Valko et al., 2021). This agrees well with our exciting new discoveries. We have revised the text to better discuss this context.

3 The authors have possibly over-interpreted their results in Figure 4B and the possibility that NHR-49 acts cell non-autonomously. The authors speculate that tissue specific genetic rescue by NHR-49 over-expression could indicate the existence of a signaling molecule (line 499). Ectopic over-expression of a transcription factor within one tissue is always tricky to interpret, as it may not be physiologically relevant, which I fear may be the case as rescue is achieved when NHR-49 is over-expressed within any tissue (i.e. there is no specificity). An alternative explanation, which is a more indirect model, is that NHR-49 over-expression shifts metabolism within a tissue to generate metabolites that are released throughout the organism to sustain it during hypoxia.

We thank the reviewer for this excellent point, and agree that indirect action of NHR-49 remains a possibility. We have added discussion to this point in the revised manuscript.

4 As an extension of MC#3, the authors demonstrate that NHR-49 is induced throughout the animal after hypoxia (Figure 5A). Presumably sites of NHR-49 induction (tissues) equates to the sites where nhr-49 is necessary. However, the images within 5A cannot be resolved to identify individual tissues, higher resolution images are necessary and quantification of GFP expression within individual tissues could lend biological insight.

We now provide higher resolution images of NHR-49::GFP in Figure 2D, Figure 2—figure supplement 1E, F.

5 The gene expression analysis is lacking details. For example, the RNA-seq data shown in Figure 3A&B is confusing. The numbers in the text do not match the figure and it is unclear whether the intersection in the Venn Diagram represent inverse relationships (i.e. the proportion of genes that are upregulated in wild-type that are either hif-1 or nhr-49 dependent). Greater detail and explanation is needed, as presented little biological insight can be discerned from the Figure 3A&B. Next, qRT-PCR validation of autophagy gene expression found in Figure 3C should be provided with that result. Lastly, are there existing datasets for changes in gene expression of C. elegans exposed to hypoxia? If so, how do the datasets compare?

We apologize for the confusion and have revised our text describing the RNA-seq analysis as well as the Figure legend. We also provide validation of the RNA-seq data with GFP-reporters and have compared our dataset to a previous study on hypoxia dependent gene regulation in C. elegans.

6 The authors identify a putative negative feedback loop between NHR-67 and NHR-49, and suggest this regulation is at the protein level (Figure 5F,G) based on a translational reporter and not transcriptional regulation based on qRT-PCR results and similar results previously found with hpk-1 (Figures S5A, 7a, and a previous study). However, the authors should more rigorously rule out dynamic changes in expression between tissues that cannot be ascertained by qRT-PCR (i.e. test whether nhr-49p::GFP expression is altered after nhr-67(RNAi) +/- hypoxia.

We agree and have more rigorously studied this interaction.

Author response:

Reviewer #1 (Public Review):

Reviewer #1, comment #1: The study is thorough and systematic, and in comparing three well-separated hypotheses about the mechanism leading from grid cells to hexasymmetry it takes a neutral stand above the fray which is to be particularly appreciated. Further, alternative models are considered for the most important additional factor, the type of trajectory taken by the agent whose neural activity is being recorded. Different sets of values, including both "ideal" and "realistic" ones, are considered for the parameters most relevant to each hypothesis. Each of the three hypotheses is found to be viable under some conditions, and less so in others. Having thus given a fair chance to each hypothesis, nevertheless, the study reaches the clear conclusion that the first one, based on conjunctive grid-by-head-direction cells, is much more plausible overall; the hypothesis based on firing rate adaptation has intermediate but rather weak plausibility; and the one based on clustering of cells with similar spatial phases in practice would not really work. I find this conclusion convincing, and the procedure to reach it, a fair comparison, to be the major strength of the study.

Response: Thanks for your positive assessment of our manuscript.

Reviewer #1, comment #2: What I find less convincing is the implicit a priori discarding of a fourth hypothesis, that is, that the hexasymmetry is unrelated to the presence of grid cells. Full disclosure: we have tried unsuccessfully to detect hexasymmetry in the EEG signal from vowel space and did not find any (Kaya, Soltanipour and Treves, 2020), so I may be ranting off my disappointment, here. I feel, however, that this fourth hypothesis should be at least aired, for a number of reasons. One is that a hexasymmetry signal has been reported also from several other cortical areas, beyond entorhinal cortex (Constantinescu et al, 2016); true, also grid cells in rodents have been reported in other cortical areas as well (Long and Zhang, 2021; Long et al, bioRxiv, 2021), but the exact phenomenology remains to be confirmed.

Response: Thank you for the suggestion to add the hypothesis that the neural hexasymmetry observed in previous fMRI and intracranial EEG studies may be unrelated to grid cells. Following your suggestion, we have now mentioned at the end of the fourth paragraph of the Introduction that “the conjunctive grid by head-direction cell hypothesis does not necessarily depend on an alignment between the preferred head directions with the grid axes”. Furthermore, at the end of section “Potential mechanisms underlying hexadirectional population signals in the entorhinal cortex” (in the Discussion) we write: “However, none of the three hypotheses described here may be true and another mechanism may explain macroscopic grid-like representations. This includes the possibility that neural hexasymmetry is completely unrelated to grid-cell activity, previously summarized as the ‘independence hypothesis' (Kunz et al., 2019). For example, a population of head-direction cells whose preferred head directions occur at offsets of 60 degrees from each other could result in neural hexasymmetry in the absence of grid cells. The conjunctive grid by head-direction cell hypothesis thus also works without grid cells, which may explain why grid-like representations have been observed (using fMRI) in regions outside the entorhinal cortex, where rodent studies have not yet identified grid cells (Doeller et al., 2010; Constantinescu et al., 2016). In that case, however, another mechanism would be needed that could explain why the preferred head directions of different head-direction cells occur at multiples of 60 degrees. Attractor-network structures may be involved in such a mechanism, but this remains speculative at the current stage.” We now also mention the results from Long and Zhang (second paragraph of the Introduction): “Surprisingly, grid cells have also been observed in the primary somatosensory cortex in foraging rats (Long and Zhang, 2021).”

Regarding your EEG study, we have added a reference to it in the manuscript and state that it is an example for a study that did not find evidence for neural hexasymmetry (end of first paragraph of the Discussion): “We note though that some studies did not find evidence for neural hexasymmetry. For example, a surface EEG study with participants “navigating” through an abstract vowel space did not observe hexasymmetry in the EEG signal as a function of the participants’ movement direction through vowel space (Kaya et al., 2020). Another fMRI study did not find evidence for grid-like representations in the ventromedial prefrontal cortex while participants performed value-based decision making (Lee et al., 2021). This raises the question whether the detection of macroscopic grid-like representations is limited to some recording techniques (e.g., fMRI and iEEG but not surface EEG) and to what extent they are present in different tasks.”

Reviewer #1, comment #3: Second, as the authors note, the conjunctive mechanism is based on the tight coupling of a narrow head direction selectivity to one of the grid axes. They compare "ideal" with "Doeller" parameters, but to me the "Doeller" ones appear rather narrower than commonly observed and, crucially, they are applied to all cells in the simulations, whereas in reality only a proportion of cells in mEC are reported to be grid cells, only a proportion of them to be conjunctive, and only some of these to be narrowly conjunctive. Further, Gerlei et al (2020) find that conjunctive grid cells may have each of their fields modulated by different head directions, a truly surprising phenomenon that, if extensive, seems to me to cast doubts on the relation between mass activity hexasymmetry and single grid cells.

Response: We have revised the manuscript in several ways to address the different aspects of this comment.

Firstly, we agree with the reviewer that our “Doeller” parameter for the tuning width is narrower than commonly observed. We have therefore reevaluated the concentration parameter κ_c in the ‘realistic’ case from 10 rad-2 (corresponding to a tuning width of 18o) to 4 rad-2 (corresponding to a tuning width of 29o). We chose this value by referring to Supplementary Figure 3 of Doeller et al. (2010). In their figure, the tuning curves usually cover between one sixth and one third of a circle. Since stronger head-direction tuning contributes the most to the resulting hexasymmetry, we chose a value of κ_c=4 for the tuning parameter, which corresponds to a tuning width (= half width) of 29o (full width of roughly one sixth of a circle). Regarding the coupling of the preferred head directions to the grid axes, the specific value of the jitter σc = 3 degrees that quantifies the coupling of the head-direction preference to the grid axes was extracted from the 95% confidence interval given in the third row of the Table in Supplementary Figure 5b of Doeller et al. 2010. We now better explain the origin of these values in our new Methods section “Parameter estimation” and provide an overview of all parameter values in Table 1.

Furthermore, in response to your comment, we have revised Figure 2E to show neural hexasymmetries for a larger range of values of the jitter (σc from 0 to 30 degrees), going way beyond the values that Doeller et al. suggested. We have also added a new supplementary figure (Figure 2 – figure supplement 1) where we further extend the range of tuning widths (parameter κ_c) to 60 degrees. This provides the reader with a comprehensive understanding of what parameter values are needed to reach a particular hexasymmetry.

Regarding your comments on the prevalence of conjunctive grid by head-direction cells, we have revised the manuscript to make it explicit that the actual percentage of conjunctive cells with the necessary properties may be low in the entorhinal cortex (first paragraph of section “A note on our choice of the values of model parameters” of the Discussion): “Empirical studies in rodents found a wide range of tuning widths among grid cells ranging from broad to narrow (Doeller et al., 2010; Sargolini et al., 2006). The percentage of conjunctive cells in the entorhinal cortex with a sufficiently narrow tuning may thus be low. Such distributions (with a proportionally small amount of narrowly tuned conjunctive cells) lead to low values in the absolute hexasymmetry. The neural hexasymmetry in this case would be driven by the subset of cells with sufficiently narrow tuning widths. If this causes the neural hexasymmetry to drop below noise levels, the statistical evaluation of this hypothesis would change.” In addition, in Figure 5, we have applied the coupling between preferred head directions and grid axes to only one third of all grid cells (parameter pc= ⅓ in Table 1), following the values reported by Boccara et al. 2010 and Sargolini et al. 2006. To strengthen the link between Figure 5 and Figure 2, we now state the hexasymmetry when using pc= ⅓ along with a ‘realistic’ tuning width and jitter for head-direction modulated grid cells in Figure 2H. Additionally, we performed new simulations where we observed a linear relationship (above the noise floor) between the proportion of conjunctive cells and the hexasymmetry. This shall help the reader understand the effect of a reduced percentage of conjunctive cells on the absolute hexasymmetry values. We have added these results as a new supplementary figure (Figure 2 – figure supplement 2).

Finally, regarding your comment on the findings by Gerlei et al. 2020, we now reference this study in our manuscript and discuss the possible implications (second paragraph of section “A note on our choice of the values of model parameters” of the Discussion): “Additionally, while we assumed that all conjunctive grid cells maintain the same preferred head direction between different firing fields, conjunctive grid cells have also been shown to exhibit different preferred head directions in different firing fields (Gerlei et al., 2020). This could lead to hexadirectional modulation if the different preferred head directions are offset by 60o from each other, but will not give rise to hexadirectional modulation if the preferred head directions are randomly distributed. To the best of our knowledge, the distribution of preferred head directions was not quantified by Gerlei et al. (2020), thus this remains an open question.”

Reviewer #1, comment #4: Finally, a variant of the fourth hypothesis is that the hexasymmetry might be produced by a clustering of head direction preferences across head direction cells similar to that hypothesized in the first hypothesis, but without such cells having to fire in grid patterns. If head direction selectivity is so clustered, who needs the grids? This would explain why hexasymmetry is ubiquitous, and could easily be explored computationally by, in fact, a simplification of the models considered in this study.

Response: We fully agree with you. We now explain this possibility in the Introduction where we introduce the conjunctive grid by head-direction cell hypothesis (fourth paragraph of the Introduction) and return to it in the Discussion (section “Potential mechanisms underlying hexadirectional population signals in the entorhinal cortex”). There, we now also explain that in such a case another mechanism would be needed to ensure that the preferred head directions of head-direction cells exhibit six-fold rotational symmetry.

Reviewer #2 (Public Review):

Reviewer #2, comment #1: Grid cells - originally discovered in single-cell recordings from the rodent entorhinal cortex, and subsequently identified in single-cell recordings from the human brain - are believed to contribute to a range of cognitive functions including spatial navigation, long-term memory function, and inferential reasoning. Following a landmark study by Doeller et al. (Nature, 2010), a plethora of human neuroimaging studies have hypothesised that grid cell population activity might also be reflected in the six-fold (or 'hexadirectional') modulation of the BOLD signal (following the six-fold rotational symmetry exhibited by individual grid cell firing patterns), or in the amplitude of oscillatory activity recorded using MEG or intracranial EEG. The mechanism by which these network-level dynamics might arise from the firing patterns of individual grid cells remains unclear, however.

In this study, Khalid and colleagues use a combination of computational modelling and mathematical analysis to evaluate three competing hypotheses that describe how the hexadirectional modulation of population firing rates (taken as a simple proxy for the BOLD, MEG, or iEEG signal) might arise from the firing patterns of individual grid cells. They demonstrate that all three mechanisms could account for these network-level dynamics if a specific set of conditions relating to the agent's movement trajectory and the underlying properties of grid cell firing patterns are satisfied.

The computational modelling and mathematic analyses presented here are rigorous, clearly motivated, and intuitively described. In addition, these results are important both for the interpretation of hexadirectional modulation in existing data sets and for the design of future experiments and analyses that aim to probe grid cell population activity. As such, this study is likely to have a significant impact on the field by providing a firmer theoretical basis for the interpretation of neuroimaging data. To my mind, the only weakness is the relatively limited focus on the known properties of grid cells in rodent entorhinal cortex, and the network level activity that these firing patterns might be expected to produce under each hypothesis. Strengthening the link with existing neurobiology would further enhance the importance of these results for those hoping to assay grid cell firing patterns in recordings of ensemble-level neural activity.

Response: Thank you very much for reviewing our manuscript and your positive assessment. Following your comments, we have revised the manuscript to more closely link our simulations to known properties of grid cells in the rodent entorhinal cortex.

Reviewer #3 (Public Review):

Reviewer #3, comment #1: This is an interesting and carefully carried out theoretical analysis of potential explanations for hexadirectional modulation of neural population activity that has been reported in the human entorhinal cortex and some other cortical regions. The previously reported hexadirectional modulation is of considerable interest as it has been proposed to be a proxy for the activation of grid cell networks. However, the extent to which this proposal is consistent with the known firing properties of grids hasn't received the attention it perhaps deserves. By comparing the predictions of three different models this study imposes constraints on possible mechanisms and generates predictions that can be tested through future experimentation.

Overall, while the conclusions of the study are convincing, I think the usefulness to the field would be increased if null hypotheses were more carefully considered and if the authors' new metric for hexadirectional modulation (H) could be directly contrasted with previously used metrics. For example, if the effect sizes for hexadirectional modulation in the previous fMRI and EEG data could be more directly compared with those of the models here, then this could help in establishing the extent to which the experimental hexadirectional modulation stands out from path hexasymmetry and how close it comes to the striking modulation observed with the conjunctive models. It could also be helpful to consider scenarios in which hexadirectional modulation is independent of grid firing, for example perhaps with appropriate coordination of head direction cell firing.

Response: Thanks for reviewing our manuscript and for the overall positive assessment. The new Methods section “Implementation of previously used metrics” starts with the following sentences: “We applied three previously used metrics to our framework: the Generalized Linear Model (GLM) method by Doeller et al. 2010; the GLM method with binning by Kunz et al. 2015; and the circular-linear correlation method by Maidenbaum et al. 2018.” We have created a new supplementary figure (Figure 5 – figure supplement 4) in which we compare the results from these other methods to the results of our new method. Overall, the results are highly similar, indicating that all these methods are equally suited to test for a hexadirectional modulation of neural activity.

In section “Implementation of previously used metrics” we then explain: “In brief, in the GLM method (e.g. used in Doeller et al., 2010), the hexasymmetry is found in two steps: the orientation of the hexadirectional modulation is first estimated on the first half of the data by using the regressors and on the time-discrete fMRI activity (Equation 9), with θt being the movement direction of the subject in time step t. The amplitude of the signal is then estimated on the second half of the data using the single regressor , where . The hexasymmetry is then evaluated as .

The GLM method with binning (e.g. used in Kunz et al., 2015) uses the same procedure as the GLM method for estimating the grid orientation in the first half of the data, but the amplitude is estimated differently on the second half by a regressor that has a value 1 if θt is aligned with a peak of the hexadirectional modulation (aligned if , modulo operator) and a value of -1 if θt is misaligned. The hexasymmetry is then calculated from the amplitude in the same way as in the GLM method.

The circular-linear correlation method (e.g. used in Maidenbaum et al., 2018) is similar to the GLM method in that it uses the regressors β1 cos(6θ_t) and β2 on the time-discrete mean activity, but instead of using β1 and β2 to estimate the orientation of the hexadirectional modulation, the beta values are directly used to estimate the hexasymmetry using the relation .”

For each of the three previously used metrics and our new method, we estimated the resulting hexasymmetry (new Figure 5 – figure supplement 4 in the manuscript). In the Methods section “Implementation of previously used metrics” we then continue with our explanations: “Regarding the statistical evaluation, each method evaluates the size of the neural hexasymmetry differently. Specifically, the new method developed in our manuscript compares the neural hexasymmetry to path hexasymmetry to test whether neural hexasymmetry is significantly above path hexasymmetry. For the two generalized linear model (GLM) methods, we compare the hexasymmetry to zero (using the Mann-Whitney U test) to establish significance. Hexasymmetry values can be negative in these approaches, allowing the statistical comparison against 0. Negative values occur when the estimated grid orientation from the first data half does not match the grid orientation from the second data half. Regarding the statistical evaluation of the circular-linear correlation method, we calculated a z-score by comparing each empirical observation of the hexasymmetry to hexasymmetries from a set of surrogate distributions (as in Maidenbaum et al., 2018). We then calculate a p-value by comparing the distribution of z-scores versus zero using a Mann-Whitney U test. We use the z-scores instead of the hexasymmetry for the circular-linear correlation method to match the procedure used in Maidenbaum et al. (2018). We obtained the surrogate distributions by circularly shifting the vector of movement directions relative to the time dependent vector of firing rates. For random walks, the vector is shifted by a random number drawn from a uniform distribution defined with the same length as the number of time points in the vector of movement directions. For the star-like walks and piecewise linear walks, the shift is a random integer multiplied by the number of time points in a linear segment. Circularly shifting the vector of movement directions scrambles the correlations between movement direction and neural activity while preserving their temporal structure.”

The results of these simulations, i.e. the comparison of our new method to previously used metrics, are summarized in Figure 5 – figure supplement 4 and show qualitatively identical findings when using the different methods. We have added this information also to the manuscript in the third paragraph of section “Quantification of hexasymmetry of neural activity and trajectories” of the Methods: “Empirical (fMRI/iEEG) studies (e.g. Doeller et al., 2010; Kunz et al., 2015; Maidenbaum et al., 2018) addressed this problem of trajectories spuriously contributing to hexasymmetry by fitting a Generalized Linear Model (GLM) to the time discrete fMRI/iEEG activity. In contrast, our new approach to hexasymmetry in Equation (12) quantifies the contribution of the path to the neural hexasymmetry explicitly, and has the advantage that it allows an analytical treatment (see next section). Comparing our new method with previous methods for evaluating hexasymmetry led to qualitatively identical statistical effects (Figure 5 – figure supplement 4).” We have also added a pointer to this new supplementary figure in the caption of Figure 5 in the manuscript: “For a comparison between our method and previously used methods for evaluating hexasymmetry, see Figure 5 – figure supplement 4.”

Author Response:

Reviewer #1 (Public Review):

Two important goals in evolutionary biology are (i) to understand why different species exhibit different levels of genetic diversity and (ii) in each species, what is the evolutionary nature of genetic variants. Are genetic variants mostly neutral, deleterious, or advantageous? In their study, Stolyarova et al. looked at one of the most polymorphic species known, the fungus Schizophyllum commune. They found that in this hyperpolymorphic species, the evolutionary forces that govern and structure genetic variation can be very different compared to less polymorphic species, including humans and flies. Specifically, the authors find that a process known as positive epistasis is quantitatively abundant among genetic variants that alter proteins in S. commune. Positive epistasis happens when a combination of multiple genetic variants is advantageous for the individuals that carry them, even though each isolated variant in the combination is not advantageous or even detrimental on its own. The authors explain that this happens frequently in their hyperpolymorphic species because the very high polymorphism level makes it very likely that the genetic variants will by chance occur together in the same individuals. In less polymorphic species, the variants that are advantageous in combination may have to wait for each other to occur for too long, for the combination to ever happen often enough in the first place.

Overall I had a great time reading the manuscript, and I feel that my understanding of evolution has been advanced on a fundamental level after reading it. However part of the reason why I enjoyed it was having to fill the gaps, answer the riddles left unanswered in the story by the authors.

Strengths:

1) The model, both extremely polymorphic and amenable to haploid cultures, is ideal to address the questions asked.

2) The study potentially represents a very important conceptual advance on the way to better understand genetic variation in general.

3) The interpretations made by the authors of their data are likely the correct ones to make, even though more definitive answers will likely only come from the sequencing of a much larger number of haplotypes, which cannot reasonably be asked of the authors at this point.

Weaknesses:

1) The manuscript does not provide enough information to judge if the synonymous controls that are compared to the nonsynonymous variants are fully adequate. Specifically, I have one concern that the Site Frequency Spectrum (SFS) of the synonymous variants at MAF>0.05 may be very different compared to the SFS of nonsynonymous variants at MAF>0.05. I focus on this because the authors mention page 5 line 3: "The excess of LDnonsyn over LDsyn corresponds to the attraction between rare alleles at nonsynonymous sites". First, it is unclear from this or from the figures at this point in the manuscript what the authors mean by rare alleles, among those alleles at MAF>0.05. This needs to be detailed quantitatively much more carefully. Second, and most importantly, this raises the question of whether or not the synonymous controls have a SFS with many less rare (but with MAF>0.05) alleles, as one may expect if they are under less purifying selection than nonsynonymous variants. This then raises the question of whether or not the synonymous control conducted by the author is adequate, or if the authors need to explicitly match the synonymous control in terms of SFS for MAF>0.05 in addition to the distance matching already done.

We thank the reviewer for this important comment. In page 5 line 3 we meant “the attraction between minor alleles”. In order to avoid confusion between SNPs with low MAF (“rare”) and minor variants at these polymorphic sites (“minor” ) we replaced “rare alleles” with “minor alleles” where appropriate.

The attraction between minor alleles in nonsynonymous polymorphic sites in S. commune holds if we pool all SNPs together, as is shown in Figure 2 - supplementary figure 4. Following the reviewer’s suggestion, we performed an additional analysis of LD between frequency-matched synonymous and nonsynonymous pairs of SNPs. Specifically, for each possible minor allele count and nucleotide distance, we calculated the number of corresponding pairs of nonsynonymous SNPs and subsampled the same number of synonymous SNPs with the same minor allele count and nucleotide distance. Such subsampling with exact matching of both MAFs and distance shows that LDnonsyn is elevated as compared to LDsyn in both S. commune populations (Figure 2 - figure supplement 3 of the revised version of the manuscript).

2) The manuscript is far too succinct on several occasions, where observations or interpretations need to be much more detailed and explained.

We revised the manuscript for clarity, as detailied below.

Reviewer #2 (Public Review):

Stolyarova et al. used a highly polymorphic species, Schizophyllum commune, to explore patterns of LD between nonsynonymous and synonymous mutations within protein-coding genes. LD is informative about interference and interactions between selected loci, with compensatory mutations expected to be in strong positive LD. The benefit of studying this fungal species with large diversity (with pi > 0.1) is that populations are able to explore relatively large regions of the fitness landscape, and chances increase that sets of epistatically interacting mutations segregate at the same time.

This study finds strong positive LD between pairs of nonsynonymous mutations within, but not between genes, compared to pairs synonymous variants. Further, the authors show that high LD is prevalent among pairs of mutations at amino acid sites that interact within the protein. This result is consistent with pairs or sets of compensatory nonsynonymous mutations cosegregating within protein-coding genes.

The conclusions of this paper are largely supported by the data, with some caveats, listed below.

1) With such large pairwise diversity, there are bound to be many deleterious variants segregating at once, and the large levels of interference between them will make selection much less efficient at purging deleterious variants.

We agree that simultaneous segregation of multiple deleterious nonsynonymous variants in the linked locus impedes their elimination by negative selection. However, stronger Hill-Robertson interference cannot result in the observed excess of LDnonsyn. Generally, Hill-Robertson interference decreases LDnonsyn, especially under low recombination rate (Hill and Robertson, 1966; Comeron et al., 2008; Garcia and Lohmueller, 2021). We discuss this in Appendix 2 (Supplementary Note 2 in the old version of the manuscript) and reproduce the effect in simulations.

While the authors argue that balancing selection is needed to account for patterns of haplotype variation they see, widespread balancing selection may not be required in this setting, and soft or partial selective sweeps (either on single mutations or sets of mutations) can also lead to patterns of diversity where a small number of haplotypes are each at appreciable frequency.

Although partial sweeps can indeed elevate LD in the linked locus, they aren’t expected to cause the excess of LDnonsyn observed in the haploblocks. In order to show this, we now simulated partial sweeps with and without epistasis. In the hard sweep model, a new beneficial mutation (s=0.5) was introduced in the population. In the soft sweep model, the beneficial mutation was picked from standing variation: selection coefficient of an initially neutral variant with frequency > 5% was changed to 0.5. In both cases, simulations were stopped when beneficial mutation achieves frequency 0.5. Both hard and soft partial sweeps increase LD as compared to simulations without sweeps (Figure R1A,B below). However, even in the presence of pairwise epistasis they don’t result in LDnonsyn > LDsyn (Figure R1C,D).

Figure R1. Patterns of LD in simulations with partial selective sweeps. Errorbars show the 95% confidence intervals obtained in 100 simulations. Simulation parameters and epistasis models are the same as described in Figure 3 - figure supplement 6.

Additionally, sweeps are expected to decrease nucleotide diversity in the linked region. However, nucleotide diversity within haploblocks observed in S. commune populations isn’t lower than in the non-haploblocks regions (Figure R2), arguing that the observed patterns can’t be caused by selective sweeps.

Figure R2. Nucleotide diversity in haploblocks in S. commune populations. Histograms show nucleotide diversity within haploblocks, solid black line shows the average nucleotide diversity in haploblocks. Dashed line shows the average nucleotide diversity in the non-haploblock regions.

There is also a tension between arguing that balancing selection is widespread and that shared SNPs across populations are expected to arise through recurrent mutation, as balancing selection is known to preserve haplotypes over long evolutionary times. In that section of the discussion especially, I had difficulty following the logic, and some statements are presented more definitively than might be warranted.

Although we find that balancing selection (either negative frequency-dependent selection or associative overdominance) maintains haploblocks for a long time within S. commune populations, haploblocks aren’t conserved between the two populations, as mentioned in the manuscript. Perhaps this is because balancing selection has had ample time to change on such large evolutionary scales (genetic difference between two S. commune populations is > 0.3 dS), making the fraction of identical by descent polymorphisms in the two populations low. Therefore, the SNPs that are shared between populations most probably arise by recurrent mutations, rather than descending from the ancestral population. We now clarify this in the main text.

Meanwhile, correlation of LDs between such shared SNPs in the two populations within genes indicates shared epistatic constraints between these populations. Such correlation is seen not because pairs of SNPs are maintained from the ancestral S. commune population, but because epistatic pairs are more likely to be under high LD in both modern populations.

2) The validations through simulation are somewhat meagre, and I am not convinced that the simulations cover the appropriate parameter regimes. With a population size of 1000, this represents a severe down-scaling of population size and up-scaling of mutation, selection, and recombination rates (if > 0), and it's unclear if such aggressive scaling puts the simulations in an interference/interaction regime far from the true populations.

Scaling was performed according to SLiM3.0 manual in order to impove calculation time for simulations of highly diverse populations. To address the Reviewer’s concern, we now also check that this approach gives the same results as scaling of N instead of μ, as long as we scale selection coefficient s to maintain Ns and simulate for 100N generations to achieve mutation-selection equilibrium. This is indeed the case for 4Nμ up to 0.05 (Figure R3). We didn’t perform simulations for larger 4Nμ because of extremely long calculation time for large N.

Figure R3. Simulations of populations with varying nucleotide diversity scaled by population size or mutation rate. (A) nucleotide diversity, (B) linkage disequilibrium for synonymous (s = 0) and nonsynonymous (2Ns = -1) polymorphisms. In simulations with scaled population size, mutation rate μ = 5e-7 and N is scaled to achieve 4Nμ equal to 0.002, 0.01 and 0.05. In simulations with scaled mutation rate, N = 1000 and μ is scaled accordingly. Simulations are performed for 100N generations. Filled areas show 95% confidence intervals calculated for 50 simulations with 4Nμ = 0.05; 250 simulations with 4Nμ = 0.01 and 1000 simulations with 4Nμ = 0.002.

A selection coefficient of -0.01 also implies 2Ns = -20, whereas Hill-Robertson interference is most pronounced between mutations with 2Ns ~ -1.

We performed additional simulations of evolution in a highly polymorphic population (4Nμ = 0.2) with nonsynonymous mutations under selection coefficient -5e-4 (2Ns = -1) and varying recombination rate. Consistent with the studies showing that the Hill-Robertson interference results in repulsion of deleterious variants (Hill and Robertson, 1966; Comeron et al., 2008; Garcia and Lohmueller, 2021), in our simulations, LDnonsyn is lower that LDsyn for all recombination rates (Appendix 2 - figure 4). We now append these results to Appendix 2.

3) Large portions of the genome (8.4 and 15.9%, depending on the population) are covered by haploblocks, which are originally detected as genomic windows with elevated LD among SNPs. It's therefore unsurprising that haploblocks identified as high-LD outliers have elevated LD compared to other regions of the genome, and the discussion about the importance of haploblocks seemed a bit circular.

Haploblocks are surprising in two ways. Firstly, the existence of haploblocks by itself is indicative of balancing selection allowing two divergent haplotypes to persist within the population for a long time. Secondly, the strongest excess of LDnonsyn over LDsyn is oberved in genes with high LD, i.e. the ones partially or fully falling within haploblock regions (Figure 3). Positive correlation of LD and excess of LDnonsyn indicates that epistasis is more efficient in regions of high LD (haploblocks), so that the strong attraction between nonsynonymous variants observed in S. commune results from interaction between epistasis and balancing selection. We now reformulated the corresponding results section to make this clearer. We also discuss the interaction between balancing selection and epistasis in the discussion section of the manuscript.

4) Finally, the authors observe a positive correlation between Pn/Ps and LD between both synonymous and nonsynonymous mutations. This result is intriguing and should be discussed, but the authors do not comment on this result in the Discussion.

Positive correlation between pn/ps, LD and the excess of LDnonsyn can be caused by multiple mechanisms, such as positive epistasis weakening the action of negative selection on nonsynonymous variants, or differences in the efficiacy of epistatic and non-epistatic selection for alleles under different allele frequency or local recombination rate. We now add the discussion on the interaction between pn/ps, LD and the excess of LDnonyn to the corresponding Results section.

Author Response

Reviewer #1 (Public Review):

This manuscript will interest cognitive scientists, neuroimaging researchers, and neuroscientists interested in the systems-level organization of brain activity. The authors describe four brain states that are present across a wide range of cognitive tasks and determine that the relative distribution of the brain states shows both commonalities and differences across task conditions.

The authors characterized the low-dimensional latent space that has been shown to capture the major features of intrinsic brain activity using four states obtained with a Hidden Markov Model. They related the four states to previously-described functional gradients in the brain and examined the relative contribution of each state under different cognitive conditions. They showed that states related to the measured behavior for each condition differed, but that a common state appears to reflect disengagement across conditions. The authors bring together a state-of-the-art analysis of systemslevel brain dynamics and cognitive neuroscience, bridging a gap that has long needed to be bridged.

The strongest aspect of the study is its rigor. The authors use appropriate null models and examine multiple datasets (not used in the original analysis) to demonstrate that their findings replicate. Their thorough analysis convincingly supports their assertion that common states are present across a variety of conditions, but that different states may predict behavioural measures for different conditions. However, the authors could have better situated their work within the existing literature. It is not that a more exhaustive literature review is needed-it is that some of their results are unsurprising given the work reported in other manuscripts; some of their work reinforces or is reinforced by prior studies; and some of their work is not compared to similar findings obtained with other analysis approaches. While space is not unlimited, some of these gaps are important enough that they are worth addressing:

We appreciate the reviewer’s thorough read of our manuscript and positive comments on its rigor and implications. We agree that the original version of the manuscript insufficiently situated this work in the existing literature. We have made extensive revisions to better place our findings in the context of prior work. These changes are described in detail below.

1) The authors' own prior work on functional connectivity signatures of attention is not discussed in comparison to the latest work. Neither is work from other groups showing signatures of arousal that change over time, particularly in resting state scans. Attention and arousal are not the same things, but they are intertwined, and both have been linked to large-scale changes in brain activity that should be captured in the HMM latent states. The authors should discuss how the current work fits with existing studies.

Thank you for raising this point. We agree that the relationship between low-dimensional latent states and predefined activity and functional connectivity signatures is an important and interesting question in both attention research and more general contexts. Here, we did not empirically relate the brain states examined in this study and functional connectivity signatures previously investigated in our lab (e.g., Rosenberg et al., 2016; Song et al., 2021a) because the research question and methodological complexities deserved separate attention that go beyond the scope of this paper. Therefore, we conceptually addressed the reviewer’s question on how functional connectivity signatures of attention are related to the brain states that were observed here. Next, we asked how arousal relates to the brain states by indirectly predicting arousal levels of each brain state based on its activity patterns’ spatial resemblance to the predefined arousal network template (Goodale et al., 2021).

Latent states and dynamic functional connectivity

Previous work suggested that, on medium time scales (~20-60 seconds), changes in functional connectivity signatures of sustained attention (Rosenberg et al., 2020) and narrative engagement (Song et al., 2021a) predicted changes in attentional states. How do these attention-related functional connectivity dynamics relate to latent state dynamics, measured on a shorter time scale (1 second)?

Theoretically, there are reasons to think that these measures are related but not redundant. Both HMM and dynamic functional connectivity provide summary measures of the whole-brain functional interactions that evolve over time. Whereas HMM identifies recurring low-dimensional brain states, dynamic functional connectivity used in our and others’ prior studies captures high-dimensional dynamical patterns. Furthermore, while the mixture Gaussian function utilized to infer emission probability in our HMM infers the states from both the BOLD activity patterns and their interactions, functional connectivity considers only pairwise interactions between regions of interests. Thus, with a theoretical ground that the brain states can be characterized at multiple scales and different methods (Greene et al., 2023), we can hypothesize that the both measures could (and perhaps, should be able to) capture brain-wide latent state changes. For example, if we were to apply kmeans clustering methods on the sliding window-based dynamic functional connectivity as in Allen et al. (2014), the resulting clusters could arguably be similar to the latent states derived from the HMM.

However, there are practical reasons why the correspondence between our prior dynamic functional connectivity models and current HMM states is difficult to test directly. A time point-bytime point matching of the HMM state sequence and dynamic functional connectivity is not feasible because, in our prior work, dynamic functional connectivity was measured in a sliding time window (~20-60 seconds), whereas the HMM state identification is conducted at every TR (1 second). An alternative would be to concatenate all time points that were categorized as each HMM state to compute representative functional connectivity of that state. This “splicing and concatenating” method, however, disrupts continuous BOLD-signal time series and has not previously been validated for use with our dynamic connectome-based predictive models. In addition, the difference in time series lengths across states would make comparisons of the four states’ functional connectomes unfair.

One main focus of our manuscript was to relate brain dynamics (HMM state dynamics) to static manifold (functional connectivity gradients). We agree that a direct link between two measures of brain dynamics, HMM and dynamic functional connectivity, is an important research question. However, due to some intricacies that needed to be addressed to answer this question, we felt that it was beyond the scope of our paper. We are eager, however, to explore these comparisons in future work which can more thoroughly address the caveats associated with comparing models of sustained attention, narrative engagement, and arousal defined using different input features and methods.

Arousal, attention, and latent neural state dynamics

Next, the reviewer posed an important question about the relationship between arousal, attention, and latent states. The current study was designed to assess the relationship between attention and latent state dynamics. However, previous neuroimaging work showed that low-dimensional brain dynamics reflect fluctuations in arousal (Raut et al., 2021; Shine et al., 2016; Zhang et al., 2023). Behavioral studies showed that attention and arousal hold a non-linear relationship, for example, mind-wandering states are associated with lower arousal and externally distracted states are associated with higher arousal, when both these states indicate low attention (Esterman and Rothlein, 2019; Unsworth and Robison, 2018, 2016).

To address the reviewer’s suggestion, we wanted to test if our brain states reflected changes in arousal, but we did not collect relevant behavioral or physiological measures. Therefore, to indirectly test for relationships, we predicted levels of arousal in brain states by applying the “arousal network template” defined by Dr. Catie Chang’s group (Chang et al., 2016; Falahpour et al., 2018; Goodale et al., 2021). The arousal network template was created from resting-state fMRI data to predict arousal levels indicated by eye monitoring and electrophysiological signals. In the original study, the arousal level at each time point was predicted by the correlation between the BOLD activity patterns of each TR to the arousal template. The more similar the whole-brain activation pattern was to the arousal network template, the higher the participant was predicted to be aroused at that moment. This activity pattern-based model was generalized to fMRI data during tasks (Goodale et al., 2021).

We correlated the arousal template to the activity patterns of the four brain states that were inferred by the HMM. The DMN state was positively correlated with the arousal template (r=0.264) and the SM state was negatively correlated with the arousal template (r=-0.303) (Author response image 1). These values were not tested for significance because they were single observations. While speculative, this may suggest that participants are in a high arousal state during the DMN state and a low arousal state during the SM state. Together with our results relating brain states to attention, it is possible that the SM state is a common state indicating low arousal and low attention. On the other hand, the DMN state, a signature of a highly aroused state, may benefit gradCPT task performance but not necessarily in engaging with a sitcom episode. However, because this was a single observation and we did not collect a physiological measure of arousal to validate this indirect prediction result, we did not include the result in the manuscript. We hope to more directly test this question in future work with behavioral and physiological measures of arousal.

Author response image 1.

Changes made to the manuscript

Importantly, we agree with the reviewer that a theoretical discussion about the relationships between functional connectivity, latent states, gradients, as well as attention and arousal was a critical omission from the original Discussion. We edited the Discussion to highlight past literature on these topics and encourage future work to investigate these relationships.

[Manuscript, page 11] “Previous studies showed that large-scale neural dynamics that evolve over tens of seconds capture meaningful variance in arousal (Raut et al., 2021; Zhang et al., 2023) and attentional states (Rosenberg et al., 2020; Yamashita et al., 2021). We asked whether latent neural state dynamics reflect ongoing changes in attention in both task and naturalistic contexts.”

[Manuscript, page 17] “Previous work showed that time-resolved whole-brain functional connectivity (i.e., paired interactions of more than a hundred parcels) predicts changes in attention during task performance (Rosenberg et al., 2020) as well as movie-watching and story-listening (Song et al., 2021a). Future work could investigate whether functional connectivity and the HMM capture the same underlying “brain states” to bridge the results from the two literatures. Furthermore, though the current study provided evidence of neural state dynamics reflecting attention, the same neural states may, in part, reflect fluctuations in arousal (Chang et al., 2016; Zhang et al., 2023). Complementing behavioral studies that demonstrated a nonlinear relationship between attention and arousal (Esterman and Rothlein, 2019; Unsworth and Robison, 2018, 2016), future studies collecting behavioral and physiological measures of arousal can assess the extent to which attention explains neural state dynamics beyond what can be explained by arousal fluctuations.”

2) The 'base state' has been described in a number of prior papers (for one early example, see https://pubmed.ncbi.nlm.nih.gov/27008543). The idea that it might serve as a hub or intermediary for other states has been raised in other studies, and discussion of the similarity or differences between those studies and this one would provide better context for the interpretation of the current work. One of the intriguing findings of the current study is that the incidence of this base state increases during sitcom watching, the strongest evidence to date is that it has a cognitive role and is not merely a configuration of activity that the brain must pass through when making a transition.

We greatly appreciate the reviewer’s suggestion of prior papers. We were not aware of previous findings of the base state at the time of writing the manuscript, so it was reassuring to see consistent findings. In the Discussion, we highlighted the findings of Chen et al. (2016) and Saggar et al. (2022). Both studies highlighted the role of the base state as a “hub”-like transition state. However, as the reviewer noted, these studies did not address the functional relevance of this state to cognitive states because both were based on resting-state fMRI.

In our revised Discussion, we write that our work replicates previous findings of the base state that consistently acted as a transitional hub state in macroscopic brain dynamics. We also note that our study expands this line of work by characterizing what functional roles the base state plays in multiple contexts: The base state indicated high attentional engagement and exhibited the highest occurrence proportion as well as longest dwell times during naturalistic movie watching. The base state’s functional involvement was comparatively minor during controlled tasks.

[Manuscript, page 17-18] “Past resting-state fMRI studies have reported the existence of the base state. Chen et al. (2016) used the HMM to detect a state that had “less apparent activation or deactivation patterns in known networks compared with other states”. This state had the highest occurrence probability among the inferred latent states, was consistently detected by the model, and was most likely to transition to and from other states, all of which mirror our findings here. The authors interpret this state as an “intermediate transient state that appears when the brain is switching between other more reproducible brain states”. The observation of the base state was not confined to studies using HMMs. Saggar et al. (2022) used topological data analysis to represent a low-dimensional manifold of resting-state whole-brain dynamics as a graph, where each node corresponds to brain activity patterns of a cluster of time points. Topologically focal “hub” nodes were represented uniformly by all functional networks, meaning that no characteristic activation above or below the mean was detected, similar to what we observe with the base state. The transition probability from other states to the hub state was the highest, demonstrating its role as a putative transition state.

However, the functional relevance of the base state to human cognition had not been explored previously. We propose that the base state, a transitional hub (Figure 2B) positioned at the center of the gradient subspace (Figure 1D), functions as a state of natural equilibrium. Transitioning to the DMN, DAN, or SM states reflects incursion away from natural equilibrium (Deco et al., 2017; Gu et al., 2015), as the brain enters a functionally modular state. Notably, the base state indicated high attentional engagement (Figure 5E and F) and exhibited the highest occurrence proportion (Figure 3B) as well as the longest dwell times (Figure 3—figure supplement 1) during naturalistic movie watching, whereas its functional involvement was comparatively minor during controlled tasks. This significant relevance to behavior verifies that the base state cannot simply be a byproduct of the model. We speculate that susceptibility to both external and internal information is maximized in the base state—allowing for roughly equal weighting of both sides so that they can be integrated to form a coherent representation of the world—at the expense of the stability of a certain functional network (Cocchi et al., 2017; Fagerholm et al., 2015). When processing rich narratives, particularly when a person is fully immersed without having to exert cognitive effort, a less modular state with high degrees of freedom to reach other states may be more likely to be involved. The role of the base state should be further investigated in future studies.”

3) The link between latent states and functional connectivity gradients should be considered in the context of prior work showing that the spatiotemporal patterns of intrinsic activity that account for most of the structure in resting state fMRI also sweep across functional connectivity gradients (https://pubmed.ncbi.nlm.nih.gov/33549755/). In fact, the spatiotemporal dynamics may give rise to the functional connectivity gradients (https://pubmed.ncbi.nlm.nih.gov/35902649/). HMM states bear a marked resemblance to the high-activity phases of these patterns and are likely to be closely linked to them. The spatiotemporal patterns are typically obtained during rest, but they have been reported during task performance (https://pubmed.ncbi.nlm.nih.gov/30753928/) which further suggests a link to the current work. Similar patterns have been observed in anesthetized animals, which also reinforces the conclusion of the current work that the states are fundamental aspects of the brain's functional organization.

We appreciate the comments that relate spatiotemporal patterns, functional connectivity gradients, and the latent states derived from the HMM. Our work was also inspired by the papers that the reviewer suggested, especially Bolt et al.’s (2022), which compared the results of numerous dimensionality and clustering algorithms and suggested three spatiotemporal patterns that seemed to be commonly supported across algorithms. We originally cited these studies throughout the manuscript, but did not discuss them comprehensively. We have revised the Discussion to situate our findings on past work that used resting-state fMRI to study low-dimensional latent brain states.

[Manuscript, page 15-16] “This perspective is supported by previous work that has used different methods to capture recurring low-dimensional states from spontaneous fMRI activity during rest. For example, to extract time-averaged latent states, early resting-state analyses identified task-positive and tasknegative networks using seed-based correlation (Fox et al., 2005). Dimensionality reduction algorithms such as independent component analysis (Smith et al., 2009) extracted latent components that explain the largest variance in fMRI time series. Other lines of work used timeresolved analyses to capture latent state dynamics. For example, variants of clustering algorithms, such as co-activation patterns (Liu et al., 2018; Liu and Duyn, 2013), k-means clustering (Allen et al., 2014), and HMM (Baker et al., 2014; Chen et al., 2016; Vidaurre et al., 2018, 2017), characterized fMRI time series as recurrences of and transitions between a small number of states. Time-lag analysis was used to identify quasiperiodic spatiotemporal patterns of propagating brain activity (Abbas et al., 2019; Yousefi and Keilholz, 2021). A recent study extensively compared these different algorithms and showed that they all report qualitatively similar latent states or components when applied to fMRI data (Bolt et al., 2022). While these studies used different algorithms to probe data-specific brain states, this work and ours report common latent axes that follow a long-standing theory of large-scale human functional systems (Mesulam, 1998). Neural dynamics span principal axes that dissociate unimodal to transmodal and sensory to motor information processing systems.”

Reviewer #2 (Public Review):

In this study, Song and colleagues applied a Hidden Markov Model to whole-brain fMRI data from the unique SONG dataset and a grad-CPT task, and in doing so observed robust transitions between lowdimensional states that they then attributed to specific psychological features extracted from the different tasks.

The methods used appeared to be sound and robust to parameter choices. Whenever choices were made regarding specific parameters, the authors demonstrated that their approach was robust to different values, and also replicated their main findings on a separate dataset.

I was mildly concerned that similarities in some of the algorithms used may have rendered some of the inter-measure results as somewhat inevitable (a hypothesis that could be tested using appropriate null models).

This work is quite integrative, linking together a number of previous studies into a framework that allows for interesting follow-up questions.

Overall, I found the work to be robust, interesting, and integrative, with a wide-ranging citation list and exciting implications for future work.

We appreciate the reviewer’s comments on the study’s robustness and future implications. Our work was highly motivated by the reviewer’s prior work.

Reviewer #3 (Public Review):

My general assessment of the paper is that the analyses done after they find the model are exemplary and show some interesting results. However, the method they use to find the number of states (Calinski-Harabasz score instead of log-likelihood), the model they use generally (HMM), and the fact that they don't show how they find the number of states on HCP, with the Schaeffer atlas, and do not report their R^2 on a test set is a little concerning. I don't think this perse impedes their results, but it is something that they can improve. They argue that the states they find align with long-standing ideas about the functional organization of the brain and align with other research, but they can improve their selection for their model.

We appreciate the reviewer’s thorough read of the paper, evaluation of our analyses linking brain states to behavior as “exemplary”, and important questions about the modeling approach. We have included detailed responses below and updated the manuscript accordingly.

Strengths:

• Use multiple datasets, multiple ROIs, and multiple analyses to validate their results

• Figures are convincing in the sense that patterns clearly synchronize between participants

• Authors select the number of states using the optimal model fit (although this turns out to be a little more questionable due to what they quantify as 'optimal model fit')

We address this concern on page 30-31 of this response letter.

• Replication with Schaeffer atlas makes results more convincing

• The analyses around the fact that the base state acts as a flexible hub are well done and well explained

• Their comparison of synchrony is well-done and comparing it to resting-state, which does not have any significant synchrony among participants is obvious, but still good to compare against.

• Their results with respect to similar narrative engagement being correlated with similar neural state dynamics are well done and interesting.

• Their results on event boundaries are compelling and well done. However, I do not find their Chang et al. results convincing (Figure 4B), it could just be because it is a different medium that explains differences in DMN response, but to me, it seems like these are just altogether different patterns that can not 100% be explained by their method/results.

We entirely agree with the reviewer that the Chang et al. (2021) data are different in many ways from our own SONG dataset. Whereas data from Chang et al. (2021) were collected while participants listened to an audio-only narrative, participants in the SONG sample watched and listened to audiovisual stimuli. They were scanned at different universities in different countries with different protocols by different research groups for different purposes. That is, there are numerous reasons why we would expect the model should not generalize. Thus, we found it compelling and surprising that, despite all of these differences between the datasets, the model trained on the SONG dataset generalized to the data from Chang et al. (2021). The results highlighted a robust increase in the DMN state occurrence and a decrease in the base state occurrence after the narrative event boundaries, irrespective of whether the stimulus was an audiovisual sitcom episode or a narrated story. This external model validation was a way that we tested the robustness of our own model and the relationship between neural state dynamics and cognitive dynamics.

• Their results that when there is no event, transition into the DMN state comes from the base state is 50% is interesting and a strong result. However, it is unclear if this is just for the sitcom or also for Chang et al.'s data.

We apologize for the lack of clarity. We show the statistical results of the two sitcom episodes as well as Chang et al.’s (2021) data in Figure 4—figure supplement 2 in our original manuscript. Here, we provide the exact values of the base-to-DMN state transition probability, and how they differ across moments after event boundaries compared to non-event boundaries.

For sitcom episode 1, the probability of base-to-DMN state transition was 44.6 ± 18.8 % at event boundaries whereas 62.0 ± 10.4 % at non-event boundaries (FDR-p = 0.0013). For sitcom episode 2, the probability of base-to-DMN state transition was 44.1 ± 18.0 % at event boundaries whereas 62.2 ± 7.6 % at non-event boundaries (FDR-p = 0.0006). For the Chang et al. (2021) dataset, the probability of base-to-DMN state transition was 33.3 ± 15.9 % at event boundaries whereas 58.1 ± 6.4 % at non-event boundaries (FDR-p < 0.0001). Thus, our result, “At non-event boundaries, the DMN state was most likely to transition from the base state, accounting for more than 50% of the transitions to the DMN state” (pg 11, line 24-25), holds true for both the internal and external datasets.

• The involvement of the base state as being highly engaged during the comedy sitcom and the movie are interesting results that warrant further study into the base state theory they pose in this work.

• It is good that they make sure SM states are not just because of head motion (P 12).

• Their comparison between functional gradient and neural states is good, and their results are generally well-supported, intuitive, and interesting enough to warrant further research into them. Their findings on the context-specificity of their DMN and DAN state are interesting and relate well to the antagonistic relationship in resting-state data.

Weaknesses:

• Authors should train the model on part of the data and validate on another

Thank you for raising this issue. To the best of our knowledge, past work that applied the HMM to the fMRI data has conducted training and inference on the same data, including initial work that implemented HMM on the resting-state fMRI (Baker et al., 2014; Chen et al., 2016; Vidaurre et al., 2018, 2017) as well as more recent work that applied HMMs to the task or movie-watching fMRI (Cornblath et al., 2020; Taghia et al., 2018; van der Meer et al., 2020; Yamashita et al., 2021). That is, the parameters—emission probability, transition probability, and initial probability—were estimated from the entire dataset and the latent state sequence was inferred using the Viterbi algorithm on the same dataset.

However, we were also aware of the potential problem this may have. Therefore, in our recent work asking a different research question in another fMRI dataset (Song et al., 2021b), we trained an HMM on a subset of the dataset (moments when participants were watching movie clips in the original temporal order) and inferred latent state sequence of the fMRI time series in another subset of the dataset (moments when participants were watching movie clips in a scrambled temporal order). To the best of our knowledge, this was the first paper that used different segments of the data to fit and infer states from the HMM.

In the current study, we wanted to capture brain states that underlie brain activity across contexts. Thus, we presented the same-dataset training and inference procedure as our primary result. However, for every main result, we also showed results where we separated the data used for model fitting and state inference. That is, we fit the HMM on the SONG dataset, primarily report the inference results on the SONG dataset, but also report inference on the external datasets that were not included in model fitting. The datasets used were the Human Connectome Project dataset (Van Essen et al., 2013), Chang et al. (2021) audio-listening dataset, Rosenberg et al. (2016) gradCPT dataset, and Chen et al. (2017) Sherlock dataset.

However, to further address the concern of the reviewer whether the HMM fit is reliable when applied to held-out data, we computed the reliability of the HMM inference by conducting crossvalidations and split-half reliability analysis.

(1) Cross-validation

To separate the dataset used for HMM training and inference, we conducted cross-validation on the SONG dataset (N=27) by training the model with the data from 26 participants and inferring the latent state sequence of the held-out participant.

First, we compared the robustness of the model training by comparing the mean activity patterns of the four latent states fitted at the group level (N=27) with the mean activity patterns of the four states fitted across cross-validation folds. Pearson’s correlations between the group-level vs. cross-validated latent states’ mean activity patterns were r = 0.991 ± 0.010, with a range from 0.963 to 0.999.

Second, we compared the robustness of model inference by comparing the latent state sequences that were inferred at the group level vs. from held-out participants in a cross-validation scheme. All fMRI conditions had mean similarity higher than 90%; Rest 1: 92.74 ± 5.02 %, Rest2: 92.74 ± 4.83 %, GradCPT face: 92.97 ± 6.41 %, GradCPT scene: 93.27 ± 5.76 %, Sitcom ep1: 93.31 ± 3.92 %, Sitcom ep2: 93.13 ± 4.36 %, Documentary: 92.42 ± 4.72 %.

Third, with the latent state sequences inferred from cross-validation, we replicated the analysis of Figure 3 to test for synchrony of the latent state sequences across participants. The crossvalidated results were highly similar to manuscript Figure 3, which was generated from the grouplevel analysis. Mean synchrony of latent state sequences are as follows: Rest 1: 25.90 ± 3.81%, Rest 2: 25.75 ± 4.19 %, GradCPT face: 27.17 ± 3.86 %, GradCPT scene: 28.11 ± 3.89 %, Sitcom ep1: 40.69 ± 3.86%, Sitcom ep2: 40.53 ± 3.13%, Documentary: 30.13 ± 3.41%.

Author response image 2.

(2) Split-half reliability

To test for the internal robustness of the model, we randomly assigned SONG dataset participants into two groups and conducted HMM separately in each. Similarity (Pearson’s correlation) between the two groups’ activation patterns were DMN: 0.791, DAN: 0.838, SM: 0.944, base: 0.837. The similarity of the covariance patterns were DMN: 0.995, DAN: 0.996, SM: 0.994, base: 0.996.

Author response image 3.

We further validated the split-half reliability of the model using the HCP dataset, which contains data of a larger sample (N=119). Similarity (Pearson’s correlation) between the two groups’ activation patterns were DMN: 0.998, DAN: 0.997, SM: 0.993, base: 0.923. The similarity of the covariance patterns were DMN: 0.995, DAN: 0.996, SM: 0.994, base: 0.996.

Together the cross-validation and split-half reliability results demonstrate that the HMM results reported in the manuscript are reliable and robust to the way we conducted the analysis. The result of the split-half reliability analysis is added in the Results.

[Manuscript, page 3-4] “Neural state inference was robust to the choice of 𝐾 (Figure 1—figure supplement 1) and the fMRI preprocessing pipeline (Figure 1—figure supplement 5) and consistent when conducted on two groups of randomly split-half participants (Pearson’s correlations between the two groups’ latent state activation patterns: DMN: 0.791, DAN: 0.838, SM: 0.944, base: 0.837).”

• Comparison with just PCA/functional gradients is weak in establishing whether HMMs are good models of the timeseries. Especially given that the HMM does not explain a lot of variance in the signal (~0.5 R^2 for only 27 brain regions) for PCA. I think they don't report their own R^2 of the timeseries

We agree with the reviewer that the PCA that we conducted to compare with the explained variance of the functional gradients was not directly comparable because PCA and gradients utilize different algorithms to reduce dimensionality. To make more meaningful comparisons, we removed the data-specific PCA results and replaced them with data-specific functional gradients (derived from the SONG dataset). This allows us to directly compare SONG-specific functional gradients with predefined gradients (derived from the resting-state HCP dataset from Margulies et al. [2016]). We found that the degrees to which the first two predefined gradients explained whole-brain fMRI time series (SONG: 𝑟! = 0.097, HCP: 0.084) were comparable to the amount of variance explained by the first two data-specific gradients (SONG: 𝑟! = 0.100, HCP: 0.086). Thus, the predefined gradients explain as much variance in the SONG data time series as SONG-specific gradients do. This supports our argument that the low-dimensional manifold is largely shared across contexts, and that the common HMM latent states may tile the predefined gradients.

These analyses and results were added to the Results, Methods, and Figure 1—figure supplement 8. Here, we only attach changes to the Results section for simplicity, but please see the revised manuscript for further changes.

[Manuscript, page 5-6] “We hypothesized that the spatial gradients reported by Margulies et al. (2016) act as a lowdimensional manifold over which large-scale dynamics operate (Bolt et al., 2022; Brown et al., 2021; Karapanagiotidis et al., 2020; Turnbull et al., 2020), such that traversals within this manifold explain large variance in neural dynamics and, consequently, cognition and behavior (Figure 1C). To test this idea, we situated the mean activity values of the four latent states along the gradients defined by Margulies et al. (2016) (see Methods). The brain states tiled the two-dimensional gradient space with the base state at the center (Figure 1D; Figure1—figure supplement 7). The Euclidean distances between these four states were maximized in the two-dimensional gradient space, compared to a chance where the four states were inferred from circular-shifted time series (p < 0.001). For the SONG dataset, the DMN and SM states fell at more extreme positions of the primary gradient than expected by chance (both FDR-p values = 0.004; DAN and SM states, FDRp values = 0.171). For the HCP dataset, the DMN and DAN states fell at more extreme positions on the primary gradient (both FDR-p values = 0.004; SM and base states, FDR-p values = 0.076). No state was consistently found at the extremes of the secondary gradient (all FDR-p values > 0.021).

We asked whether the predefined gradients explain as much variance in neural dynamics as latent subspace optimized for the SONG dataset. To do so, we applied the same nonlinear dimensionality reduction algorithm to the SONG dataset’s ROI time series. Of note, the SONG dataset includes 18.95% rest, 15.07% task, and 65.98% movie-watching data whereas the data used by Margulies et al. (2016) was 100% rest. Despite these differences, the SONG-specific gradients closely resembled the predefined gradients, with significant Pearson’s correlations observed for the first (r = 0.876) and second (r = 0.877) gradient embeddings (Figure 1—figure supplement 8). Gradients identified with the HCP data also recapitulated Margulies et al.’s (2016) first (r = 0.880) and second (r = 0.871) gradients. We restricted our analysis to the first two gradients because the two gradients together explained roughly 50% of the entire variance of functional brain connectome (SONG: 46.94%, HCP: 52.08%), and the explained variance dropped drastically from the third gradients (more than 1/3 drop compared to second gradients). The degrees to which the first two predefined gradients explained whole-brain fMRI time series (SONG: 𝑟! = 0.097, HCP: 0.084) were comparable to the amount of variance explained by the first two data-specific gradients (SONG: 𝑟! = 0.100, HCP: 0.086; Figure 1—figure supplement 8). Thus, the low-dimensional manifold captured by Margulies et al. (2016) gradients is highly replicable, explaining brain activity dynamics as well as data-specific gradients, and is largely shared across contexts and datasets. This suggests that the state space of whole-brain dynamics closely recapitulates low-dimensional gradients of the static functional brain connectome.”

The reviewer also pointed out that the PCA-gradient comparison was weak in establishing whether HMMs are good models of the time series. However, we would like to point out that the purpose of the comparison was not to validate the performance of the HMM. Instead, we wanted to test whether the gradients introduced by Margulies et al. (2016) could act as a generalizable lowdimensional manifold of brain state dynamics. To argue that the predefined gradients are a shared manifold, these gradients should explain SONG data fMRI time series as much as the principal components derived directly from the SONG data. Our results showed comparable 𝑟!, both in predefined gradient vs. data-specific PC comparisons and predefined gradient vs. data-specific gradient comparisons, which supported our argument that the predefined gradients could be the shared embedding space across contexts and datasets.

The reviewer pointed out that the 𝑟2 of ~0.5 is not explaining enough variance in the fMRI signal. However, we respectfully disagree with this point because there is no established criterion for what constitutes a high or low 𝑟2 for this type of analysis. Of note, previous literature that also applied PCA to fMRI time series (Author response image 4A and 4B) (Lynn et al., 2021; Shine et al., 2019) also found that the cumulative explained variance of top 5 principal components is around 50%. Author response image 4C shows cumulative variances to which gradients explain the functional connectome of the resting-state fMRI data (Margulies et al., 2016).

Author response image 4.

Finally, the reviewer pointed out that the 𝑟! of the HMM-derived latent sequence to the fMRI time series should be reported. However, there is no standardized way of measuring the explained variance of the HMM inference. There is no report of explained variance in the traditional HMMfMRI papers (Baker et al., 2014; Chen et al., 2016; Vidaurre et al., 2018, 2017). Rather than 𝑟!, the HMM computes the log likelihood of the model fit. However, because log likelihood values are dependent on the number of data points, studies do not report log likelihood values nor do they use these metrics to interpret the goodness of model fit.

To ask whether the goodness of the HMM fit was significant above chance, we compared the log likelihood of the HMM to the log likelihood distribution of the null HMM fits. First, we extracted the log likelihood of the HMM fit with the real fMRI time series. We iterated this 1,000 times when calculating null HMMs using the circular-shifted fMRI time series. The log likelihood of the real model was significantly higher than the chance distribution, with a z-value of 2182.5 (p < 0.001). This indicates that the HMM explained a large variance in our fMRI time series data, significantly above chance.

• Authors do not specify whether they also did cross-validation for the HCP dataset to find 4 clusters

We apologize for the lack of clarity. When we computed the Calinski-Harabasz score with the HCP dataset, three was chosen as the most optimal number of states (Author response image 5A). When we set K as 3, the HMM inferred the DMN, DAN, and SM states (Author response image 5C). The base state was included when K was set to 4 (Author response image 5B). The activation pattern similarities of the DMN, DAN, and SM states were r = 0.981, 0.984, 0.911 respectively.

Author response image 5.

We did not use K = 3 for the HCP data replication because we were not trying to test whether these four states would be the optimal set of states in every dataset. Although the CalinskiHarabasz score chose K = 3 because it showed the best clustering performance, this does not mean that the base state is not meaningful to this dataset. Likewise, the latent states that are inferred when we increase/decrease the number of states are also meaningful states. For example, in Figure 1—figure supplement 1, we show an example of the SONG dataset’s latent states when we set K to 7. The seven latent states included the DAN, SM, and base states, the DMN state was subdivided into DMN-A and DMN-B states, and the FPN state and DMN+VIS state were included. Setting a higher number of states like K = 7 would mean that we are capturing brain state dynamics in a higher dimension than when using K = 4. Because we are utilizing a higher number of states, a model set to K = 7 would inevitably capture a larger variance of fMRI time series than a model set to K = 4.

The purpose of latent state replication with the HCP dataset was to validate the generalizability of the DMN, DAN, SM, and base states. Before characterizing these latent states’ relevance to cognition, we needed to verify that these latent states were not simply overfit to the SONG dataset. The fact that the HMM revealed a similar set of latent states when applied to the HCP dataset suggested that the states were not merely specific to SONG data.

To make our points clearer in the manuscript, we emphasized that we are not arguing for the four states to be the exclusive states. We made edits to Discussion as follows.

[Manuscript, page 16] “Our study adopted the assumption of low dimensionality of large-scale neural systems, which led us to intentionally identify only a small number of states underlying whole-brain dynamics. Importantly, however, we do not claim that the four states will be the optimal set of states in every dataset and participant population. Instead, latent states and patterns of state occurrence may vary as a function of individuals and tasks (Figure 1—figure supplement 2). Likewise, while the lowest dimensions of the manifold (i.e., the first two gradients) were largely shared across datasets tested here, we do not argue that it will always be identical. If individuals and tasks deviate significantly from what was tested here, the manifold may also differ along with changes in latent states (Samara et al., 2023). Brain systems operate at different dimensionalities and spatiotemporal scales (Greene et al., 2023), which may have different consequences for cognition. Asking how brain states and manifolds—probed at different dimensionalities and scales—flexibly reconfigure (or not) with changes in contexts and mental states is an important research question for understanding complex human cognition.”

• One of their main contributions is the base state but the correlation between the base state in their Song dataset and the HCP dataset is only 0.399

This is a good point. However, there is precedent for lower spatial pattern correlation of the base state compared to other states in the literature.

Compared to the DMN, DAN, and SM states, the base state did not show characteristic activation or deactivation of functional networks. Most of the functional networks showed activity levels close to the mean (z = 0). With this flattened activation pattern, relatively low activation pattern similarity was observed between the SONG base state and the HCP base state.

In Figure 1—figure supplement 6, we write, “The DMN, DAN, and SM states showed similar mean activity patterns. We refrained from making interpretations about the base state’s activity patterns because the mean activity of most of the parcels was close to z = 0”.

A similar finding has been reported in a previous work by Chen et al. (2016) that discovered the base state with HMM. State 9 (S9) of their results is comparable to our base state. They report that even though the spatial correlation coefficient of the brain state from the split-half reliability analysis was the lowest for S9 due to its low degrees of activation or deactivation, S9 was stably inferred by the HMM. The following is a direct quote from their paper:

“To the best of our knowledge, a state similar to S9 has not been presented in previous literature. We hypothesize that S9 is the “ground” state of the brain, in which brain activity (or deactivity) is similar for the entire cortex (no apparent activation or deactivation as shown in Fig. 4). Note that different groups of subjects have different spatial patterns for state S9 (Fig. 3A). Therefore, S9 has the lowest reproducible spatial pattern (Fig. 3B). However, its temporal characteristics allowed us to distinguish it consistently from other states.” (Chen et al., 2016)

Thus, we believe our data and prior results support the existence of the “base state”.

• Figure 1B: Parcellation is quite big but there seems to be a gradient within regions

This is a function of the visualization software. Mean activity (z) is the same for all voxels within a parcel. To visualize the 3D contours of the brain, we chose an option in the nilearn python function that smooths the mean activity values based on the surface reconstructed anatomy.

In the original manuscript, our Methods write, “The brain surfaces were visualized with nilearn.plotting.plot_surf_stat_map. The parcel boundaries in Figure 1B are smoothed from the volume-to-surface reconstruction.”

• Figure 1D: Why are the DMNs further apart between SONG and HCP than the other states

To address this question, we first tested whether the position of the DMN states in the gradient space is significantly different for the SONG and HCP datasets. We generated surrogate HMM states from the circular-shifted fMRI time series and positioned the four latent states and the null DMN states in the 2-dimensional gradient space (Author response image 6).

Author response image 6.

We next tested whether the Euclidean distance between the SONG dataset’s DMN state and the HCP dataset’s DMN state is larger than would be expected by chance (Author response image 7). To do so, we took the difference between the DMN state positions and compared it to the 1,000 differences generated from the surrogate latent states. The DMN states of the SONG and HCP datasets did not significantly differ in the Gradient 1 dimension (two-tailed test, p = 0.794). However, as the reviewer noted, the positions differed significantly in the Gradient 2 dimension (p = 0.047). The DMN state leaned more towards the Visual gradient in the SONG dataset, whereas it leaned more towards the Somatosensory-Motor gradient in the HCP dataset.

Author response image 7.

Though we cannot claim an exact reason for this across-dataset difference, we note a distinctive difference between the SONG and HCP datasets. Both datasets largely included resting-state, controlled tasks, and movie watching. The SONG dataset included 18.95% of rest, 15.07% of task, and 65.98% of movie watching. The task only contained the gradCPT, i.e., sustained attention task. On the other hand, the HCP dataset included 52.71% of rest, 24.35% of task, and 22.94% of movie watching. There were 7 different tasks included in the HCP dataset. It is possible that different proportions of rest, task, and movie watching, and different cognitive demands involved with each dataset may have created data-specific latent states.

• Page 5 paragraph starting at L25: Their hypothesis that functional gradients explain large variance in neural dynamics needs to be explained more, is non-trivial especially because their R^2 scores are so low (Fig 1. Supplement 8) for PCA

We address this concern on page 21-23 of this response letter.

• Generally, I do not find the PCA analysis convincing and believe they should also compare to something like ICA or a different model of dynamics. They do not explain their reasoning behind assuming an HMM, which is an extremely simplified idea of brain dynamics meaning they only change based on the previous state.

We appreciate this perspective. We replaced the Margulies et al.’s (2016) gradient vs. SONGspecific PCA comparison with a more direct Margulies et al.’s (2016) gradient vs. SONG-specific gradient comparison as described on page 21-23 of this response letter.

More broadly, we elected to use HMM because of recent work showing correspondence between low-dimensional HMM states and behavior (Cornblath et al., 2020; Taghia et al., 2018; van der Meer et al., 2020; Yamashita et al., 2021). We also found the model’s assumption—a mixture Gaussian emission probability and first-order Markovian transition probability—to be the most suited to analyzing the fMRI time series data. We do not intend to claim that other data-reduction techniques would not also capture low-dimensional, behaviorally relevant changes in brain activity. Instead, our primary focus was identifying a set of latent states that generalize (i.e., recur) across multiple contexts and understanding how those states reflect cognitive and attentional states.

Although a comparison of possible data-reduction algorithms is out of the scope of the current work, an exhaustive comparison of different models can be found in Bolt et al. (2022). The authors compared dozens of latent brain state algorithms spanning zero-lag analysis (e.g., principal component analysis, principal component analysis with Varimax rotation, Laplacian eigenmaps, spatial independent component analysis, temporal independent component analysis, hidden Markov model, seed-based correlation analysis, and co-activation patterns) to time-lag analysis (e.g., quasi-periodic pattern and lag projections). Bolt et al. (2022) writes “a range of empirical phenomena, including functional connectivity gradients, the task-positive/task-negative anticorrelation pattern, the global signal, time-lag propagation patterns, the quasiperiodic pattern and the functional connectome network structure, are manifestations of the three spatiotemporal patterns.” That is, many previous findings that used different methods essentially describe the same recurring latent states. A similar argument was made in previous papers (Brown et al., 2021; Karapanagiotidis et al., 2020; Turnbull et al., 2020).

We agree that the HMM is a simplified idea of brain dynamics. We do not argue that the four number of states can fully explain the complexity and flexibility of cognition. Instead, we hoped to show that there are different dimensionalities to which the brain systems can operate, and they may have different consequences to cognition. We “simplified” neural dynamics to a discrete sequence of a small number of states. However, what is fascinating is that these overly “simplified” brain state dynamics can explain certain cognitive and attentional dynamics, such as event segmentation and sustained attention fluctuations. We highlight this point in the Discussion.

[Manuscript, page 16] “Our study adopted the assumption of low dimensionality of large-scale neural systems, which led us to intentionally identify only a small number of states underlying whole-brain dynamics. Importantly, however, we do not claim that the four states will be the optimal set of states in every dataset and participant population. Instead, latent states and patterns of state occurrence may vary as a function of individuals and tasks (Figure 1—figure supplement 2). Likewise, while the lowest dimensions of the manifold (i.e., the first two gradients) were largely shared across datasets tested here, we do not argue that it will always be identical. If individuals and tasks deviate significantly from what was tested here, the manifold may also differ along with changes in latent states (Samara et al., 2023). Brain systems operate at different dimensionalities and spatiotemporal scales (Greene et al., 2023), which may have different consequences for cognition. Asking how brain states and manifolds—probed at different dimensionalities and scales—flexibly reconfigure (or not) with changes in contexts and mental states is an important research question for understanding complex human cognition.”

• For the 25- ROI replication it seems like they again do not try multiple K values for the number of states to validate that 4 states are in fact the correct number.

In the manuscript, we do not argue that the four will be the optimal number of states in any dataset. (We actually predict that this may differ depending on the amount of data, participant population, tasks, etc.) Instead, we claim that the four identified in the SONG dataset are not specific (i.e., overfit) to that sample, but rather recur in independent datasets as well. More broadly we argue that the complexity and flexibility of human cognition stem from the fact that computation occurs at multiple dimensions and that the low-dimensional states observed here are robustly related to cognitive and attentional states. To prevent misunderstanding of our results, we emphasized in the Discussion that we are not arguing for a fixed number of states. A paragraph included in our response to the previous comment (page 16 in the manuscript) illustrates this point.

• Fig 2B: Colorbar goes from -0.05 to 0.05 but values are up to 0.87

We apologize for the confusion. The current version of the figure is correct. The figure legend states, “The values indicate transition probabilities, such that values in each row sums to 1. The colors indicate differences from the mean of the null distribution where the HMMs were conducted on the circular-shifted time series.”

We recognize that this complicates the interpretation of the figure. However, after much consideration, we decided that it was valuable to show both the actual transition probabilities (values) and their difference from the mean of null HMMs (colors). The values demonstrate the Markovian property of latent state dynamics, with a high probability of remaining in the same state at consecutive moments and a low probability of transitioning to a different state. The colors indicate that the base state is a transitional hub state by illustrating that the DMN, DAN, and SM states are more likely to transition to the base state than would be expected by chance.

• P 16 L4 near-critical, authors need to be more specific in their terminology here especially since they talk about dynamic systems, where near-criticality has a specific definition. It is unclear which definition they are looking for here.

We agree that our explanation was vague. Because we do not have evidence for this speculative proposal, we removed the mention of near-criticality. Instead, we focus on our observation as the base state being the transitional hub state within a metastable system.

[Manuscript, page 17-18] “However, the functional relevance of the base state to human cognition had not been explored previously. We propose that the base state, a transitional hub (Figure 2B) positioned at the center of the gradient subspace (Figure 1D), functions as a state of natural equilibrium. Transitioning to the DMN, DAN, or SM states reflects incursion away from natural equilibrium (Deco et al., 2017; Gu et al., 2015), as the brain enters a functionally modular state. Notably, the base state indicated high attentional engagement (Figure 5E and F) and exhibited the highest occurrence proportion (Figure 3B) as well as the longest dwell times (Figure 3—figure supplement 1) during naturalistic movie watching, whereas its functional involvement was comparatively minor during controlled tasks. This significant relevance to behavior verifies that the base state cannot simply be a byproduct of the model. We speculate that susceptibility to both external and internal information is maximized in the base state—allowing for roughly equal weighting of both sides so that they can be integrated to form a coherent representation of the world—at the expense of the stability of a certain functional network (Cocchi et al., 2017; Fagerholm et al., 2015). When processing rich narratives, particularly when a person is fully immersed without having to exert cognitive effort, a less modular state with high degrees of freedom to reach other states may be more likely to be involved. The role of the base state should be further investigated in future studies.”

• P16 L13-L17 unnecessary

We prefer to have the last paragraph as a summary of the implications of this paper. However, if the length of this paper becomes a problem as we work towards publication with the editors, we are happy to remove these lines.

• I think this paper is solid, but my main issue is with using an HMM, never explaining why, not showing inference results on test data, not reporting an R^2 score for it, and not comparing it to other models. Secondly, they use the Calinski-Harabasz score to determine the number of states, but not the log-likelihood of the fit. This clearly creates a bias in what types of states you will find, namely states that are far away from each other, which likely also leads to the functional gradient and PCA results they have. Where they specifically talk about how their states are far away from each other in the functional gradient space and correlated to (orthogonal) components. It is completely unclear to me why they used this measure because it also seems to be one of many scores you could use with respect to clustering (with potentially different results), and even odd in the presence of a loglikelihood fit to the data and with the model they use (which does not perform clustering).

(1) Showing inference results on test data

We address this concern on page 19-21 of this response letter.

(2) Not reporting 𝑹𝟐 score

We address this concern on page 21-23 of this response letter.

(3) Not comparing the HMM model to other models

We address this concern on page 27-28 of this response letter.

(4) The use of the Calinski-Harabasz score to determine the number of states rather than the log-likelihood of the model fit

To our knowledge, the log-likelihood of the model fit is not used in the HMM literature. It is because the log-likelihood tends to increase monotonically as the number of states increases. Baker et al. (2014) illustrates this problem, writing:

“In theory, it should be possible to pick the optimal number of states by selecting the model with the greatest (negative) free energy. In practice however, we observe that the free energy increases monotonically up to K = 15 states, suggesting that the Bayes-optimal model may require an even higher number of states.”

Similarly, the following figure is the log-likelihood estimated from the SONG dataset. Similar to the findings of Baker et al. (2014), the log-likelihood monotonically increased as the number of states increased (Author response image 8, right). The measures like AIC or BIC, which account for the number of parameters, also have the same issue of monotonic increase.

Author response image 8.

Because there is “no straightforward data-driven approach to model order selection” (Baker et al., 2014), past work has used different approaches to decide on the number of states. For example, Vidaurre et al. (2018) iterated over a range of the number of states to repeat the same HMM training and inference procedures 5 times using the same hyperparameters. They selected the number of states that showed the highest consistency across iterations. Gao et al. (2021) tested the clustering performance of the model output using the Calinski-Harabasz score. The number of states that showed the highest within-cluster cohesion compared to the across-cluster separation was selected as the number of states. Chang et al. (2021) applied HMM to voxels of the ventromedial prefrontal cortex using a similar clustering algorithm, writing: “To determine the number of states for the HMM estimation procedure, we identified the number of states that maximized the average within-state spatial similarity relative to the average between-state similarity”. In our previous paper (Song et al., 2021b), we reported both the reliability and clustering performance measures to decide on the number of states.

In the current manuscript, the model consistency criterion from Vidaurre et al. (2018) was ineffective because the HMM inference was extremely robust (i.e., always inferring the exact same sequence) due to a large number of data points. Thus, we used the Calinski-Harabasz score as our criterion for the number of states selected.

We agree with the reviewer that the selection of the number of states is critical to any study that implements HMM. However, the field lacks a consensus on how to decide on the number of states in the HMM, and the Calinski-Harabasz score has been validated in previous studies. Most importantly, the latent states’ relationships with behavioral and cognitive measures give strong evidence that the latent states are indeed meaningful states. Again, we are not arguing that the optimal set of states in any dataset will be four nor are we arguing that these four states will always be the optimal states. Instead, the manuscript proposes that a small number of latent states explains meaningful variance in cognitive dynamics.

• Grammatical error: P24 L29 rendering seems to have gone wrong

Our intention was correct here. To avoid confusion, we changed “(number of participantsC2 iterations)” to “(#𝐶!iterations, where N=number of participants)” (page 26 in the manuscript).

Questions:

• Comment on subject differences, it seems like they potentially found group dynamics based on stimuli, but interesting to see individual differences in large-scale dynamics, and do they believe the states they find mostly explain global linear dynamics?

We agree with the reviewer that whether low-dimensional latent state dynamics explain individual differences—above and beyond what could be explained by the high-dimensional, temporally static neural signatures of individuals (e.g., Finn et al., 2015)—is an important research question. However, because the SONG dataset was collected in a single lab, with a focus on covering diverse contexts (rest, task, and movie watching) over 2 sessions, we were only able to collect 27 participants. Due to this small sample size, we focused on investigating group-level, shared temporal dynamics and across-condition differences, rather than on investigating individual differences.

Past work has studied individual differences (e.g., behavioral traits like well-being, intelligence, and personality) using the HMM (Vidaurre et al., 2017). In the lab, we are working on a project that investigates latent state dynamics in relation to individual differences in clinical symptoms using the Healthy Brain Network dataset (Ji et al., 2022, presented at SfN; Alexander et al., 2017).

Finally, the reviewer raises an interesting question about whether the latent state sequence that was derived here mostly explains global linear dynamics as opposed to nonlinear dynamics. We have two responses: one methodological and one theoretical. First, methodologically, we defined the emission probabilities as a linear mixture of Gaussian distributions for each input dimension with the state-specific mean (mean fMRI activity patterns of the networks) and variance (functional covariance across networks). Therefore, states are modeled with an assumption of linearity of feature combinations. Theoretically, recent work supports in favor of nonlinearity of large-scale neural dynamics, especially as tasks get richer and more complex (Cunningham and Yu, 2014; Gao et al., 2021). However, whether low-dimensional latent states should be modeled nonlinearly—that is, whether linear algorithms are insufficient at capturing latent states compared to nonlinear algorithms—is still unknown. We agree with the reviewer that the assumption of linearity is an interesting topic in systems neuroscience. However, together with prior work which showed how numerous algorithms—either linear or nonlinear—recapitulated a common set of latent states, we argue that the HMM provides a strong low-dimensional model of large-scale neural activity and interaction.

• P19 L40 why did the authors interpolate incorrect or no-responses for the gradCPT runs? It seems more logical to correct their results for these responses or to throw them out since interpolation can induce huge biases in these cases because the data is likely not missing at completely random.

Interpolating the RTs of the trials without responses (omission errors and incorrect trials) is a standardized protocol for analyzing gradCPT data (Esterman et al., 2013; Fortenbaugh et al., 2018, 2015; Jayakumar et al., 2023; Rosenberg et al., 2013; Terashima et al., 2021; Yamashita et al., 2021). The choice of this analysis is due to an assumption that sustained attention is a continuous attentional state; the RT, a proxy for the attentional state in the gradCPT literature, is a noisy measure of a smoothed, continuous attentional state. Thus, the RTs of the trials without responses are interpolated and the RT time courses are smoothed by convolving with a gaussian kernel.

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Author Response

Reviewer #2 (Public Review):

"The cellular architecture of memory modules in Drosophila supports stochastic input integration" is a classical biophysical compartmental modelling study. It takes advantage of some simple current injection protocols in a massively complex mushroom body neuron called MBON-a3 and compartmental models that simulate the electrophysiological behaviour given a detailed description of the anatomical extent of its neurites.

This work is interesting in a number of ways:

• The input structure information comes from EM data (Kenyon cells) although this is not discussed much in the paper - The paper predicts a potentially novel normalization of the throughput of KC inputs at the level of the proximal dendrite and soma - It claims a new computational principle in dendrites, this didn’t become very clear to me Problems I see:

• The current injections did not last long enough to reach steady state (e.g. Figure 1FG), and the model current injection traces have two time constants but the data only one (Figure 2DF). This does not make me very confident in the results and conclusions.

These are two important but separate questions that we would like to address in turn.

As for the first, in our new recordings using cytoplasmic GFP to identify MBON-alpha3, we performed both a 200 ms current injection and performed prolonged recordings of 400 ms to reach steady state (for all 4 new cells 1’-4’). For comparison with the original dataset we mainly present the raw traces for 200 ms recordings in Figure 1 Supplement 2. In addition, we now provide a direct comparison of these recordings (200 ms versus 400 ms) and did not observe significant differences in tau between these data (Figure 1 Supplement 2 K). This comparison illustrates that the 200 ms current injection reaches a maximum voltage deflection that is close to the steady state level of the prolonged protocol. Importantly, the critical parameter (tau) did not change between these datasets.

Regarding the second question, the two different time constants, we thank the reviewer for pointing this out. Indeed, while the simulated voltage follows an approximately exponential decay which is, by design, essentially identical to the measured value (τ≈ 16ms, from Table 1; ee Figure 1 Supplement 2 for details), the voltage decays and rises much faster immediately following the onset and offset of the current injections. We believe that this is due to the morphology of this neuron. Current injection, and voltage recordings, are at the soma which is connected to the remainder of the neuron by a long and thin neurite. This ’remainder’ is, of course, in linear size, volume and surface (membrane) area much larger than the soma, see Fig 2A. As a result, a current injection will first quickly charge up the membrane of the soma, resulting in the initial fast voltage changes seen in Fig 2D,F, before the membrane in the remainder of the cell is charged, with the cell’s time constant τ.

We confirmed this intuition by running various simplified simulations in Neuron which indeed show a much more rapid change at step changes in injected current than over the long-term. Indeed, we found that the pattern even appears in the simplest possible two-compartment version of the neuron’s equivalent circuit which we solved in an all-purpose numerical simulator of electrical circuitry (https://www.falstad.com/circuit). The circuit is shown in Figure 1. We chose rather generic values for the circuit components, with the constraints that the cell capacitance, chosen as 15pF, and membrane resistance, chosen as 1GΩ, are in the range of the observed data (as is, consequently, its time constant which is 15ms with these choices); see Table 1 of the manuscript. We chose the capacitance of the soma as 1.5pF, making the time constant of the soma (1.5ms) an order of magnitude shorter than that of the cell.

Figure 1: Simplified circuit of a small soma (left parallel RC circuit) and the much larger remainder of a cell (right parallel RC circuit) connected by a neurite (right 100MΩ resistor). A current source (far left) injects constant current into the soma through the left 100MΩ resistor.

Figure 2 shows the somatic voltage in this circuit (i.e., at the upper terminal of the 1.5pF capacitor) while a -10pA current is injected for about 4.5ms, after which the current is set back to zero. The combination of initial rapid change, followed by a gradual change with a time constant of ≈ 15ms is visible at both onset and offset of the current injection. Figure 3 show the voltage traces plotted for a duration of approximately one time constant, and Fig 4 shows the detailed shape right after current onset.

Figure 2: Somatic voltage in the circuit in Fig. 1 with current injection for about 4.5ms, followed by zero current injection for another ≈ 3.5ms.

Figure 3: Somatic voltage in the circuit, as in Fig. 2 but with current injected for approx. 15msvvvvv

While we did not try to quantitatively assess the deviation from a single-exponential shape of the voltage in Fig. 2E, a more rapid increase at the onset and offset of the current injection is clearly visible in this Figure. This deviation from a single exponential is smaller than what we see in the simulation (both in Fig 2D of the manuscript, and in the results of the simplified circuit here in the rebuttal). We believe that the effect is smaller in Fig. E because it shows the average over many traces. It is much more visible in the ’raw’ (not averaged) traces. Two randomly selected traces from the first of the recorded neurons are shown in Figure 2 Supplement 2 C. While the non-averaged traces are plagued by artifacts and noise, the rapid voltage changes are visible essentially at all onsets and offsets of the current injection.

Figure 4: Somatic voltage in the circuit, as in Fig. 2 but showing only for the time right after current onset, about 2.3ms.

We have added a short discussion of this at the end of Section 2.3 to briefly point out this observation and its explanation. We there also refer to the simplified circuit simulation and comparison with raw voltage traces which is now shown in the new Figure 2 Supplement 2.

• The time constant in Table 1 is much shorter than in Figure 1FG?

No, these values are in agreement. To facilitate the comparison we now include a graphical measurement of tau from our traces in Figure 1 Supplement 2 J.

• Related to this, the capacitance values are very low maybe this can be explained by the model’s wrong assumption of tau?

Indeed, the measured time constants are somewhat lower than what might be expected. We believe that this is because after a step change of the injected current, an initial rapid voltage change occurs in the soma, where the recordings are taken. The measured time constant is a combination of the ’actual’ time constant of the cell and the ’somatic’ (very short) time constant of the soma. Please see our explanations above.

Importantly, the value for tau from Table 1 is not used explicitly in the model as the parameters used in our simulation are determined by optimal fits of the simulated voltage curves to experimentally obtained data.

• That latter in turn could be because of either space clamp issues in this hugely complex cell or bad model predictions due to incomplete reconstructions, bad match between morphology and electrophysiology (both are from different datasets?), or unknown ion channels that produce non-linear behaviour during the current injections.

Please see our detailed discussion above. Furthermore, we now provide additional recordings using cytoplasmic GFP as a marker for the identification of MBON-alpha3 and confirm our findings. We agree that space-clamp issues could interfere with our recordings in such a complex cell. However, our approach using electrophysiological data should still be superior to any other approach (picking text book values). As we injected negative currents for our analysis at least voltage-gated ion channels should not influence our recordings.

• The PRAXIS method in NEURON seems too ad hoc. Passive properties of a neuron should probably rather be explored in parameter scans.

We are a bit at a loss of what is meant by the PRAXIS method being "too ad hoc." The PRAXIS method is essentially a conjugate gradient optimization algorithm (since no explicit derivatives are available, it makes the assumption that the objective function is quadratic). This seems to us a systematic way of doing a parameter scan, and the procedure has been used in other related models, e.g. the cited Gouwens & Wilson (2009) study.

Questions I have:

• Computational aspects were previously addressed by e.g. Larry Abbott and Gilles Laurent (sparse coding), how do the findings here distinguish themselves from this work

In contrast to the work by Abbott and Laurent that addressed the principal relevance and suitability of sparse and random coding for the encoding of sensory information in decision making, here we address the cellular and computational mechanisms that an individual node (KC>MBON) play within the circuitry. As we use functional and morphological relevant data this study builds upon the prior work but significantly extends the general models to a specific case. We think this is essential for the further exploration of the topic.

• What is valence information?

Valence information is the information whether a stimulus is good (positive valence, e.g. sugar in appetitive memory paradigms, or negative valence in aversive olfactory conditioning - the electric shock). Valence information is provided by the dopaminergic system. Dopaminergic neurons are in direct contact with the KC>MBON circuitry and modify its synaptic connectivity when olfactory information is paired with a positive or negative stimulus.

• It seems that Martin Nawrot’s work would be relevant to this work

We are aware of the work by the Nawrot group that provided important insights into the processing of information within the olfactory mushroom body circuitry. We now highlight some of his work. His recent work will certainly be relevant for our future studies when we try to extend our work from an individual cell to networks.

• Compactification and democratization could be related to other work like Otopalik et al 2017 eLife but also passive normalization. The equal efficiency in line 427 reminds me of dendritic/synaptic democracy and dendritic constancy

Many thanks for pointing this out. This is in line with the comments from reviewer 1 and we now highlight these papers in the relevant paragraph in the discussion (line 442ff).

• The morphology does not obviously seem compact, how unusual would it be that such a complex dendrite is so compact?

We should have been more careful in our terminology, making clear that when we write ’compact’ we always mean ’electrotonically compact," in the sense that the physical dimensions of the neuron are small compared to its characteristic electrotonic length (usually called λ). The degree of a dendritic structure being electrotonically compact is determined by the interaction of morphology, size and conductances (across the membrane and along the neurites). We don’t believe that one of these factors alone (e.g. morphology) is sufficient to characterize the electrical properties of a dendritic tree. We have now clarified this in the relevant section.

• What were the advantages of using the EM circuit?

The purpose of our study is to provide a "realistic" model of a KC>MBON node within the memory circuitry. We started our simulations with random synaptic locations but wondered whether such a stochastic model is correct, or whether taking into account the detailed locations and numbers of synaptic connections of individual KCs would make a difference to the computation. Therefore we repeated the simulations using the EM data. We now address the point between random vs realistic synaptic connectivity in Figure 4F. We do not observe a significant difference but this may become more relevant in future studies if we compute the interplay between MBONs activated by overlapping sets of KCs. We simply think that utilizing the EM data gets us one step closer to realistic models.

• Isn’t Fig 4E rather trivial if the cell is compact?

We believe this figure is a visually striking illustration that shows how electrotonically compact the cell is. Such a finding may be trivial in retrospect, once the data is visualized, but we believe it provides a very intuitive description of the cell behavior.

Overall, I am worried that the passive modelling study of the MBON-a3 does not provide enough evidence to explain the electrophysiological behaviour of the cell and to make accurate predictions of the cell’s responses to a variety of stochastic KC inputs.

In our view our model adequately describes the behavior of the MBON with the most minimal (passive) model. Our approach tries to make the least assumptions about the electrophysiological properties of the cell. We think that based on the current knowledge our approach is the best possible approach as thus far no active components within the dendritic or axonal compartments of Drosophila MBONs have been described. As such, our model describes the current status which explains the behavior of the cell very well. We aim to refine this model in the future if experimental evidence requires such adaptations.

Reviewer #3 (Public Review):

This manuscript presents an analysis of the cellular integration properties of a specific mushroom body output neuron, MBON-α3, using a combination of patch clamp recordings and data from electron microscopy. The study demonstrates that the neuron is electrotonically compact permitting linear integration of synaptic input from Kenyon cells that represent odor identity.

Strengths of the manuscript:

The study integrates morphological data about MBON-α3 along with parameters derived from electrophysiological measurements to build a detailed model. 2) The modeling provides support for existing models of how olfactory memory is related to integration at the MBON.

Weaknesses of the manuscript:

The study does not provide experimental validation of the results of the computational model.

The goal of our study is to use computational approaches to provide insights into the computation of the MBON as part of the olfactory memory circuitry. Our data is in agreement with the current model of the circuitry. Our study therefore forms the basis for future experimental studies; those would however go beyond the scope of the current work.

The conclusion of the modeling analysis is that the neuron integrates synaptic inputs almost completely linearly. All the subsequent analyses are straightforward consequences of this result.

We do, indeed, find that synaptic integration in this neuron is almost completely linear. We demonstrate that this result holds in a variety of different ways. All analyses in the study serve this purpose. These results are in line with the findings by Hige and Turner (2013) who demonstrated that also synaptic integration at PN>KC synapses is highly linear. As such our data points to a feature conservation to the next node of this circuit.

The manuscript does not provide much explanation or intuition as to why this linear conclusion holds.

We respectfully disagree. We demonstrate that this linear integration is a combination of the size of the cell and the combination of its biophysical parameters, mainly the conductances across and along the neurites. As to why it holds, our main argument is that results based on the linear model agree with all known (to us) empirical results, and this is the simplest model.

In general, there is a clear takeaway here, which is that the dendritic tree of MBON-α3 in the lobes is highly electrotonically compact. The authors did not provide much explanation as to why this is, and the paper would benefit from a clearer conclusion. Furthermore, I found the results of Figures 4 and 5 rather straightforward given this previous observation. I am sceptical about whether the tiny variations in, e.g. Figs. 3I and 5F-H, are meaningful biologically.

Please see the comment above as to the ’why’ we believe the neuron is electrotonically compact: a model with this assumption agrees well with empirically found results.

We agree that the small variations in Fig 5F-H are likely not biologically meaningful. We state this now more clearly in the figure legends and in the text. This result is important to show, however. It is precisely because these variations are small, compared to the differences between voltage differences between different numbers of activated KCs (Fig 5D) or different levels of activated synapses (Fig 5E) that we can conclude that a 25% change in either synaptic strength or number can represent clearly distinguishable internal states, and that both changes have the same effect. It is important to show these data, to allow the reader to compare the differences that DO matter (Fig 5D,E) and those that DON’T (Fig 5F-H).

The same applies to Fig 3I. The reviewer is entirely correct: the differences in the somatic voltage shown in Figure 3I are minuscule, less than a micro-Volt, and it is very unlikely that these difference have any biological meaning. The point of this figure is exactly to show this!. It is to demonstrate quantitatively the transformation of the large differences between voltages in the dendritic tree and the nearly complete uniform voltage at the soma. We feel that this shows very clearly the extreme "democratization" of the synaptic input!

Author Response

Reviewer #1 (Public Review):

Nicotine preference is highly variable between individuals. The paper by Mondoloni et al. provided some insight into the potential link between IPN nAchR heterogeneity with male nicotine preference behavior. They scored mice using the amount of nicotine consumption, as well as the rats' preference of the drug using a two-bottle choice experiment. An interesting heterogeneity in nicotine-drinking profiles was observed in adult male mice, with about half of the mice ceasing nicotine consumption at high concentrations. They observed a negative association of nicotine intake with nicotine-evoked currents in the antiparticle nucleus (IPN). They also identified beta4-containing nicotine acetylcholine receptors, which exhibit an association with nicotine aversion. The behavioral differentiation of av vs. n-avs and identification of IPN variability, both in behavioral and electrophysiological aspects, add an important candidate for analyzing individual behavior in addiction.

The native existence of beta4-nAchR heterogeneity is an important premise that supports the molecules to be the candidate substrate of variabilities. However, only knockout and re-expression models were used, which is insufficient to mimic the physiological state that leads to variability in nicotine preference.

We’d like to thank reviewer 1 for his/her positive remarks and for suggesting important control experiments. Regarding the reviewer’s latest comment on the link between b4 and variability, we would like to point out that the experiment in which mice were put under chronic nicotine can be seen as another way to manipulate the physiological state of the animal. Indeed, we found that chronic nicotine downregulates b4 nAChR expression levels (but has no effect on residual nAChR currents in b4-/- mice) and reduces nicotine aversion. Therefore, these results also point toward a role of IPN b4 nAChRs in nicotine aversion. We have now performed additional experiments and analyses to address these concerns and to reinforce our demonstration.

Reviewer #2 (Public Review):

In the current study, Mondoloni and colleagues investigate the neural correlates contributing to nicotine aversion and its alteration following chronic nicotine exposure. The question asked is important to the field of individual vulnerability to drug addiction and has translational significance. First, the authors identify individual nicotine consumption profiles across isogenic mice. Further, they employed in vivo and ex vivo physiological approaches to defining how antiparticle nuclei (IPn) neuronal response to nicotine is associated with nicotine avoidance. Additionally, the authors determine that chronic nicotine exposure impairs IPn neuronal normal response to nicotine, thus contributing to higher amounts of nicotine consumption. Finally, they used transgenic and viralmediated gene expression approaches to establish a causal link between b4 nicotine receptor function and nicotine avoidance processes.

The manuscript and experimental strategy are well designed and executed; the current dataset requires supplemental analyses and details to exclude possible alternatives. Overall, the results are exciting and provide helpful information to the field of drug addiction research, individual vulnerability to drug addiction, and neuronal physiology. Below are some comments aiming to help the authors improve this interesting study.

We would like to thank the reviewer for his/her positive remarks and we hope the new version of the manuscript will clarify his/her concerns.

1) The authors used a two-bottle choice behavioral paradigm to investigate the neurophysiological substrate contributing to nicotine avoidance behaviors. While the data set supporting the author's interpretation is compelling and the experiments are well-conducted, a few supplemental control analyses will strengthen the current manuscript.

a) The bitter taste of nicotine might generate confounds in the data interpretation: are the mice avoiding the bitterness or the nicotine-induced physiological effect? To address this question, the authors mixed nicotine with saccharine, thus covering the bitterness of nicotine. Additionally, the authors show that all the mice exposed to quinine avoid it, and in comparison, the N-Av don't avoid the bitterness of the nicotine-saccharine solution. Yet it is unclear if Av and N-Av have different taste discrimination capacities and if such taste discrimination capacities drive the N-Av to consume less nicotine. Would Av and N-Av mice avoid quinine differently after the 20-day nicotine paradigm? Would the authors observe individual nicotine drinking behaviors if nicotine/quinine vs. quinine were offered to the mice?

As requested by all three reviewers, we have now performed a two-bottle choice experiment to verify whether different sensitivities to the bitterness of the nicotine solution could explain the different sensitivities to the aversive properties of nicotine. Indeed, even though we used saccharine to mask the bitterness of the nicotine solution, we cannot fully exclude the possibility that the taste capacity of the mice could affect their nicotine consumption. Reviewers 1 and 2 suggested to perform nicotine/quinine versus quinine preference tests, but we were afraid that forcing mice to drink an aversive, quinine-containing solution might affect the total volume of liquid consumed per day, and also might create a “generalized conditioned aversion to drinking water - detrimental to overall health and a confounding factor” as pointed out by reviewer 3. Therefore, we designed the experiment a little differently.

In this two-bottle choice experiment, mice were first proposed a high concentration of nicotine (100 µg/ml) which has previously been shown to induce avoidance behavior in mice (Figure 3C). Then, mice were offered three increasing concentrations of quinine: 30, 100 and 300 µM. Quinine avoidance was dose dependent, as expected: it was moderate for 30 µM but almost absolute for 300 µM quinine. We then investigated whether nicotine and quinine avoidances were linked. We found no correlation between nicotine and quinine preference (new Figure: Figure 1- supplementary figure 1D). This new experiment strongly suggests that aversion to the drug is not directly tied to the sensitivity of mice to the bitter taste of nicotine.

Other results reinforce this conclusion. First, none of the b4-/- mice (0/13) showed aversion to nicotine, whereas about half of the virally-rescued animals (8/17, b4 re-expressed in the IPN of b4-/- mice) showed nicotine aversion, a proportion similar to the one observed in WT mice. This experiment makes a clear, direct link between the expression of b4 nAChRs in the IPN and aversion to the drug.

Furthermore, we also verified that the sensitivity of b4-/- mice to bitterness is not different from that of WT mice (new Figure 4 – figure supplement 1B). This new result indicates that the reason why b4-/- mice consume more nicotine than WT mice is not because they have a reduced sensitivity bitterness.

Together, these new experiments strongly suggests that interindividual differences in sensitivity to the bitterness of nicotine play little role in nicotine consumption behavior in mice.

b) Metabolic variabilities amongst isogenic mice have been observed. Thus, while the mice consume different amounts of nicotine, changes in metabolic processes, thus blood nicotine concentrations, could explain differences in nicotine consumption and neurophysiology across individuals. The authors should control if the blood concentration of nicotine metabolites between N-Av and Av are similar when consuming identical amounts of nicotine (50ug/ml), different amounts (200ug/ml), and in response to an acute injection of a fixed nicotine quantity.

We agree with the reviewer that metabolic variabilities could explain (at least in part) the differences observed between avoiders and non-avoiders. But other factors could also play a role, such as stress level (there is a strong interaction between stress and nicotine addiction, as shown by our group (PMID: 29155800, PMID: 30361503) and others), hierarchical ranking, epigenetic factors etc… Our goal in this study is not to examine all possible sources of variability. What is striking about our results is that deletion of a single gene (encoding the nAChR b4 subunit) is sufficient to eliminate nicotine avoidance, and that re-expression of this receptor subunit in the IPN is sufficient to restore nicotine avoidance. In addition, we observe a strong correlation between the amplitude of nicotineinduced current in the IPN, and nicotine consumption. Therefore, the expression level of b4 in the IPN is sufficient to explain most of the behavioral variability we observe. We do not feel the need to explore variations in metabolic activities, which are (by the way) very expensive experiments. However, we have added a sentence in the discussion to mention metabolic variabilities as a potential source of variability in nicotine consumption.

2) Av mice exposed to nicotine_200ug/ml display minimal nicotine_50ug/ml consumption, yet would Av mice restore a percent nicotine consumption >20 when exposed to a more extended session at 50ug/kg? Such a data set will help identify and isolate learned avoidance processes from dose-dependent avoidance behaviors.

We have now performed an additional two-bottle choice experiment to examine an extended time at 50 µg/ml. But we also performed the experiment a little differently. We directly proposed a high nicotine concentration to mice (200 µg/ml), followed by 8 days at 50 µg/ml. We found that, overall, mice avoided the 200 µg/ml nicotine solution, and that the following increase in nicotine preference was slow and gradual throughout the eight days at 50 µg/ml (Figure 2-figure supplement 1C). This slow adjustment to a lower-dose contrasts with the rapid (within a day) change in intake observed when nicotine concentration increases (Figure 1-figure supplement 1A). About half of the mice (6/13) retained a steady, low nicotine preference (< 20%) throughout the eight days at 50 µg/ml, resembling what was observed for avoiders in Figure 2D. Together, these results suggest that some of the mice, the non-avoiders, rapidly adjust their intake to adapt to changes in nicotine concentration in the bottle. For avoiders, aversion for nicotine seems to involve a learning mechanism that, once triggered, results in prolonged cessation of nicotine consumption.

3) The author should further investigate the basal properties of IPn neuron in vivo firing rate activity recorded and establish if their spontaneous activity determines their nicotine responses in vivo, such as firing rate, ISI, tonic, or phasic patterns. These analyses will provide helpful information to the neurophysiologist investigating the function of IPn neurons and will also inform how chronic nicotine exposure shapes the IPn neurophysiological properties.

We have performed additional analyses of the in vivo recordings. First, we have built maps of the recorded neurons, and we show that there is no anatomical bias in our sampling between the different groups. The only condition for which we did not sample neurons similarly is when we compare the responses to nicotine in vivo in WT and b4-/- mice (Figure 4E). The two groups were not distributed similarly along the dorso-ventral axis (Figure 4-figure supplement 2B). Yet, we do not think that the difference in nicotine responses observed between WT and b4-/- mice is due to a sampling bias. Indeed, we found no link between the response to nicotine and the dorsoventral coordinates of the neurons, in any of the groups (MPNic and MP Sal in Figure 3-figure supplement 1D; WT and b4-/- mice in Figure 4-figure supplement 2C). Therefore, our different groups are directly comparable, and the conclusions drawn in our study fully justified.

As requested, we have looked at whether the basal firing rate of IPN neurons determines the response to nicotine and indeed, neurons with higher firing rate show greater change in firing frequency upon nicotine injection (Figure 3 -figure supplement 1G and Figure 4-figure supplement 2F). We have also looked at the effect of chronic nicotine on the spontaneous firing rate of IPN neurons (Figure 3 -figure supplement 1F) but found no evidence for a change in basal firing properties. Similarly, the deletion of b4 had no effect on the spontaneous activity of the recorded neurons (Figure 4-figure supplement 2F). Finally, we found no evidence for any link between the anatomical coordinates of the neurons and their basal firing rate (Figure 3-figure supplement 1E and Figure 4figure supplement 2D).

Reviewer #3 (Public Review):

The manuscript by Mondoloni et al characterizes two-bottle choice oral nicotine consumption and associated neurobiological phenotypes in the antiparticle nucleus (IPN) using mice. The paper shows that mice exhibit differential oral nicotine consumption and correlate this difference with nicotine-evoked inward currents in neurons of the IPN. The beta4 nAChR subunit is likely involved in these responses. The paper suggests that prolonged exposure to nicotine results in reduced nAChR functional responses in IPN neurons. Many of these results or phenotypes are reversed or reduced in mice that are null for the beta4 subunit. These results are interesting and will add a contribution to the literature. However, there are several major concerns with the nicotine exposure model and a few other items that should be addressed.

Strengths:

Technical approaches are well-done. Oral nicotine, electrophysiology, and viral re-expression methods were strong and executed well. The scholarship is strong and the paper is generally well-written. The figures are high-quality.

We would like to thank the reviewer for his/her comments and suggestions on how to improve the manuscript.

Weaknesses:

Two bottle choice (2BC) model. 2BC does not examine nicotine reinforcement, which is best shown as a volitional preference for the drug over the vehicle. Mice in this 2BC assay (and all such assays) only ever show indifference to nicotine at best - not preference. This is seen in the maximal 50% preference for the nicotine-containing bottle. 2BC assays using tastants such as saccharin are confounded. Taste responses can very likely differ from primary reinforcement and can be related to peripheral biology in the mouth/tongue rather than in the brain reward pathway.

The two-bottle nicotine drinking test is a commonly used method to study addiction in mice (Matta, S. G. et al. 2006. Guidelines on nicotine dose selection for in vivo research. Psychopharmacology 190, 269–319). Like all methods, it has its limitations, but it also allows for different aspects to be addressed than those covered by selfadministration protocols. The two-bottle nicotine drinking test simply measures the animals' preference for a solution containing nicotine over a control solution without nicotine: the animals are free to choose nicotine or not, which allows to evaluate sensitivity and avoidance thresholds. What we show in this paper is precisely that despite interindividual differences in the way the drug is used (passively or actively), a significant proportion of the animals avoids the nicotine bottle at a certain concentration, suggesting that we are dealing with individual characteristics that are interesting to identify in the context of addiction and vulnerability. We agree that the twobottle choice test cannot provide as much information about the reinforcing effects of the drug as selfadministration procedures. We are aware of the limitations of the method and were careful not to interpret our data in terms of reinforcement to the drug. For instance, mice that consume nicotine were called “non-avoiders” and not “consumers”. We added a few sentences at the beginning of the discussion to highlight these limitations.

The reviewer states that the mice in this 2BC assay (and all such assays) “only ever show indifference to nicotine at best - not preference”. This is seen in the maximal 50% preference for the nicotine-containing bottle. While this is true on average, it isn’t when we look at individual profiles, as we did here. We clearly observed that some mice have a strong preference for nicotine and, conversely, that some mice actively avoid nicotine after a certain concentration is proposed in the bottle.

Regarding tastants, we indeed used saccharine to hide the bitter taste of nicotine and prevent taste-related side bias. This is a classical (though not perfect) paradigm in the field of nicotine research (Matta, S. G. et al. 2006. Guidelines on nicotine dose selection for in vivo research. Psychopharmacology 190, 269–319). To evaluate whether different sensitivities to the bitterness of nicotine may explain the interindividual differences in nicotine consumption we performed new experiments (as suggested by all three reviewers). In this two-bottle choice experiment, mice were first proposed a high concentration of nicotine (100 µg/ml) which has previously been shown to induce avoidance behavior in mice (Figure 3C). Then, mice were offered three increasing concentrations of quinine: 30, 100 and 300 µM. Quinine avoidance was dose dependent, as expected: it was moderate for 30 µM but almost absolute for 300 µM quinine. We then investigated whether nicotine and quinine avoidances were linked. We found no correlation between nicotine and quinine preference (new Figure: Figure 1- supplementary figure 1D). This new experiment strongly suggests that aversion to the drug is not directly tied to the sensitivity of mice to the bitter taste of nicotine. Other results reinforce this conclusion. First, none of the b4-/- mice (0/13) showed aversion to nicotine, whereas about half of the virally-rescued animals (8/17, b4 re-expressed in the IPN of b4-/- mice) showed nicotine aversion, a proportion similar to the one observed in WT mice. This experiment makes a clear, direct link between the expression of b4 nAChRs in the IPN and aversion to the drug. Furthermore, we also verified that the sensitivity of b4-/- mice to bitterness is not different from that of WT mice (new Figure 4 - figure supplement 1B). This new result indicates that the reason why b4-/- mice consume more nicotine than WT mice is not because they have a reduced sensitivity bitterness. Together, these new experiments strongly suggests that interindividual differences in sensitivity to the bitterness of nicotine play little role in nicotine consumption behavior in mice.

Moreover, this assay does not test free choice, as nicotine is mixed with water which the mice require to survive. Since most concentrations of nicotine are aversive, this may create a generalized conditioned aversion to drinking water - detrimental to overall health and a confounding factor.

Mice are given a choice between two bottles, only one of which contains nicotine. Hence, even though their choices are not fully free (they are being presented with a limited set of options), mice can always decide to avoid nicotine and drink from the bottle containing water only. We do not understand how this situation may create a generalized aversion to drinking. In fact, we have never observed any mouse losing weight or with deteriorated health condition in this test, so we don’t think it is a confounding factor.

What plasma concentrations of nicotine are achieved by 2BC? When nicotine is truly reinforcing, rodents and humans titrate their plasma concentrations up to 30-50 ng/mL. The Discussion states that oral self-administration in mice mimics administration in human smokers (lines 388-389). This is unjustified and should be removed. Similarly, the paragraph in lines 409-423 is quite speculative and difficult or impossible to test. This paragraph should be removed or substantially changed to avoid speculation. Overall, the 2BC model has substantial weaknesses, and/or it is limited in the conclusions it will support.

The reviewer must have read another version of our article, because these sentences and paragraphs are not present in our manuscript.

Regarding the actual concentration of nicotine in the plasma, this is indeed a good question. We have actually measured the plasma concentrations of nicotine for another study (article in preparation). The results from this experiment can be found below. The half-life of nicotine is very short in the blood and brain of mice (about 6 mins, see Matta, S. G. et al. 2006. Guidelines on nicotine dose selection for in vivo research. Psychopharmacology 190, 269–319), making it very hard to assess. Therefore, we also assessed the plasma concentration of cotinine, the main metabolite of nicotine. We compared 4 different conditions: home-cage (forced drinking of 100 ug/ml nicotine solution); osmotic minipump (OP, 10 mg/kg/d, as in our current study); Souris-city (a large social environment developed by our group, see Torquet et al. Nat. Comm. 2018); and the two-bottle choice procedure (when a solution of nicotine 100 ug/ml was proposed). The concentrations of plasma nicotine found were very low for all groups that drank nicotine, but not for the group that received nicotine through the osmotic minipump group. This is most likely because mice did not drink any nicotine in the hour prior to being sampled and all nicotine was metabolized. Indeed, when we look at the plasma concentration of cotinine, we see that cotinine was present in all of the groups. The plasma concentration of cotinine was similar in the groups for which “consumption” was forced: forced drinking in the home cage (HC) or infusion through osmotic minipump. This indicates that the plasma concentration of cotinine is similar whether mice drink nicotine (100 ug/ml) or whether nicotine is infused with the minipump (10 mg/kg/d). For Souris city and the two-bottle choice procedure, the cotinine concentrations were in the same range (mostly between 0-100 ng/ml). Globally, the concentrations of nicotine and cotinine found in the plasma of mice that underwent the two-bottle choice procedure are in the range of what has been previously described (Matta, S. G. et al. 2006. Guidelines on nicotine dose selection for in vivo research. Psychopharmacology 190, 269–319).

Regarding the limitations of the two-bottle choice test, we discuss them more extensively in the current version of the manuscript.

Statistical testing on subgroups. Mice are run through an assay and assigned to subgroups based on being classified as avoiders or non-avoiders. The authors then perform statistical testing to show differences between the avoiders and non-avoiders. It is circular to do so. When the authors divided the mice into avoiders and non-avoiders, this implies that the mice are different or from different distributions in terms of nicotine intake. Conducting a statistical test within the null hypothesis framework, however, implies that the null hypothesis is being tested. The null hypothesis, by definition, is that the groups do NOT differ. Obviously, the authors will find a difference between the groups in a statistical test when they pre-sorted the mice into two groups, to begin with. Comparing effect sizes or some other comparison that does not invoke the null hypothesis would be appropriate.

Our analysis, which can be summarized as follows, is fairly standard (see Krishnan, V. et al. (2007) Molecular adaptations underlying susceptibility and resistance to social defeat in brain reward regions. Cell 131, 391–404). Firstly, the mice are segregated into two groups based on their consumption profile, using the variability in their behavior. The two groups are obviously statistically different when comparing their consumption. This first analytical step allows us to highlight the variability and to establish the properties of each sub-population in terms of consumption. Our analysis could support the reviewer's comment if it ended at this point. However, our analysis doesn't end here and moves on to the second step. The separation of the mice into two groups (which is now a categorical variable) is used to compare the distribution of other variables, such as mouse choice strategy and current amplitude, based on the 2 categories. The null hypothesis tested is that the value of these other variables is not different between groups. There is no a priori obvious reason for the currents recorded in the IPN to be different in the two groups. These approaches allow us to show correlations between the variables. Finally, in the third and last step, one (or several) variable(s) are manipulated to check whether nicotine consumption is modified accordingly. Manipulation was performed by exposing mice to chronic nicotine, by using mutant mice with decreased nicotinic currents, and by re-expressing the deleted nAChR subunit only in the IPN. This procedure is fairly standard, and cannot be considered as a circular analysis with data selection problem, as explained in (Kriegeskorte, N., Simmons, W. K., Bellgowan, P. S. F. & Baker, C. I. (2009) Circular analysis in systems neuroscience: the dangers of double dipping. Nature Neuroscience 12, 535-540).

Decreased nicotine-evoked currents following passive exposure to nicotine in minipumps are inconsistent with published results showing that similar nicotine exposure enhances nAChR function via several measures (Arvin et al, J Neurosci, 2019). The paper does acknowledge this previous paper and suggests that the discrepancy is explained by the fact that they used a higher concentration of nicotine (30 uM) that was able to recruit the beta4containing receptor (whereas Arvin et al used a caged nicotine that was unable to do so). This may be true, but the citation of 30 uM nicotine undercuts the argument a bit because 30 uM nicotine is unlikely to be achieved in the brain of a person using tobacco products; nicotine levels in smokers are 100-500 nM. It should be noted in the paper that it is unclear whether the down-regulated receptors would be active at concentrations of nicotine found in the brain of a smoker.

We indeed find opposite results compared to Arvin et al., and we give possible explanations for this discrepancy in the discussion. To be honest we don’t fully understand why we have opposite results. However, we clearly observed a decreased response to nicotine, both in vitro (with 30 µM nicotine on brain slices) and in vivo (with a classical dose of 30 µg/kg nicotine i.v.), while Arvin et al. only tested nicotine in vitro.

Regarding the reviewer’s comment about the nicotine concentration used (30 µM): we used that concentration in vitro to measure nicotine-induced currents (it’s a concentration close to the EC50 for heteromeric receptors, which will likely recruit low affinity a3b4 receptors) and to evaluate the changes in nAChR current following nicotine exposure. We did not use that concentration to induce nAChR desensitization, so we don’t really understand the argument regarding the levels of nicotine in smokers. For inducing desensitization, we used a minipump that delivers a daily dose of 10 mg/kg/day, which is the amount of nicotine mice drink in our assay.

The statement in lines 440-41 ("we show that concentrations of nicotine as low as 7.5 ug/kg can engage the IPN circuitry") is misleading, as the concentration in the water is not the same as the concentration in the CSF since the latter would be expected to build up over time. The paper did not provide measurements of nicotine in plasma or CSF, so concluding that the water concentration of nicotine is related to plasma concentrations of nicotine is only speculative.

The sentence “we show that concentrations of nicotine as low as 7.5 ug/kg can engage the IPN circuitry" is not in the manuscript so the reviewer must have read another version of the paper.

The results in Figure 2E do not appear to be from a normal distribution. For example, results cluster at low (~100 pA) responses, and a fraction of larger responses drive the similarities or differences.

Indeed, that is why we performed a non-parametric Mann-Whitney test for comparing the two groups, as indicated in the legend of figure 2E.

10 mg/kg/day in mice or rats is likely a non-physiological exposure to nicotine. Most rats take in 1.0 to 1.5 mg/kg over a 23-hour self-administration period (O'Dell, 2007). Mice achieve similar levels during SA (Fowler, Neuropharmacology 2011). Forced exposure to 10 mg/kg/day is therefore 5 to 10-fold higher than rodents would ever expose themselves to if given the choice. This should be acknowledged in a limitations section of the Discussion.

The two-bottle choice task is very different from nicotine self-administration procedures in terms of administration route: oral versus injected (in the blood or in the brain), respectively. Therefore, the quantities of drug consumed cannot be directly compared. In our manuscript, mice consume on average 10 mg/kg/day of nicotine at the highest nicotine concentration tested, which is fully consistent with what was already published in many studies (20 mg/kg/day in Frahm et al. Neuron 2013, 5-10 mg/kg/day in Bagdas et al., NP 2020, 10-20 mg/kg/day in Bagdas et al. NP2019, to cite a few...). Hence, we used that concentration of nicotine (10 mg/kg/d) for chronic administration of nicotine using minipumps. This is also a nicotine concentration that is classically used in osmotic minipumps for chronic administration of nicotine: 10 mg/kg/d in Dongelmans et al. Nat. Com 2021 (our lab), 12 mg/kg/d in Arvin et al. J. Neuro. 2019 (Drenan lab), 12 mg/kg/d in Lotfipour et al. J. Neuro. 2013 (Boulter lab) etc… Therefore, we do not see the issue here.

Are the in vivo recordings in IPN enriched or specific for cells that have a spontaneous firing at rest? If so, this may or may not be the same set/type of cells that are recorded in patch experiments. The results could be biased toward a subset of neurons with spontaneous firing. There are MANY different types of neurons in IPN that are largely intermingled (see Ables et al, 2017 PNAS), so this is a potential problem.

It is true that there are many types of neurons in the IPN. In-vivo electrophysiology and slice electrophysiology should be considered as two complementary methods to obtain detailed properties of IPN neurons. The populations sampled by these two methods are certainly not identical (IPR in patch -clamp versus mostly IPR and IPC in vivo), and indeed only spontaneously active neurons are recorded in in-vivo electrophysiology. The question is whether this is or not a potential problem. The results we obtained using in-vivo and brain-slice electrophysiology are consistent (i.e., a decreased response to nicotine), which indicates that our results are robust and do not depend on the selection of a particular subpopulation. In addition, we now provide the maps of the neurons recorded both in slices and in vivo (see supplementary figures, and response to the other two referees). We show that, overall, there is no bias sampling between the different groups. Together, these new analyses strongly suggest that the differences we observe between the groups are not due to sampling issues. We have added the Ables 2017 reference and are discussing neuron variability more extensively in the revised manuscript.

Related to the above issue, which of the many different IPN neuron types did the group re-express beta4? Could that be controlled or did beta4 get re-expressed in an unknown set of neurons in IPN? There is insufficient information given in the methods for verification of stereotaxic injections.

Re-expression of b4 was achieved with a strong, ubiquitous promoter (pGK), hence all cell types should in principle be transduced. This is now clearly stated in the result section, the figure legend and the method section. Unfortunately, we had no access to a specific mouse line to restrict expression of b4 to b4-expressing cells, since the b4-Cre line of GENSAT is no more alive. This mouse line was problematic anyways because expression levels of the a3, a5 and b4 nAChR subunits, which belong to the same gene cluster, were reported to be affected. Yet, we show in this article that deleting b4 leads to a strong reduction of nicotine-induced currents in the IPR (80%, patch-clamp), and of the response to nicotine in vivo (65%). These results indicate that b4 is strongly expressed in the IPN, likely in a large majority of IPR and IPC neurons (see also our response to reviewer 1). In addition, we show that our re-expression strategy restores nicotine-induced currents in patch-clamp experiments and also the response to nicotine in vivo (new Figure 5C). Non-native expression levels could potentially be achieved (e.g. overexpression) but this is not what we observed: responses to nicotine were restored to the WT levels (in slices and in vivo). And importantly this strategy rescued the WT phenotype in terms of nicotine consumption. Expression of b4 alone in cells that do not express any other nAChR subunit (as, presumably, in the lateral parts of the IPN, see GENSAT images above) should not produce any functional nAChR, since alpha subunits are mandatory to produce functional receptors. As specified in the manuscript, proper transduction of the IPN was verified using post-hoc immunochemistry, and mice with transduction of b4 in the VTA were excluded from the analyses.

Data showing that alpha3 or beta4 disruption alters MHb/IPN nAChR function and nicotine 2BC intake is not novel. In fact, some of the same authors were involved in a paper in 2011 (Frahm et al., Neuron) showing that enhanced alpha3beta4 nAChR function was associated with reduced nicotine consumption. The present paper would therefore seem to somewhat contradict prior findings from members of the research group.

Frahm et al used a transgenic mouse line (called TABAC) in which the expression of a3b4 receptor is increased, and they observed reduced nicotine consumption. We do the exact opposite: we reduce (a3)b4 receptor expression (using the b4 knock-out line, or by putting mice under chronic nicotine), and observe increased consumption. There is thus no contradiction. In fact, we discuss our findings in the light of Frahm et al. in the discussion section.

Sex differences. All studies were conducted in male mice, therefore nothing was reported regarding female nicotine intake or physiology responses. Nicotine-related biology often shows sex differences, and there should be a justification provided regarding the lack of data in females. A limitations section in the Discussion section is a good place for this.

We agree with the reviewer. We added a sentence in the discussion.

Author Response

Reviewer #2 (Public Review):

We are in a golden age for comparative genomics and this is a prime example of the utility of the field. "Vision-related convergent gene losses reveal SERPINE3's unknown role in the eye" details the discovery of a function for a previously uncharacterized gene in regulating organ development in evolution. The authors intersect patterns of gene loss, quantified as the percentage of intact coding sequence, with visual acuity scores across Mammalia. This analysis identified 26 significant genes that have undergone convergent loss with phenotypic decreases of vision. Many of those genes have previously been annotated in the eye, indicating the analysis was successful and suggesting the uncharacterized genes may also have roles there.

The authors ruled out the top hit due to its specific expression in the testis, and instead performed an in-depth characterization of the second hit, SERPINE3. This included an impressive breadth of comparative genomics across 430 placental mammals, carefully describing the many and diverse genetic perturbations of SERPINE3 in lineages with low visual acuity. These results are persuasive that SERPINE3 is involved in vision, and it is a great example and description of gene loss in adaptation.

Critically, the authors validated the role of SERPINE3 in eye structure by confirming expression patterns in the eye, and characterizing its knockout in zebrafish, demonstrating both qualitative and quantitative impairments to eye structure. This is particularly satisfying as many comparative genomics make such associations but never validate the result. Here, validation of SERPINE3 was an undeniable success and puts a functional annotation to a previously uncharacterized gene. The utility of comparative genomics and zebrafish genetic models has been expertly capitalized upon and there is no doubt our knowledge of eye genetics has increased.

We thank the reviewer for these kind words and the valuable comments that we addressed below.

While these end results are certainly valuable to the community, details regarding the statistics and filters underlying the initial convergence analysis are too sparse to interpret. The impressive false discovery rate of the top hits is called into question when the top hit (corrected p-value < 1.1E-15 with visual acuity < 2) is subsequently skipped due to its specific expression in the testes. Given this disconnect, and without knowing the rationale and consequences of the various filters, it is difficult to get a sense of the accuracy and robustness of these p-values. Plots of p-value distributions across the dataset would demonstrate the method is statistically sound and would provide the backdrop to interpret the top hits of interest.

We have now simplified the workflow to detect convergent gene losses in species with lower visual acuity values and explained the rationale of each step (this is detailed in the responses below). We would like to mention that our screen may find genes that are associated with other phenotypes that are shared between species exhibiting lower visual acuity values. For example, several of these species are subterranean mammals, which share other traits and adaptations to their environment. While we do not know to which trait the loss of the testis gene TSACC is associated with, its FDR is only slightly lower than the FDR of the second-ranked SERPINE3 (FDR 1.1E-6 vs. 1.5E-6).

As suggested, we plotted the distribution of the raw P-values of all 13172 genes for which we ran the phylogenetic least square approach. This distribution has a peak at low P-values, indicating that some genes are preferentially lost in the poor-vision mammals. The distribution also showed a peak at ~0.5 and at ~1. We investigated which patterns of the %intact reading frame values appear to contribute to these two peaks.

Many genes with P-values of ~0.5 have one high-acuity species (blue), where the %intact value is slightly reduced, whereas other high- and poor-acuity (red) species all have a 100% intact reading frame. Two examples, where rhesus or dolphin have lower %intact values are shown below:

Similarly, many genes with P-values of ~1 have two or more high-acuity species, where the %intact value is reduced, whereas all other species have a 100% intact reading frame.

Since these genes have lower %intact values in a few high-acuity species, the high P-values likely capture a negative association with our trait of interest. While it is not clear why many P-values are around 0.5 or 1, it is clear that these genes are not associated with poor vision.

Our main purpose of using the phylogenetic least square approach was to rank the genes by their association with the poor vision phenotype. Importantly, the top-ranked candidates are all preferentially lost in low-acuity mammals, which is evident from Figure 1A. Furthermore, for SERPINE3, where we experimentally confirmed an eye-related function, three different screens with different phenotype definitions robustly support a preferential loss in low-acuity species (detailed below).

Notes on how many genes pass each filter, and what kinds of genes, would allow interpretation of possible bias in those filters and how they interact with the convergence analysis.

We thank the reviewer for this suggestion. As detailed below, we have now simplified the filtering procedure, justified the filter steps in the revised methods section, and added a flowchart (Figure 1 - supplement figure 1) describing each step and how many genes passed each filter (below).

For instance, the slight changes in visual acuity cutoffs have non-obvious operational consequences for vision, yet large impacts on the resulting gene lists, making it difficult to interpret how the measure is functioning. Most importantly, a negative control in the convergence analysis, demonstrating a null p-value distribution with the same filters, would assuage most concerns.

The reviewer is correct that changes in the visual acuity cutoff leads to different gene lists because the screen searches for genes preferentially lost in different species. However, our screens using three visual acuity cutoffs consistently find SERPINE3 as a candidate in the top 8 genes (Figure 1 - source data 5,6), showing that the association with lower visual acuity is robust for this gene.

As suggested, we have now run a negative control screen. For the negative control, we considered close relatives of the low-acuity species as trait-loss species. Specifically, we selected elephant, rhinoceros, horse, the two flying foxes, guinea pig, degu and squirrel. These 8 species represent five independent lineages. All other species (including the low-acuity species) were treated as trait-preserving species. A Forward genomics screen with otherwise identical filter parameters retrieved only two hits, TUBAL3 and TRIM52, which have no known function in the eye. This supports the specificity of our screen.

We added this to the main text:

“To confirm the specificity of these results, we performed a control screen for genes that are preferentially lost in high-acuity sister species of the low-acuity mammals. This control screen retrieved only two genes, none of which have known functions in the eye (Figure 1 - source data 4). Together, this shows that our genome-wide screen for genes preferentially lost in low-acuity species successfully retrieved known vision-related genes.”

and Methods:

“As a control to ensure that a Forward Genomics screen does not always retrieve vision-related genes, we ran a new screen, searching for genes preferentially lost in high-acuity sister species (elephant, rhinoceros, horse, two flying foxes, guinea pig, degu, squirrel) of the low-acuity mammals that we used in the original screen. All other species including the other high-acuity mammals were then treated as background (Figure 1 - source data 4).“

Author Response

Reviewer #1 (Public Review):

1) Although I found the introduction well written, I think it lacks some information or needs to develop more on some ideas (e.g., differences between the cerebellum and cerebral cortex, and folding patterns of both structures). For example, after stating that "Many aspects of the organization of the cerebellum and cerebrum are, however, very different" (1st paragraph), I think the authors need to develop more on what these differences are. Perhaps just rearranging some of the text/paragraphs will help make it better for a broad audience (e.g., authors could move the next paragraph up, i.e., "While the cx is unique to mammals (...)").

We have added additional context to the introduction and developed the differences between cerebral and cerebellar cortex, also re-arranging the text as suggested.

2) Given that the authors compare the folding patterns between the cerebrum and cerebellum, another point that could be mentioned in the introduction is the fact that the cerebellum is convoluted in every mammalian species (and non-mammalian spp as well) while the cerebrum tends to be convoluted in species with larger brains. Why is that so? Do we know about it (check Van Essen et al., 2018)? I think this is an important point to raise in the introduction and to bring it back into the discussion with the results.

We now mention in the introduction the fact that the cerebellum is folded in mammals, birds and some fishes, and provide references to the relevant literature. We have also expanded our discussion about the reasons for cortical folding in the discussion, which now contains a subsection addressing the subject (this includes references to the work of Van Essen).

3) In the results, first paragraph, what do the authors mean by the volume of the medial cerebellum? This needs clarification.

We have modified the relevant section in the results, and made the definition of the medial cerebellum more clear indicating that we refer to the vermal region of the cerebellum.

4) In the results: When the authors mention 'frequency of cerebellar folding', do they mean the degree of folding in the cerebellum? At least in non-mammalian species, many studies have tried to compare the 'degree or frequency of folding' in the cerebellum by different proxies/measurements (see Iwaniuk et al., 2006; Yopak et al., 2007; Lisney et al., 2007; Yopak et al., 2016; Cunha et al., 2022). Perhaps change the phrase in the second paragraph of the result to: "There are no comparative analyses of the frequency of cerebellar folding in mammals, to our knowledge".

We have modified the subsection in the methods referring to the measurement of folial width and folial perimeter to make the difference more clear. The folding indices that have been used previously (which we cite) are based on Zilles’s gyrification index. This index provides only a global idea of degree of folding, but it’s unable to distinguish a cortex with profuse shallow folds from one with a few deep ones. An example of this is now illustrated in Fig. 3d, where we also show how that problem is solved by the use of our two measurements (folial width and perimeter). The problem is also discussed in the section about the measurement of folding in the discussion section:

“Previous studies of cerebellar folding have relied either on a qualitative visual score (Yopak et al. 2007, Lisney et al. 2008) or a “gyrification index” based on the method introduced by Zilles et al. (1988, 1989) for the study of cerebral folding (Iwaniuk et al. 2006, Cunha et al. 2020, 2021). Zilles’s gyrification index is the ratio between the length of the outer contour of the cortex and the length of an idealised envelope meant to reflect the length of the cortex if it were not folded. For instance, a completely lissencephalic cortex would have a gyrification index close to 1, while a human cerebral cortex typically has a gyrification index of ~2.5 (Zilles et al. 1988). This method has certain limitations, as highlighted by various researchers (Germanaud et al. 2012, 2014, Rabiei et al. 2018, Schaer et al. 2008, Toro et al. 2008, Heuer et al. 2019). One important drawback is that the gyrification index produces the same value for contours with wide variations in folding frequency and amplitude, as illustrated in Fig. 3d. In reality, folding frequency (inverse of folding wavelength) and folding amplitude represent two distinct dimensions of folding that cannot be adequately captured by a single number confusing both dimensions. To address this issue we introduced 2 measurements of folding: folial width and folial perimeter. These measurements can be directly linked to folding frequency and amplitude, and are comparable to the folding depth and folding wavelength we introduced previously for cerebral 3D meshes (Heuer et al. 2019). By using these measurements, we can differentiate folding patterns that could be confused when using a single value such as the gyrification index (Fig. 3d). Additionally, these two dimensions of folding are important, because they can be related to the predictions made by biomechanical models of cortical folding, as we will discuss now.”

5) Sultan and Braitenberg (1993) measured cerebella that were sagittally sectioned (instead of coronal), right? Do you think this difference in the plane of the section could be one of the reasons explaining different results on folial width between studies? Why does the foliation index calculated by Sultan and Braitenberg (1993) not provide information about folding frequency?

The measurement of foliation should be similar as far as enough folds are sectioned perpendicular to their main axis. This will be the case for folds in the medial cerebellum (vermis) sectioned sagittally, and for folds in the lateral cerebellum sectioned coronally. The foliation index of Sultan and Braitenberg does not provide a similar account of folding frequency as we do because they only measure groups of folia (what some called lamellae), whereas we measure individual folia. It is not easy to understand exactly how Sultan and Braitenberg proceeded from their paper. We contacted Prof. Fahad Sultan (we acknowledge his help in our manuscript). Author response image 1 provides a more clear description of their procedure:

Author response image 1.

As Author response image 1 shows, each of the structures that they call a fold is composed of several folia, and so their measurements are not comparable with ours which measure individual folia (a). The flattened representation (b) is made by stacking the lengths of the fold axes (dashed lines), separating them by the total length of each fold (the solid lines), which each may contain several folia.

6) Another point that needs to be clarified is the log transformation of the data. Did the authors use log-transformed data for all types of analyses done in the study? Write this information in the material and methods.

Yes, we used the log10 transformation for all our measurements. This is now mentioned in the methods section, and again in the section concerning allometry. We are including a link to all our code to facilitate exact replication of our entire method, including this transformation.

7) The discussion needs to be expanded. The focus of the paper is on the folding pattern of the cerebellum (among different mammalian species) and its relationship with the anatomy of the cerebrum. Therefore, the discussion on this topic needs to be better developed, in my opinion (especially given the interesting results of this paper). For example, with the findings of this study, what can we say about how the folding of the cerebellum is determined across mammals? The authors found that the folial width, folial perimeter, and thickness of the molecular layer increase at a relatively slow rate across the species studied. Does this mean that these parameters have little influence on the cerebellar folding pattern? What mostly defines the folding patterns of the cerebellum given the results? Is it the interaction between section length and area? Can the authors explain why size does not seem to be a "limiting factor" for the folding of the cerebellum (for example, even relatively small cerebella are folded)? Is that because the 'white matter' core of the cerebellum is relatively small (thus more stress on it)?

We have expanded the discussion as suggested, with subsections detailing the measuring of folding, the modelling of folding for the cerebrum and the cerebellum, and the role that cerebellar folding may play in its function. We refer to the literature on cortical folding modelling, and we discuss our results in terms of the factors that this research has highlighted as critical for folding. From the discussion subsection on models of cortical folding:

“The folding of the cerebral cortex has been the focus of intense research, both from the perspective of neurobiology (Borrell 2018, Fernández and Borrell 2023) and physics (Toro and Burnod 2005, Tallinen et al. 2014, Kroenke and Bayly 2018). Current biomechanical models suggest that cortical folding should result from a buckling instability triggered by the growth of the cortical grey matter on top of the white matter core. In such systems, the growing layer should first expand without folding, increasing the stress in the core. But this configuration is unstable, and if growth continues stress is released through cortical folding. The wavelength of folding depends on cortical thickness, and folding models such as the one by Tallinen et al. (2014) predict a neocortical folding wavelength which corresponds well with the one observed in real cortices. Tallinen et al. (2014) provided a prediction for the relationship between folding wavelength λ and the mean thickness (𝑡) of the cortical layer: λ = 2π𝑡(µ/(3µ𝑠))1/3. (...)”

From this biomechanical framework, our answers to the questions of the Reviewer would be:

• How is the folding of the cerebellum determined across mammals? By the expansion of a layer of reduced thickness on top of an elastic layer (the white matter)

• Folial width, folial perimeter, and thickness of the molecular layer increase at a relatively slow rate across the species studied. Does this mean that these parameters have little influence on the cerebellar folding pattern? On the contrary, that indicates that the shape of individual folia is stable, providing the smallest level of granularity of a folding pattern. In the extreme case where all folia had exactly the same size, a small cerebellum would have enough space to accommodate only a few folia, whereas a large cerebellum would accommodate many more.

• What mostly defines the folding patterns of the cerebellum given the results? Is it the interaction between section length and area? It’s the mostly 2D expansion of the cerebellar cortical layer and its thickness.

• Can the authors explain why size does not seem to be a "limiting factor" for the folding of the cerebellum? Because even a cerebellum of very small volume would fold if its cortex were thin enough and expanded sufficiently. That’s why the cerebellum folds even while being smaller than the cerebrum: because its cortex is much thinner.

8) One caveat or point to be raised is the fact that the authors use the median of the variables measured for the whole cerebellum (e.g., median width and median perimeter across all folia). Although the cerebellum is highly uniform in its gross internal morphology and circuitry's organization across most vertebrates, there is evidence showing that the cerebellum may be organized in different functional modules. In that way, different regions or folia of the cerebellum would have different olivo-cortico-nuclear circuitries, forming, each one, a single cerebellar zone. Although it is not completely clear how these modules/zones are organized within the cerebellum, I think the authors could acknowledge this at the end of their discussion, and raise potential ideas for future studies (e.g., analyse folding of the cerebellum within the brain structure - vermis vs lateral cerebellum, for example). I think this would be a good way to emphasize the importance of the results of this study and what are the main questions remaining to be answered. For example, the expansion of the lateral cerebellum in mammals is suggested to be linked with the evolution of vocal learning in different clades (see Smaers et al., 2018). An interesting question would be to understand how foliation within the lateral cerebellum varies across mammalian clades and whether this has something to do with the cellular composition or any other aspect of the microanatomy as well as the evolution of different cognitive skills in mammals.

We now address this point in a subsection of the discussion which details the implications of our methodological decisions and the limitations of our approach. It is true that the cerebellum is regionally variable. Our measurements of folial width, folial perimeter and molecular layer thickness are local, and we should be able to use them in the future to study regional variation. However, this comes with a number of difficulties. First, it would require sampling all the cerebellum (and the cerebrum) and not just one section. But even if that were possible that would increase the number of phenotypes, beyond the current scope of this study. Our central question about brain folding in the cerebellum compared to the cerebrum is addressed by providing data for a substantial number of mammalian species. As indicated by Reviewer #3, adding more variables makes phylogenetic comparative analyses very difficult because the models to fit become too large.

Reviewer #2 (Public Review):

1) The methods section does not address all the numerical methods used to make sense of the different brain metrics.

We now provide more detailed descriptions of our measurements of foliation, phylogenetic models, analysis of partial correlations, phylogenetic principal components, and allometry. We have added illustrations (to Figs. 3 and 5), examples and references to the relevant literature.

2) In the results section, it sometimes makes it difficult for the reader to understand the reason for a sub-analysis and the interpretation of the numerical findings.

The revised version of our manuscript includes motivations for the different types of analyses, and we have also added a paragraph providing a guide to the structure of our results.

3) The originality of the article is not sufficiently brought forward:

a) the novel method to detect the depth of the molecular layer is not contextualized in order to understand the shortcomings of previously-established methods. This prevents the reader from understanding its added value and hinders its potential re-use in further studies.

The revised version of the manuscript provides additional context which highlights the novelty of our approach, in particular concerning the measurement of folding and the use of phylogenetic comparative models. The limitations of the previous approaches are stated more clearly, and illustrated in Figs. 3 and 5.

b) The numerous results reported are not sufficiently addressed in the discussion for the reader to get a full grasp of their implications, hindering the clarity of the overall conclusion of the article.

Following the Reviewer’s advice, we have thoroughly restructured our results and discussion section.

Reviewer #3 (Public Review):

1) The first problem relates to their use of the Ornstein-Uhlenbeck (OU) model: they try fitting three evolutionary models, and conclude that the Ornstein-Uhlenbeck model provides the best fit. However, it has been known for a while that OU models are prone to bias and that the apparent superiority of OU models over Brownian Motion is often an artefact, a problem that increases with smaller sample sizes. (Cooper et al (2016) Biological Journal of the Linnean Society, 2016, 118, 64-77).

Cooper et al.’s (2016) article “A Cautionary Note on the Use of Ornstein Uhlenbeck Models in Macroevolutionary Studies” suggests that comparing evolutionary models using the model’s likelihood leads often to incorrectly selecting OU over BM even for data generated from a BM process. However, Grabowski et al (2023) in their article ‘A Cautionary Note on “A Cautionary Note on the Use of Ornstein Uhlenbeck Models in Macroevolutionary Studies”’ suggest that Cooper et al.’s (2016) claim may be misleading. The work of Clavel et al. (2019) and Clavel and Morlon (2017) shows that the penalised framework implemented in mvMORPH can successfully recover the parameters of a multivariate OU process. To address more directly the concern of the Reviewer, we used simulations to evaluate the chances that we would decide for an OU model when the correct model was BM – a similar procedure to the one used by Cooper et al.’s (2016). However, instead of using the likelihood of the fitted models directly as Cooper et al. (2016) – which does not control for the number of parameters in the model – we used the Akaike Information Criterion, corrected for small sample sizes: AICc. The standard Akaike Information Criterion takes the number of parameters of the model into account, but this is not sufficient when the sample size is small. AICc provides a score which takes both aspects into account: model complexity and sample size. This information has been added to the manuscript:

“We selected the best fitting model using the Akaike Information Criterion (AIC), corrected for 𝐴𝐼𝐶 = − 2 𝑙𝑜𝑔(𝑙𝑖𝑘𝑒𝑙𝑖ℎ𝑜𝑜𝑑) + 2 𝑝. This approximation is insufficient when the𝑝 sample size small sample sizes (AICc). AIC takes into account the number of parameters in the model: is small, in which case an additional correction is required, leading to the corrected AIC: 𝐴𝐼𝐶𝑐 = 𝐴𝐼𝐶 + (2𝑝2 + 2𝑝)/(𝑛 − 𝑝 − 1), where 𝑛 is the sample size.”

In 1000 simulations of 9 correlated multivariate traits for 56 species (i.e., 56*9 data points) using our phylogenetic tree, only 0.7% of the times we would decide for OU when the real model was BM.

2) Second, for the partial correlations (e.g. fig 7) and Principal Components (fig 8) there is a concern about over-fitting: there are 9 variables and only 56 data points (violating the minimal rule of thumb that there should be >10 observations per parameter). Added to this, the inclusion of variables lacks a clear theoretical rationale. The high correlations between most variables will be in part because they are to some extent measuring the same things, e.g. the five different measures of cerebellar anatomy which include two measures of folial size. This makes it difficult to separate their effects. I get that the authors are trying to tease apart different aspects of size, but in practice, I think these results (e.g. the presence of negative coefficients in Fig 7) are really hard or impossible to interpret. The partial correlation network looks like a "correlational salad" rather than a theoretically motivated hypothesis test. It isn't clear to me that the PC analyses solve this problem, but it partly depends on the aims of these analyses, which are not made very clear.

PCA is simply a rigid rotation of the data, distances among multivariate data points are all conserved. Neither our PCA nor our partial correlation analysis involve model fitting, the concept of overfitting does not apply. PCA and partial correlations are also not used here for hypothesis testing, but as exploratory methods which provide a transformation of the data aiming at capturing the main trends of multivariate change. The aim of our analysis of correlation structure is precisely to avoid the “correlational salad” that the Reviewer mentions. The Reviewer is correct: all our variables are correlated to a varying degree (note that there are 56 data points per variable = 56*9 data points, not just 56 data points). Partial correlations and PCA aim at providing a principled way in which correlated measurements can be explored. In the revised version of the manuscript we include a more detailed description of partial correlations and PCA (phylogenetic). Whenever variables measure the same thing, they will be combined into the same principal component (these are the combinations shown in Fig. 8 b and d). Additionally, two variables may be correlated because of their correlation with a third variable (or more). Partial correlations address this possibility by looking at the correlations between the residuals of each pair of variables after all other variables have been covaried out. We provide a simple example which should make this clear, providing in particular an intuition for the meaning of negative correlations:

“All our phenotypes were strongly correlated. We used partial correlations to better understand pairwise relationships. The partial correlation between 2 vectors of measurements a and b is the correlation between their residuals after the influence of all other measurements has been covaried out. Even if the correlation between a and b is strong and positive, their partial correlation could be 0 or even negative. Consider, for example, 3 vectors of measurements a, b, c, which result from the combination of uncorrelated random vectors x, y, z. Suppose that a = 0.5 x + 0.2 y + 0.1 z, b = 0.5 x - 0.2 y + 0.1 z, and c = x. The measurements a and b will be positively correlated because of the effect of x and z. However, if we compute the residuals of a and b after covarying the effect of c (i.e., x), their partial correlation will be negative because of the opposite effect of y on a and b. The statistical significance of each partial correlation being different than 0 was estimated using the edge exclusion test introduced by Whittaker (1990).”

The rationale for our analyses has been made more clear in the revised version of the manuscript, aided by the more detailed description of our methods. In particular, we describe better the reason for our 2 measurements of folial shape – width and perimeter – which measure independent dimensions of folding (this is illustrated in Fig. 3d).

3) The claim of concerted evolution between cortical and cerebellar values (P 11-12) seems to be based on analyses that exclude body size and brain size. It, therefore, seems possible - or even likely - that all these analyses reveal overall size effects that similarly influence the cortex and cerebellum. When the authors state that they performed a second PC analysis with body and brain size removed "to better understand the patterns of neuroanatomical evolution" it isn't clear to me that is what this achieves. A test would be a model something like [cerebellar measure ~ cortical measure + rest of the brain measure], and this would deal with the problem of 'correlation salad' noted below.

The answer to this question is in the partial correlation diagram in Fig. 7c. This analysis does not exclude body weight nor brain weight. It shows that the strong correlation between cerebellar area and length is supported by a strong positive partial correlation, as is the link between cerebral area and length. There is a significant positive partial correlation between cerebellar section area and cerebral section length. That is, even after covarying everything else, there is still a correlation between cerebellar section area and cerebral section length (this partial correlation is equivalent to the suggestion of the Reviewer). Additionally, there is a positive partial correlation between body weight and cerebellar section area, but not significant partial correlation between body weight and cerebral section area or length. Our approach aims at obtaining a general view of all the relationships in the data. Testing an individual model would certainly decrease the number of correlations, however, it would provide only a partial view of the problem.

4) It is not quite clear from fig 6a that the result does indeed support isometry between the data sets (predicted 2/3 slope), and no coefficient confidence intervals are provided.

We have now added the numerical values of the CIs to all our plots in addition to the graphical representations (grey regions) in the previous version of the manuscript. The isometry slope (0.67) is either within the CIs (both for the linear and orthogonal regressions) or at the margin, indicating that if the relationships are not isometric, they are very close to it.

Referencing/discussion/attribution of previous findings

5) With respect to the discussion of the relationship between cerebellar architecture and function, and given the emphasis here on correlated evolution with cortex, Ramnani's excellent review paper goes into the issues in considerable detail, which may also help the authors develop their own discussion: Ramnani (2006) The primate cortico-cerebellar system: anatomy and function. Nature Reviews Neuroscience 7, 511-522 (2006)

We have added references to the work of Ramnani.

6) The result that humans are outliers with a more folded cerebellum than expected is interesting and adds to recent findings highlighting evolutionary changes in the hominin human cerebellum, cerebellar genes, and epigenetics. Whilst Sereno et al (2020) are cited, it would be good to explain that they found that the human cerebellum has 80% of the surface area of the cortex.

We have added this information to the introduction:

“In humans, the cerebellum has ~80% of the surface area of the cerebral cortex (Sereno et al. 2020), and contains ~80% of all brain neurons, although it represents only ~10% of the brain mass (Azevedo et al. 2009)”

7) It would surely also be relevant to highlight some of the molecular work here, such as Harrison & Montgomery (2017). Genetics of Cerebellar and Neocortical Expansion in Anthropoid Primates: A Comparative Approach. Brain Behav Evol. 2017;89(4):274-285. doi: 10.1159/000477432. Epub 2017 (especially since this paper looks at both cerebellar and cortical genes); also Guevara et al (2021) Comparative analysis reveals distinctive epigenetic features of the human cerebellum. PLoS Genet 17(5): e1009506. https://doi.org/10.1371/journal. pgen.1009506. Also relevant here is the complex folding anatomy of the dentate nucleus, which is the largest structure linking cerebellum to cortex: see Sultan et al (2010) The human dentate nucleus: a complex shape untangled. Neuroscience. 2010 Jun 2;167(4):965-8. doi: 10.1016/j.neuroscience.2010.03.007.

The information is certainly important, and could have provided a wider perspective on cerebellar evolution, but we would prefer to keep a focus on cerebellar anatomy and address genetics only indirectly through phylogeny.

8) The authors state that results confirm previous findings of a strong relationship between cerebellum and cortex (P 3 and p 16): the earliest reference given is Herculano-Houzel (2010), but this pattern was discovered ten years earlier (Barton & Harvey 2000 Nature 405, 1055-1058. https://doi.org/10.1038/35016580; Fig 1 in Barton 2002 Nature 415, 134-135 (2002). https://doi.org/10.1038/415134a) and elaborated by Whiting & Barton (2003) whose study explored in more detail the relationship between anatomical connections and correlated evolution within the cortico-cerebellar system (this paper is cited later, but only with reference to suggestions about the importance of functions of the cerebellum in the context of conservative structure, which is not its main point). In fact, Herculano-Houzel's analysis, whilst being the first to examine the question in terms of numbers of neurons, was inconclusive on that issue as it did not control for overall size or rest of the brain (A subsequent analysis using her data did, and confirmed the partially correlated evolution - Barton 2012, Philos Trans R Soc Lond B Biol Sci. 367:2097-107. doi: 10.1098/rstb.2012.0112.)

We apologise for this oversight, these references are now included.

Author Response

Reviewer #1 (Public Review):

This study focuses on elucidating the function of CD59, a small GPI-anchored glycoprotein, in Schwann cell development. Patients with CD59 deficiency suffer from neurological dysfunctions, but the link between CD59 deficiency and the development of neurological dysfunctions remains unclear. To clarify this link, the authors used zebrafish as an animal model. They generated cd59 mutant zebrafish and studied their Schwann cell development. The authors started this study by showing CD59 expression data from different sources in the Schwann cell and oligodendrocyte lineages in zebrafish and mice. They continued by demonstrating that CD59 is expressed only by a subset of developing Schwann cells, which is very interesting conceptually for the identification of different Schwann cell populations and their specific functions and also for the potential development of future techniques targeting specific Schwann cell populations. However, since the authors focused in the following parts of the article on Schwann cell development, it is unclear why they have included data on oligodendrocytes at the start of the manuscript.

Thank you for this question. We included the data on oligodendrocytes because we wanted to be thorough and transparent. Additionally, because some of our own expression data show oligodendrocyte expression, we felt it was prudent to confirm this expression in published RNAseq datasets. Finally, we created and/or used tools to label cd59-positive cells, and we often used expression in both oligodendrocytes and Schwann cells as a readout of complete expression of these tools.

In this study, the authors show that cd59 ablation in zebrafish leads to increased Schwann cell proliferation between 48 and 55 hpf (hours post fertilization), which is quite convincing. However, they claim that this transient increase in proliferation leads to impaired myelination and node of Ranvier formation. Unfortunately, these findings remain correlative and it appears unclear why an increased number of Schwann cells that stop proliferating at the same time-point as wild type Schwann cells would impair myelination and node of Ranvier formation. This phenotype is attributed by the authors to increased proliferation of Schwann cells between 48 and 55 hpf, which seems rather unlikely or not supported by the data currently presented. The hypomyelination phenotype is rather mild, while the impairment of node of Ranvier formation seems quite strong - however, the data currently presented is not very convincing and needs improvement.

Thank you for your observations. With regards to how an increase in SC proliferation could impact myelination and node of Ranvier formation, although the rate of proliferation transiently increases, these excess SCs persist on the nerve. So, even though the mutants can stop developmental proliferation at the same stage, the mutants ultimately have more SCs on the nerve after proliferation has ceased. This raises the interesting question of how could more SCs lead to less myelin? To address this question, we added to the discussion to speculate on possible hypotheses as to why this is the case (please see line 510).

With regards to comparing the strength of the myelin phenotype and the node of Ranvier phenotype, there is no reason to suspect that there is a linear relationship between myelin volume and node of Ranvier assembly. We do know that myelination and SCs are necessary for node of Ranvier assembly. So, it is very possible that any perturbation in myelination could drastically affect node of Ranvier assembly. That said, this relationship is very interesting, and we hope that the cd59 mutant model can be utilized to further investigate these questions in future studies.

In regards to the node of Ranvier data itself, we have provided co-labeling of NF186 and NaV channels on mbpa:tagrfp-caax-positive nerves (see Figure 5 – figure supplement 1D). Using Imaris, we demonstrate that each NF186 cluster colocalizes with a NaV channel cluster. Furthermore, this colocalization only occurs within the myelinated nerve. Collectively, this data demonstrates that our quantification of nodes of Ranvier is reliable.

The data showing an increase of complement activation in cd59 mutants is also not very convincing and should be improved.

Thank you for sharing your concern. To address this issue, we have used Imaris to show MACs that are bound to SC membranes (see Figure 6B) for a clearer view of the data. Comparing wildtype and mutant larvae, there is a visible and significant increase in MAC binding to SC membranes when cd59 is perturbed. Additionally, we have included controls for these antibody labeling experiments to show specificity of these tools.

In addition, the link between increased complement activation and increased proliferation remains to be proven in the context of this study, and the choice of dexamethasone as an inhibitor of complement activation does not appear to be the best choice since it is not specific to the complement.

Thank you for sharing your concern. We agree that dexamethasone impacts other aspects of immune activation other than complement. With this in mind, we did test another drug called compstatin, which inhibits complement protein 3 (C3). Inhibition of C3 impairs all three complement pathways and would abrogate downstream assembly of MACs. Our preliminary data was very promising, demonstrating the same relationship that we see with our dexamethasone treatment (see below). However, we were unable to reproducibly get the same results in subsequent experiments after we purchased a new stock of this drug. To solve this problem, we tried compstatin from a different company as well as increasing the concentration, but none of our troubleshooting efforts yielded the same results that we had originally observed. Obviously, this is incredibly disappointing to us. So, although these results initially repeated, we did not feel it was ethical to publish this data. (In the figure below, wildtype and mutant embryos were treated with 1% DMSO or 50 µM compstatin in 1% DMSO from 24 hpf to 55 hpf. The number of SCs was quantified with a Sox10 antibody and confocal imaging at 55 hpf).

Given these technical limitations, we ultimately decided to include the dexamethasone experiments because they were reproducible. Considering the broader effects of dexamethasone on the immune system, we have softened our claims to include inflammation as well as complement activation. That said, we hope future studies will be able to use this model to gather more information on the specific pathways that are regulating Cd59-dependent SC proliferation.

Page 49, lines 437-439: Here the authors claim that their data "demonstrates that developmental inflammation aids in normal SC proliferation and that this process is amplified when cd59 is mutated." The data presented in Figure 6C-D and commented by the authors on page 49, lines 435-437, show however that "Dex treatment in cd59uva48 mutant embryos restored SC numbers to wildtype levels, whereas wildtype SCs were not significantly affected by Dex application". Dex (dexamethasone) was used here to inhibit inflammation and associated complement activation. Therefore, these data do not show that developmental inflammation aids in normal SC proliferation, but rather that it has no influence.

Thank you for your comment. When compared alone, there are significantly fewer SCs in dexamethasone-treated wildtype larvae compared to DMSO-treated wildtype larvae. We have updated the figure and text to better highlight this relationship (please see Figure 7A, C and line 457). We also quantified EdU incorporation into SCs treated with dexamethasone. Here we also observed a decrease in EdU-positive SCs in wildtype larvae treated with dexamethasone, supporting our observation that developmental inflammation is contributing to normal SC proliferation (please see Figure 7B, D).

Dexamethasone treatment: The authors claim that dexamethasone treatment, by decreasing inflammation and associated complement activation, leads to a decrease of SC proliferation in the cd59 mutant. To support this, there is only Figure 7-Figure Supplement 1 showing a decreased SC number in the mutant treated by dexamethasone as compared to vehicle-treated mutant. To strengthen this point, the authors also need to specifically quantify proliferation by EdU incorporation, as they did in Figure 4, and also cell death.

Thank you for your comment. We have added quantification of EdU incorporation after dex treatment (please see Figure 7B, D). Dr. Feltri, the Reviewing Editor, told us that measuring apoptosis after treatment was not necessary for the revision.

In addition, the mechanistic hypothesis of increased proliferation in cd59 mutant is that cd59 interferes with the activation of the complement and complement-induced pore formation in the plasma membrane. However, dexamethasone is not a specific inhibitor of the complement. Therefore, its potential effect on SC proliferation could be due to other effects than complement inactivation. It is unclear why the authors did not use an inhibitor of the complement that is more specific than dexamethasone.

Thank you for your comment. Please see our previous response to this comment.

Page 54, lines 456-457: The following statement "Collectively, these data demonstrate that inflammation-induced SC proliferation contributes to perturbed myelin and node of Ranvier development." is not accurate since these data remain correlative. Indeed, there is in this study nothing showing that increased SC proliferation between 48 and 55 hpf leads to perturbed myelin and node of Ranvier development. In addition, the term "inflammation" is not precise enough here. What the authors attempt to show is an increase of complement activation due to the absence of cd59 expression in SCs. The authors did not try to induce inflammation in wild type animals to see whether this induces proliferation and perturbed myelin and node of Ranvier development. They also did not try to directly knock down C8/C9 in cd59 mutants to see whether they would rescue the phenotype of the cd59 mutant, at least to some extent. In addition, their statement mentioned above needs to be more precise by stating that their findings apply to cd59 mutants and not to wild type animals.

Thank you for your comment. Please see our previous responses to these comments.

Reviewer #3 (Public Review):

Wiltbank and colleagues explore the function of CD59 in developmental Schwann cell myelination. Using previously published transcriptomics data sets they arrive at CD59 as a differentially expressed gene in myelinating glia. In addition, patients with pathogenic variants have neuropathy. The authors construct a transgenic zebrafish reporter line for cd59. Surprisingly, it labels a very, very small percentage of Schwann cells (less than 10% throughout development). The authors then construct several loss-of-function mutants for cd59. They report these mutants have increased numbers of Schwann cells, but nerves are smaller and EM shows they have reduced the number of myelin wraps. Consistent with impaired myelination they also observe fewer nodes of Ranvier. The authors suggest loss of cd59 results in increased MAC deposition on myelinating Schwann cells. Remarkably, using an inhibitor of inflammation (dexamethasone), the authors show that they can normalize/rescue the main phenotypes: 1) normalize the number of SCs, 2, dramatically improve myelination to normal nerve volumes, and 3) rescue node of Ranvier formation. This last experiment that rescues the phenotype is really terrific. The experiments are mostly very well done and the story is both interesting and conceptually novel. Nevertheless, there are a few points that I think the authors could address:

1) It is very surprising that the cd59 reporter line only showed expression in a small subset (10% or less) of Schwann cells. How do the authors explain the widespread effects? Similarly, the authors make a point of stating that motor Schwann cells did not express cd59. Did myelinated motor axons show the same phenotype - reduced myelination, impaired node formation? How can the expression of cd59 in only 10% of cells cause widespread effects throughout the nerve? How can it limit overproliferation if 9/10 cells don't even express it?

Thank you for the question. It is really interesting that a small subset of cells can have such a big impact on nerve development. One of our current hypotheses is that overproliferation of SCs has led to activation of contact-inhibition pathways, which in turn are negatively regulating myelination. We expand further on this hypothesis in our discussion (please see line 536). We also suggest questions addressing glial cell heterogeneity to explore in the future (please see line 603).

In regards to the motor nerves, we quantified the number of Sox10-positive cells (SCs and MEP glia) on motor nerves at 72 hpf and showed that there was no overproliferation of these cell types (please see Figure 4I, J). We have not observed any issues with motor nerve myelination, which is what we would expect if motor SC proliferation was unaffected. That said, these differences between motor and pLLN SCs are really interesting because it opens up discussion for glial cell heterogeneity between nerve types (e.g. sensory versus motor nerves). We see similar evidence of this in satellite glia that populate the cochlear spiral ganglion versus those that surround the dorsal root ganglia (see Tasdemir-Yilmaz et al. 2021 or Wiltbank and Kucenas 2021), so it makes sense that there could be some SC diversity between nerve types as well. We expand further on these ideas in our discussion (please see line 603).

2) It is surprising to me that there is a significant increase in SC proliferation, but no change in the length of myelin sheaths. Does this mean there are more SCs that remain unmyelinated and undifferentiated?

Thank you for your comment. We were also surprised. With our current tools, we are unable to determine the fate of these extra SCs but hope that future studies will be able to clarify this question. We have added discussion around this topic to the text (please see line 554).

3) The results showing deposition of the MAC (via C5b-9+C5b-8 immunostaining) are not convincing. The overall background level of immunostaining is dramatically increased. This result is central to the overall story in the paper. What controls were performed to confirm this doesn't simply reflect an overall higher background artifact during immunostaining?

Thank you for your comment. We have added our antibody controls to the supplemental figures (please see Figure 6 – figure supplement 1A) demonstrating that we can increase MAC deposition by inducing complement activation (either through heat-related damage or DNase-elicited DNA damage). We also do not observe signal when the primary antibody is not present. Based on our controls, we do not think the extra MAC labeling is background. Rather, we believe that MAC deposition has increased globally in the cd59 mutant embryos. This is not surprising given that complement activation leads to a positive feedback loop of more complement and immune activation, which is likely occurring in the cd59 mutants.

To help clarify the MAC data, we have also added Imaris renderings of the MACs that are bound to the SC membranes, demonstrating that there are more MACs embedded in the cd59 mutant SC membranes compared to wildtype SCs (see Figure 6B).

4) Can the authors speculate on a mechanism for how promoting more MAC results in increased proliferation?

Thank you for your question. We have added discussion around this topic to the text (please see line 585).

Author Response:

Reviewer #1:

The authors present an interesting concept for the mechanism of rash induction in EGFR inhibitor (EGFRi) treated rats. EGFRi causes production of pro-inflammatory factors in epidermal keratinocytes which may induce dedifferentiation and reduction of the dWAT compartment, presumably mediated via PPAR. Factors produced by dedifferentiated FB then recruit monocytes thereby inducing skin inflammation. This work is aiming to improve targeted cancer therapy efficiency and is therefore of potential clinical relevance.

However, most of the conclusions drawn by the authors are based on correlations, e.g. between the amount of dWAT and rash intensity. Mechanistic data have been mainly generated in vitro. The exact order of events to formulate a definitive mechanistic proof in vivo for this hypothesis is missing. In particular, it is not clear which cells in the skin, apart from keratinocytes, are specifically targeted by EGFR inhibitors and/or by Rosiglitazone. The authors also do not show EGFR staining in adipocytes and its inhibition by Afa. The effects of Afa and Rosi on monocytes / macrophages are completely ignored by the authors. Additionally, some of the presented results are overinterpreted and not really supporting what is claimed.

Most importantly, the whole study is based on inhibitor treatments. Afatinib for example is not only inhibiting EGFR but all other erbB family members and as such it represents a panErbB inhibitor and it is not clear whether the observed effects are induced by inhibition of EGFR of other erbB receptors which have been shown to have also effects in the skin. For further specification of the role of EGFR, other, more specific inhibitors should be used to confirm the basic concept along with genetic proof either in genetically engineered mice or by Crispr-mediated-deletion.

To further support the hypotheses of the authors, the study needs to be further substantiated by mechanistic experiments and the clinical relevance should be strengthened by performing histologic analysis of skin samples of patients treated with EGFRi and respective analysis of rash and e.g. BMI etc.

Thanks for your positive comments on the potential impact for cancer patients suffering EGFR inhibitor induced skin rash. We have carefully considered all comments from the reviewer and revised our manuscript accordingly. In the following section, we summarize our responses to each comment of the reviewer. We believe that our responses have well addressed all concerns from the reviewer.

We agree with the reviewer’s comment that our research may need more direct mechanistic in vivo studies upon our in vitro results. In our research, we have collected evidence from previous studies and used various in vitro and ex vivo experiments to investigate our findings. However, the study was still limited by currently available technologies.

In the revised version, we supplemented the pEGFR and pERK staining of adipocytes in Figure 3-figure supplement 1C. The levels of phospho-EGFR and ERK in dWAT were significantly decreased after EGFRi treatment.

This study was inspired by the observations of the unusual dWAT reduction during EGFRi treatment, thus we focused on the investigation of dermal adipocytes. In addition, the roles of mastocytes, monocytes, and macrophages in EGFRi-induced cutaneous toxicity have been thought as responders to increased expressions of cytokines. Local depletion of macrophages and degranulated mastocytes just provided partial resolution, indicating a multifactorial and complicated pathology of cutaneous toxicity induced by anti-EGFR therapy(Lichtenberger et al., 2013; Mascia et al., 2013).

In terms of some inappropriate descriptions, we agree with the reviewer that they will be more convincing if there is a direct assessment from genetically engineered mice. For example, we tried to establish the relationship between S. aureus infection and EGFRi-induced rash based on a well-accepted study from Lingjuan Zhang (Zhang et al., 2015). They reported that adipose precursor cells secret antimicrobial peptide cathelicidin during differentiation to against S. aureus infection. Mice with impaired adipogenesis were more susceptible to S. aureus infection. This conclusion gave us insights into the relationship between S. aureus infection and EGFRi-induced skin inflammation. Unfortunately, the anti-CAMP antibody was made by the author’s lab and there are no mature products that can recognize CAMP in rats. To provide more mechanistic evidences, we conducted qPCR experiments to study the transcriptional level of the Camp gene both in dWAT and dFB cells isolated from rat skin (Figure 3I and 3J). dWAT in Afa group showed a lower expression level of Camp compared with control group. In addition, in different differentiation stages of dFB in vitro, transcriptional levels of Camp were decreased by Afa treatment while increased by Rosi. In summary, the data we collected could verify the causal relationship between EGFRi-induced dWAT reduction and S. aureus infection to some extent. However, the limitation of the technology is an obstacle for us to provide more evidences. Thus, in the revised manuscript, we have edited our writing to make the statement not that strong.

According to the clinical evidence, the rash can also be induced by many specific Erbb1 inhibitors. All three generations of EGFR inhibitors in the clinic have very high incidence rates of cutaneous toxicity (Supplementary file 1). In the revised version, we provided rash models induced by both first-generation EGFRi, Erlotinib, Gefitinib, and the third-generation EGFRi, Osimertinib. As shown in Figure 1-figure supplement 1D, the rash caused by Erlotinib, Gefitinib, and Osimertinib had the same phenotypes as Afatinib-induced rash.

In summary, the current form of evidences should support our findings, even more direct mechanistic studies would be better. We are now seeking the opportunity for cooperation to build a dermal adipocyte knockout mouse model platform and hope to investigate the specific roles of dermal adipocytes in the future. We also plan to have cooperation with hospitals to explore the clinical evidence of patients receiving EGFR inhibitors.

References:

Lichtenberger BM, Gerber PA, Holcmann M, Buhren BA, Amberg N, Smolle V, Schrumpf H, Boelke E, Ansari P, Mackenzie C, Wollenberg A, Kislat A, Fischer JW, Röck K, Harder J, Schröder JM, Homey B, Sibilia M. 2013. Epidermal EGFR controls cutaneous host defense and prevents inflammation. Sci Transl Med 5.

Mascia F, Lam G, Keith C, Garber C, Steinberg SM, Kohn E, Yuspa SH. 2013. Genetic ablation of epidermal EGFR reveals the dynamic origin of adverse effects of anti-EGFR therapy. Sci Transl Med 5.

Zhang L, Guerrero-juarez CF, Hata T, Bapat SP, Ramos R, Plikus M V, Gallo RL. 2015. Dermal adipocytes protect against invasive Staphylococcus aureus skin infection. Science 347:67–72.

Reviewer #2:

Leying Chen et al. investigated the mechanism of EGFR inhibitor-induced rash. They find that atrophy of dermal white adipose tissue (dWAT), a highly plastic adipose tissue with various skin-specific functions, correlates with rash occurrence and exacerbation in a murine model. The data indicate that EGFR inhibition induces the dedifferentiation of dWAT and lipolysis , finally lead to dWAT reduction which is a hallmark of the pathophysiology of rash. Notably, they demonstrate that stimulating dermal adipocyte expansion with a high-fat diet (HFD) or the pharmacological PPARγ agonist rosiglitazone (Rosi) ameliorated the severity of rash. Therefore, PPARγ agonists may represent a promising new therapeutic strategy in the treatment of EGFRI-related skin disorders pending to be confirmed in further study.

We greatly appreciate the reviewer for giving the above positive comments.

The conclusions of this paper are mostly well supported by data, but some results need to be clarified and verified.

1) PPAR signaling in the pathology of EGFRI-induced skin toxicity. In figure 2 , the results show Rosi reversed the dedifferentiation of dermal adipocytes induced by Afa. This may due to PPARγ upregulation but not be confirmed in the results. The relative genes expression in dWAT after treated with Afa and ROSi were not demonstrated in the results.

We thank the reviewer for reminding us for additional experiment of PPARγ. In the revised version, we collected attatched-dWAT after 5-day Afa or Rosi treatment, and performed transcriptional experiment of Pparg. The expression level of Pparg was downregulated by Afa treatment and upregulated by Rosi treatment (Figure 2-figure supplement 1D).

2) the effect of PPAR signaling on PDGFRA-PI3K-AKT pathway The AKT pathway is a key downstream target of EGFR kinase, so it is reasonable to see p-AKT1 and p-AKT2 levels were decreased by Afa (figure 3C) However, addition of Rosi to Afa significantly activated both AKT1 and AKT2 . What is the underlying mechanism for the results and whether it is related to the PPAR signaling pathway.

Given the importance of the PI3K/AKT pathway in regulating AP and mature adipocyte biology(Jeffery et al., 2015), we used p-AKT to characterize the activation of dFBs. The mechanism of how modulating PPARγ affects AKT is still unknown. One study found that MAPK and PI3K are upregulated and activated by rosiglitazone that in turn might enhance adipogenesis(Fayyad et al., 2019). In skeletal muscle, PPARγ enhances insulin-stimulated PI3K and Akt activation(Marx et al., 2004). It is also reported rosiglitazone has a neuroprotection effect against oxidative stress. The PPARγ-rosiglitazone complex binds to the neurotrophic factor-α1 (NF-α1) promoter and activates the transcription of NF-α1 mRNA which is then translated to the protein. NF-α1 binds to a cognate receptor and activates the AKT and ERK pathways(Thouennon et al., 2015). Thus, further studies should be carried out to investigate the effects of rosiglitazone to PI3K/AKT pathway on adipogenesis.

3) According to figure 3 F , 3G and 3H., authors draw a conclusion that " a lack of APs and mature dWAT impairs the maintenance of the host defense and hair growth in the skin" In my opinion, there are no results can directly prove this. According to figure 3H, the impairment of hair growth may be caused by EGFR inhibition of hair follicles.

We appreciate the reviewer for pointing this important point out. We tried to establish the relationship between S. aureus infection and EGFRI-induced rash based on a well-accepted study from Lingjuan Zhang (Zhang et al., 2015). They reported that adipose precursor cells secret antimicrobial peptide cathelicidin during differentiation to against S. aureus infection. Mice with impaired adipogenesis were more susceptible to S. aureus infection. This conclusion gave us insights into the relationship between S. aureus infection and EGFRI-induced skin inflammation. Unfortunately, the anti-CAMP antibody was made by the author’s lab and there are no mature products that can recognize CAMP in rats. To provide more mechanistic evidences, we conducted qPCR experiments to study the transcriptional level of the Camp gene both in dWAT and dFB cells isolated from rat skin (Figure 3I and 3J). dWAT in Afa group showed a lower expression level of Camp compared with control group. In addition, in different differentiation stages of dFB in vitro, transcriptional levels of Camp were decreased by Afa treatment while increased by Rosi. In summary, the data we collected depending on the current technology could verify the causal relationship between EGFRI-induced dWAT reduction and S. aureus infection to some extent. However, we agree with the reviewer that this conclusion needs more direct evidence. Thus, in the revised manuscript, we have edited our writing to make the statement not that strong.

Since recent reports have shown that dermal adipocytes have the capacity to support hair regeneration, we used this conclusion to characterize the function of dWAT. However, we agree with the reviewer that it needs more specific and direct experiments to verify the causality with dWAT. And we are seeking the opportunity for cooperation to build a dermal adipocyte knockout mouse model platform and hope to investigate the specific roles of dermal adipocytes in the future. In the revised manuscript, we also adjusted the statements.

4) EGFRI stimulates keratinocytes (HaCaT cells) to produce lipolytic cytokines (IL-6) (Figure 4G). IL6 enhanced the lipolysis of differentiated dFB (Figure S4M) and C18 fatty acids were supposed to be released the cell matrix during lipolysis. In figure 4H, HaCaTcells supernatants and dFB supernatants were collected. IL-6 was supposed to increase in HaCaTcells supernatants and was confirmed in Figure 4SK and S4L.However, C18 fatty acids were not showed to be in the dFB supernatants in the study directly.

We thank the reviewer for pointing this out. We conducted additional lipidomics of dFB supernatants. However, because the differentiation medium needs to be changed every two days, it is hard to accumulate enough FFAs. We collected supernatants on Day3, Day 6, and Day 9. They were all below the detection limit of mass spectrum. We agree with the reviewer that more evidences are needed to prove the correlation between C18 FFAs and lipolysis. Therefore, we performed a mass spectrometry analysis of skin tissues from Ctrl and Afa groups after 3-day treatment to confirm the releasing of C18 FFAs. The result showed an increased tendency of C18:2 and other FFAs in the Afa group (Figure 1 in response letter). However, this increase had no significant statistic difference. This might be due to the interference of sebaceous gland and dermal adipocytes. In consequence, we adjusted the descriptions in the revised manuscript to make this statement not that strong.

Figure 1. C18 concentrations in skin tissues from Ctrl and Afa groups after 3-day treatment. n=3.

References:

Fayyad AM, Khan AA, Abdallah SH, Alomran SS, Bajou K, Khattak MNK. 2019. Rosiglitazone Enhances Browning Adipocytes in Association with MAPK and PI3-K Pathways During the Differentiation of Telomerase-Transformed Mesenchymal Stromal Cells into Adipocytes. Int J Mol Sci 20.

Jeffery E, Church CD, Holtrup B, Colman L, Rodeheffer MS. 2015. Rapid depot-specific activation of adipocyte precursor cells at the onset of obesity. Nat Cell Biol 17:376–385.

Marx N, Duez H, Fruchart J-C, Staels B. 2004. Peroxisome proliferator-activated receptors and atherogenesis: regulators of gene expression in vascular cells. Circ Res 94:1168–1178. Thouennon E, Cheng Y, Falahatian V, Cawley NX, Loh YP. 2015. Rosiglitazone-activated PPARγ induces neurotrophic factor-α1 transcription contributing to neuroprotection. J Neurochem 134:463–470.

Zhang L, Guerrero-juarez CF, Hata T, Bapat SP, Ramos R, Plikus M V, Gallo RL. 2015. Dermal adipocytes protect against invasive Staphylococcus aureus skin infection. Science 347:67–72.

Author Response:

Reviewer 2 (Public Review):

Weaknesses 1. I had difficulty following the ANOVA results for Figure 1. I assume ANOVA was performed with factors of session and block. However, a single F statistic is reported. I do not know what this is referring to. It would be more appropriate to either perform repeated measures ANOVA with session and block as factors for each dependent variable or even better, multiple analyses of variance for the three dependent measures concurrently. Then report the univariate ANOVA results for each dependent measure. The graphs in Figure 1 (C-E) suggest a main effect of block, but as reported, I cannot tell if this is the case. Further, why was sex not included as an ANOVA factor?

For the sake of transparency, we had included plots showing sessions split by each block whereas statistics related to the right side bar plots where data are collapsed across risk (which was done to minimize effects from ‘missing’ data). We appreciate that this may have caused confusion. In the revised manuscript we specify the exact figure for each statistical result and have added a better description in the methods and updated the statistics (Table 1) with the ANOVA and post-hoc results.

Previously we had used a mixed effects model because one subject did not complete any risk trials in session 3 but in the revised manuscript, we decided to remove that subjects’ sessions to permit RM ANOVA. As requested by the reviewer, we performed a multivariate analysis on risk and no risk trials. Because of the repeated measures design we opted to utilize the multiple RM package developed by Friedrich et al. 2019, which permits multivariate analysis on repeated measures data with minimal assumptions and bootstrapped p-values for small sample sizes. We found significant interactions for session (or treatment) and risk (see tables below). This justifies the two-way univariate ANOVA which is now reported in the rest of the manuscript. Sex differences were not included in the ANOVA because the study was not intended to assess sex differences but, rather, was designed according to NIH requirements for inclusion of males and females.

Note: MATS test was utilized based on author recommendations in Friedrich et al., (2019) for when test violates singularity, which was reported. To replicate use a random seed of 8675309.

Package link: https://rdrr.io/github/smn74/MANOVA.RM/man/multRM.html Publication: Friedrich, S., Konietschke, F., & Pauly, M. (2019). Resampling-based analysis of multivariate data and repeated measures designs with the R package MANOVA. RM. R J., 11(2), 380.

1. The authors describe session 1 as characterized by 'overgeneralization' due to increased reward latencies. I do not follow this logic. Generalization typically refers to a situation in which a response to one action or cue extends to a second, similar action or cue. In the authors' design, there is only one cue and one action. I do not see how generalization is relevant here.

This wording has been changed to “non-specific” in the results and discussion.

1. The authors consistently report dmPFC and VTA 'neural activity'. The authors did not record neural activity. The authors recorded changes in fluorescence due to calcium influx into neurons. Even if these changes have similar properties to neural activity measured with single-unit recording, the authors did not record neural activity in this manuscript.

We do not imply that we recorded unit activity in these studies and state in the introduction that fiber photometry is an indirect measure of neural activity. We have also reworded much of the text in the manuscript to use “calcium activity.”

1. Comparing the patterns in Figures 2 and 3, it appears that dmPFC change in fluorescence was similar in non-shocked and shock trials up until shock delivery. However, the VTA patterns differ. No cue differences were observed for sessions 1-3 on shock trials (Figure 3A), yet differences were observed on non-shocked trials (Figure 2F). Further, changes in fluorescence between sessions 1 and 2/3 appeared to emerge just as foot shock would have been delivered. A split should be evident in Figure 3B - but it is not. Were these differences caused by sampling issues due to foot shock trials being rarer?

We agree, although some of this could be because footshock trials were collapsed across blocks 2 and 3 (as no differences in shock response was observed between blocks). Nevertheless, we have added a caveat about cue responses to the results (see page 11-bottom and 15-top). Regarding the lack of a split in Figure 3A – this difference may be due to shock onset time. The permutation tests indicate the differences in action activity in Figure 2B emerge about 0.5 – 0.8 seconds after action which is when the shock begins. So it is not surprising the results in 2F do not match well with 3A given the rapid and robust response to the footshock.

1. Similar to Figure 1, I could not follow the ANOVA results for the effects of diazepam treatment on trials completed, action latency and reward latency (Figure 4). Related, from what session do the bar plot data in Figure 4B come from? Is it the average of the 6% and 10% blocks? I cannot tell.

Please see our response in comment 1 for relevant analysis to this comment. Yes average of risk blocks is the average of 6 and 10%. Better explanation of what bar plot data represent are now explained in the methods.

1. For the diazepam experiment, did all rats receive saline and diazepam injections in separate sessions? If so, were these sessions counterbalanced? And further, how did the session numbers relate to sessions 1-3 of the first study? All of these details are extremely relevant to interpreting the results and comparing them to the first study, as session # appeared to be an important factor. For example - the decrease in dmPFC fluorescence to reward during the No-Risk block appeared to better match the fluorescent pattern seen in sessions 1 and 2 of the first experiment. In which case, the saline vs. diazepam difference was due to saline rats not showing the expected pattern of fluorescence.

Subjects received saline and diazepam in separate sessions. Furthermore, diazepam was not tested until animals had at least 3 sessions of training (range of sessions 4-8). Clarification has been added to the methods.

The new AUC analysis for Reviewer 1 allows for better assessment of the potential differences between earlier sessions and saline (see figure 7- supplements 2 and 3). We also found the effect with reward and diazepam perplexing and somewhat modest. However, even after comparing only Saline and Session 3 PFC AUC data we found no significant effect of session or session*risk interaction for action or reward (F values < 1.3, p values >.27).

1. The authors seem convinced that fiber photometry is a surrogate for neural activity. Although significant correlation coefficients are found during action and reward, these values hover around 0.6 for the dmPFC and 0.75 for the VTA. Further, no correlations are observed for cue periods. A strength of the calcium imaging approach is that it permits the monitoring of specific neural populations. This would have been very valuable for the VTA, in which dopamine and GABA neurons must show very different patterns of activity. Opting for fiber photometry and then using a pan-neuronal approach fails to leverage the strength of the approach.

The parent paper (Park & Moghaddam, 2017) used unit recording in this task (including reporting data from dopamine and non-dopamine VTA units). We assure the reviewer that we do not claim that fiber photometry is a perfect surrogate for direct recording of neural activity. However, a key question we wanted to answer in this study was whether the response of PFC and VTA to the footshock changes during task acquisition (please see last paragraph of introduction), hence the choice to use fiber photometry. We note in the results and discussion that this approach is not optimal for detecting cue or other rapid responses (see page 15 and 23).

Reviewer 3 (Public Review):

Probably the biggest overall issue is that it is unclear what is being learned specifically. There is no probe test at the end to dissociate the direct impact of shock from its learned impact. And the blocks are not signaled in some other way. And though there seems to be some evidence that the shock effects get more pronounced with a session, it is not clear if the rats are really learning to associate specific shock risks with the particular trials. Indeed with so few sessions and so few actual shocks, this seems really unlikely, especially since without an independent cue, the shock and its frequency is the cue for the block switch. It seems especially unlikely that there is a strong dichotomy in the rats model of the environment between 6% and 10% blocks. This may be quite relevant for understanding foraging under risk. But I think it means some of the language in the paper about contingencies and the like should be avoided.

While the parent paper (Park & Moghaddam, 2017) delved more deeply into this question we agree that what exactly is learned may be difficult to ascertain. To address this (please also see response to reviewer #1’s first comment), we have toned down our use of the “contingency learning” throughout the manuscript and use the word contingency in relation to the underlying reinforcement/punishment schedules.

The second issue I had was that I had some trouble lining up the claims in the results with what appeared to be meaningful differences in the figures. Just looking at it, it seems to me that VTA shows higher activities at higher shocks, particularly at the time of reward but also when comparing safe vs risky anyway for the cue and action periods. DmPFC shows a similar pattern in the reward period. […] But these results are not described at all like this. The focus is on the action period only and on ramping? I don't really see ramping. it says "Anxiogenic contingencies also did not influence the phasic response to reward...". But fig 3 seems to show clearly different reward responses? The characterization of the change is particularly important since to me it looks like the diazepam essentially normalizes these features of the response. This makes sense to me […].

We initially believed that much of the differences in reward (with the exception of Session 2 in the PFC) were from carryover of differences in the peri-action period. However upon quantifying these responses again using AUC change scores to adjust for pre-event differences in the signal, we observed small reward related increases (data are in Figure 7 – supplements 2/3) and have updated results and the discussion.

Although some lessening of reward response may be apparent across the diazepam session in the VTA (Figure 7 – supplement 2/3G), we do not have statistical support for this as no significant differences were observed in permutation comparisons to saline and only session 3 deviated from the first session for the reward period in the AUC analyses.

Author Response:

Reviewer #1:

General overview and merit of academic rigor:

Xu et. al put forth an innovative experimental pipeline to examine the connections of the raphe nuclei. This manuscript details elegantly designed viral tract-tracing methods coupled with fMOST intact imaging and sophisticated analyses. All figures are of good quality. The studies presented in the current manuscript will be a valuable contribution to the field, therefore an enthusiastic recommendation for publication is endorsed presently. However, there is a cluster of revisions and clarifications warranted before publication.

Major concerns:

1. The manuscript's English needs to be proofread extensively for readability and clarity.

We invited two native English experts to proofread the manuscript's English and revise the whole manuscript.

1. The term MR (median raphe) is used in the atlas of Paxinos and Franklin. But, the entire study follows the Allen Reference Atlas nomenclature, in which the same raphe nucleus is called the "Superior center nucleus" (CS). To keep consistency, I suggest using "CS" instead of "MR". Alternatively, in the Introduction, please make a clear statement that the MR is equivalent to CS in the Allen Reference Atlas.

As suggested, we added the statement that MR is equivalent to CS in the Allen CCFv3 in Line 15-18.

“The dorsal raphe nucleus (DR) and median raphe nucleus (MR, equivalent to the superior central nucleus raphe in the Allen Mouse Brain Common Coordinate Framework version 3 (Allen CCFv3)) belong to the rostral group of the raphe nuclei and contain most of brain’s serotonergic neurons (Wang et al., 2020; Watson, et al., 2012).”

1. In the Introduction, it is unclear the rationale behind the decision to selectively study the DR and MR here (why other raphe nuclei are not included?).

We have revised the Introduction and described why to selectively study the DR and MR in Line 15-25.

“The dorsal raphe nucleus (DR) and median raphe nucleus (MR, equivalent to the superior central nucleus raphe in the Allen Mouse Brain Common Coordinate Framework version 3 (Allen CCFv3)) belong to the rostral group of the raphe nuclei and contain most of brain’s serotonergic neurons (Wang et al., 2020; Watson, et al., 2012). The DR and MR are involved in a multitude of functions (Domonkos et al.,2016; Huang et al., 2019; Szőnyi et al., 2019); moreover, they have different, and even antagonistic roles in the regulation of specific functions, including emotional behavior, social behavior, and aggression (Balázsfi et al., 2018; Ohmura et al., 2020; Teissier et al., 2015). The diverse regulatory processes are related to the connectivity of heterogeneous raphe groups (Muzerelle et al., 2016; Nectow et al., 2017; Schneeberger et al., 2019). Deciphering precise input and output organization of different neuron types in the DR and MR is fundamental for understanding their specific functions.”

1. In the Results, I did not find any figure panel or images to show the anatomical location of the MR. Figure 1 shows only one injection site in DR. It is necessary to also show at least one representative injection site in the MR.

As suggested, we added more information of injection site in Figure 1—figure supplement 2 and Figure 4—figure supplement 1.

Figure1—figure supplement 2. Validation of the labeling of whole-brain inputs. (A) Representative coronal section of the injection site showing the starter cells (cyan). The image is from a representative sample that label the inputs to MR Gad2+ neurons. Scale bar, 1mm. (B) Enlarged view of dotted box area in (A). Scale bar, 100 μm. (C) The number and on-target rate of labeled starter neurons, and the ratio of input neurons to starter cell. The data are from validation samples that label the inputs to MR Gad2+ neurons. Data are shown as mean ± s.e.m., n = 3. (D) Comparison of inputs to MR Gad2+ neurons.

Figure 4—figure supplement 1. Validation of the injection sites of whole-brain outputs. (A) Representative coronal section of the injection site of a representative sample that label the outputs of MR Vglut2+ neurons. The dataset has been registered to the Allen CCFv3. White dotted lines, MR in the Allen CCFv3; Yellow lines, segmented injection site. (B) Representative coronal sections of the injection site of the representative sample in (A). (C) Proportion of signal of the injection site in the DR/MR. Data are shown as mean ± s.e.m., n = 4 per group. Scale bars, A, 1 mm; B, 500 μm.

1. This study is designed to map the input/output of two major populations of neurons (Glu+ and GABAergic) in the DR and MR using two cre-driver lines (Vglut2-cre and Gad2-cre). Please clarify how these two cre lines were characterized and whether those cre expressions are consistent with endogenous gene expressions. What are their distribution patterns in the DR and MR? Are they intermingled or relatively segregated? How are their distributions in comparison with that of serotonergic neurons?

The Vglut2-Cre and Gad2-Cre mice were purchased from Jackson Laboratory and carried out genotyping according to the instructions. To verify the expressions characterization and distribution pattern of Vglut2+ and Gad2+ neurons, we crossed the Cre driver line mice with reporter line respectively (Figure 1—figure supplement 1). In the DR, Vglut2+ neurons were mostly found in the rostral part of the DR, while Gad2+ neurons were widely distributed and densely assembled in the lateral DR. In the MR, Vglut2+ neurons were mainly found in the caudal part of the MR, and the Vglut2+ neurons in the rostral part of the MR were mainly distributed laterally; moreover, Gad2+ neurons were distributed throughout the MR. And there are obvious differences between the overall distribution pattern of Vglut2+ and Gad2+ neurons in the same raphe nucleus. Compared with the distribution of serotonergic neurons (http://connectivity.brain-map.org/ transgenic/experiment/100140881), the distribution of Vglut2+ neurons seem to be relatively segregated with them, and the distribution of Gad2+ neurons are intermingled with them.

As Gad2-Cre generally labels all mature GABAergic neurons, while Vglut2-Cre only labels a population of glutamatergic neurons, and there are also numerous Vglut3+ neurons in the DR and MR, we decide to perform experiments to characterize the specificity of the labeled Vglut2+ starter cells. We performed in situ hybridization to characterize the specificity of labeled starter cells in the Vglut2-Cre mice and found that they were Vglut2 positive, with a few simultaneously being Vglut3 positive (Figure 1B,C; Figure1—figure supplement 3), which was confirmed by immunohistochemical staining (Figure 1—figure supplement 4).

Figure 1—figure supplement 1. Distribution and total number of Vglut2+ and Gad2+ neurons in the DR and MR. (A) Representative coronal sections of maximum intensity projection showing the distribution of Vglut2+ and Gad2+ neurons in the DR. The projections are 200 μm thick. Scale bar, 200 μm. The total number of Vglut2+ and Gad2+ neurons in the DR are presented as mean ± s.e.m., n = 2. (B) Representative coronal sections of maximum intensity projection showing the distribution of Vglut2+ and Gad2+ neurons in the MR. The projections are 200 μm thick. Scale bar, 200 μm. The total number of Vglut2+ and Gad2+ neurons in the MR are presented as mean ± s.e.m., n = 2. (C) Density plot of specific neuron types in the DR and MR along the anterior-posterior axis. Bin width, 100 μm. The shaded area indicates s.e.m., n=2.

Figure 1—figure supplement 3. Characterization of the specificity of starter cells using in situ hybridization. (A) In situ hybridization at the MR in Vglut2-Cre mouse. (B) Enlarged view of the box area in (A). White arrows, starter cells. Scale bar, A, 200 μm, B, 20 μm.

Figure 1—figure supplement 4. Validation of the specificity of starter cells using immunohistochemical staining. (A) Immunohistochemical staining against Vglut3 at the DR in Vglut2-Cre mouse. White arrows, starter cells. Red arrows, starter cells that are Vglut3 positive. (B) Immunohistochemical staining against Vglut3 at the MR in Vglut2-Cre mouse. White arrows, starter neurons. Red arrows, starter cells that are Vglut3 positive. (C) Control experiment, immunohistochemical staining against Vglut3 at the SSp in Vglut2-Cre mouse. Scale bar, 50 μm.

1. Overall Discussion is not well organized. I suggest to start with a clear statement about the novel discoveries of this study in comparison with existing literature, and then compare the overall input/output patterns of Glu+ and GABAergic populations in the DR and MR. The current discussion focuses on a few major targets (i.e., CEA, LH), but missed a big picture. Additionally, it is necessary and important to carefully compare their connectivity patterns with that of serotonergic neurons in these two raphe nuclei.

As suggested, we have reorganized the Discussion. At first, we compared the results with existing literature and pointed out the similarities and differences of connectivity patterns compared with that of serotonergic neurons. Then, we compared the overall input/output patterns of glutamatergic and GABAergic neurons in the DR and MR and discussed their implications for behavior functions. At last, we discussed the potential caveats in our viral tracing techniques and data analysis.

Minor concerns:

1. The Impact statement reads, "We reconstructed the input-output circuits of glutamatergic and GABAergic neurons in the dorsal raphe nucleus and median raphe nucleus and proposed a more refined model of the habenula-raphe circuit." When a comparison like this is put down, a specific reference to what your method is more refined than is required. This is well explained in lines 242 and 243, "Based on the conventional model of the habenula-raphe circuit (Hikosaka, 2010; Hu et al., 2020), we proposed a more refined model of the habenula-raphe circuit (Figure 5C)." Make a similar claim earlier in the Impact statement.

We have revised the impact statement as follow:

“Whole-brain quantitative input-output circuits of glutamatergic and GABAergic neurons in the mouse dorsal and median raphe nuclei were mapped using viral tracing and high-resolution optical imaging.”

1. For Figure 2A, it would be easier on the reader if inputs for each region (DR and MR) and each plane of the section were placed on the same image akin to the inputs presented on coronal maps in Figures 2B and 5A and the inputs/outputs for each region (MR and DR) in the sagittal summary diagrams in Figure 7.

For Figures 2A and 2B, we wanted to present the whole-brain inputs from different perspectives. For Figure 2A, as there were tens of thousands of input neurons and the input patterns were similar, if we placed the inputs on the same image, the color would mix up and it would be difficult to see clearly. Thus, we presented them separately in sagittal and horizonal views in Figure 2A. Further, we presented the inputs together on coronal maps in Figure 2B.

1. It is unclear what the nonsignificant grey open circles represent in Figures 3A-D; 4D and E.

In Figures 3A-D, the circles represent the proportion of input neurons in each brain region. If there is a significant difference between the inputs in one brain region to two neuron groups, the circle is red and solid, and the name of the brain region are presented nearby. If there is no significant difference between the inputs in that region to two neuron groups, the circle is gray and hollow. To highlight those brain areas with significant differences, the names of these brain regions are not presented. Moreover, we provided the source data in Supplementary File 2. As for Figures 4D and E, it is akin to Figures 3A-D.

1. In Figure 4A, the imaging portion would be clearer if it read "optical sectioning."

As suggested, we revised the image portion to make it clearer.

1. In Figure 7A and B, the position of ACA on the flatmap looks odd to me (it is a little bit too caudal).

As suggested, we revised the position of ACA on the flatmap.

Reviewer #2:

This work from Xu et. al. "Whole-brain connectivity atlas of glutamatergic and GABAergic neurons in mouse dorsal and median raphe nucleus" provided a comprehensive brain-wide analysis for input and output patterns to/from specific DR/MR neuronal populations in adult mouse brain. With exceptional strength in experimental approaches for high quality whole brain imaging that this group is famous for, their data and analysis are thorough and convincing for the general conclusion of the manuscript for describing both convergent and divergent patterns of DR/MR connectivity. While the current study is based on structural but not functional correlation analysis, the results are validated with prior knowledge of the field. It will provide a more complete picture to facilitate future investigation of DR/MR connectivity and physiological functions.

The work would provide a significant and useful knowledge for the field, while also promoting the generation and application of advanced brain-wide profiling resource to advance board neuroscience research topics. However, there are still a few technical and analytical concerns that need to be addressed or discussed to refine the conclusions.

Major concerns:

1. For targeted injection-based analysis, it is critical to carefully analyze and discuss on-target vs off-target rates of labeled cells in DR/MR to validate the datasets. Whole mount data would best fit for such accurate analysis not possible before.

As for the inputs, samples from the same batch of virus tracing experiments were treated as validation datasets to analyze on-target rates of labeled starter cells. As for samples that label inputs to MR Gad2+ neurons, the on-target rate of labeled starter cells is 66.40 ± 2.78% (Figure 1—figure supplement 2C). And we counted the input neurons and calculated the ratio of input neurons to starter cells (Figure 1—figure supplement 2C). Compared with experiment datasets, they have consistent input patterns (Figure 1—figure supplement 2D). As for the outputs, we manually segmented the injection region and calculated the proportion of signal of the injection region in the DR/MR (Figure 4—figure supplement 1).

1. It is also important to know what percentage of the cells get labeled over individual samples, and how many samples and in total what coverage/saturation over the entire anatomical structure has been achieved to justify a complete/comprehensive analysis.

We counted the Vglut2+ and Gad2+ neurons in the DR and MR in crossed mice (Vglut2-Cre: LSL-H2B-GFP mice and Gad2-Cre: LSL-H2B-GFP mice; Figure 1—figure supplement 1A,B). As for the inputs to MR Gad2+ neurons, the labeling rate is 11.60±1.28 % (Figure 1—figure supplement 2C). As for the outputs, we counted the labeled Vglut2+ and Gad2+ neurons in the DR and MR and calculated the percentage (DR Vglut2+: 18.38±8.33%, DR Gad2+: 10.66±2.65%, MR Vglut2+: 43.67±8.25%, MR Gad2+: 11.10±2.09%) (Supplementary File 3). The data were replicated in 4 samples, which was comparable to previous studies of input and output circuits (Ährlund-Richter et al. 2019. Nature Neuroscience, 22: 657–668; Do et al. 2016. eLife, 5: e13214; Gehrlach et al. 2020. eLife, 9: e55585.).

1. Further on last point, the labeling rates need to be small enough to warrant a more meaningful analysis in Figure 6. From another aspect, is there any anatomical correlation of the target sites in DR/MR for the distinct input/output clusters? This can probably be best addressed with single neuron resolution analysis that this group is good at. For the current study it is a vital part to include this detailed information for better resource to the field (e.g. to guide or map to future spatial transcriptomic analysis to study molecular-cellular correlations).

Following the previous question, the labeling rate is at a low level, which could ensure that the analysis is meaningful. The analysis in Figure 6 implied that the glutamatergic and GABAergic neurons in the DR/MR might receive inputs from and project to various unions of brain regions. The brain regions in one cluster might be connected with the same subsets of specific neuron types. The brain regions of negative correlation might be connected with distinct subsets of specific neuron types (Weissbourd et al. 2014. Neuron 83: 645–662). As for the inputs to DR Vglut2+ neurons, Vglut2+ neurons receiving inputs from the SNc might be the same as those receiving inputs from the VTA and SNr, but distinct from those receiving inputs from the BST (Figure 6A). These implications are worth illustrating through complete single neuron reconstruction. However, single neuron reconstruction needs substantial time, which is beyond the scope of this work but in our future plans. And our datasets have been registered to the AllenCCFv3, which enables to be directly incorporated to more resource with the same coordinate system. Spatial transcriptome is the current research hotspot, but spatial localization cannot reach the level of single neuron, and it is difficult to integrate with the morphology. We are engaged in this research, but there is no significant progress.

Reviewer #3:

Xu et al utilize retrograde and anterograde viral tracing in Cre-transgenic mouse lines to map the inputs and outputs of glutamatergic and GABAergic neuronal populations in the dorsal (DR) and median raphe (MR) nucleus. The experiments generate a large anatomical dataset which the authors analyse with correlation analysis, revealing subtle differences in connectivity patterns between the targeted cell types and nuclei. The study furthermore focuses on the lateral habenula (LH) to raphe nucleus circuit, identifying large amounts of inputs from the LH to both glutamatergic and GABAergic DR and MR populations, but scarce projections from these cells back to the LH, with some cell-type specific differences. In particular, MR glutamatergic neurons send the strongest projections to LH among the targeted populations, supporting previous studies which identified this pathway as playing a role in aversive behaviors.

Overall, this study nicely complements previously published work on whole-brain connectivity of the DR and MR which have chiefly focused on the main neuromodulatory neurons found in these nuclei, ie. serotonin and dopamine neurons. Some of the experiments in the study are not completely novel, such as input tracing to GAD2-expressing neurons in DR (Weissbourd et al, 2014). However, comprehensive side-by-side comparison analysis between glutamatergic and GABAergic connectivity of both DR and MR nuclei has not been performed before, and will provide a welcome resource to circuit neuroscientist looking to elucidate functional circuits of the raphe nuclei. A further strength of the study is the high-resolution 3D imaging, revealing three distinct projection pathways from MR glutamatergic neurons to LH.

Two main concerns regarding the study are:

1) The authors do not sufficiently justify the use of Vglut2 as a marker for glutamatergic neurons in DR and MR. The majority of previous studies, especially of the DR, use another glutamatergic marker which is more specifically expressed in the raphe nuclei, namely Vglut3. Vglut3 is much more anatomically restricted to the DR and MR (but has also been shown to partially overlap with serotonergic expression). In contrast, Vglut2 is very broadly expressed throughout the brain and in regions adjacent to DR and MR. For this reason, and from the data in the main manuscript as well as raw microscopy images provided in the accompanying website, it is unclear how specific the starter neuron targeting really is. The authors should show more detailed starter neuron analysis for both the broadly expressed Vglut2 and Gad2 in the DR and MR, showing the histology of the helper virus BFP and RV-ΔG-EnvA-GFP, their anatomical locations, and some quantification of proportion of starter cells within DR/MR (Fig 1B-C shows it only for Vglut2, but in insufficient detail). Furthermore, a rationale for using Vglut2 instead of Vglut3 would be appreciated, especially given that the vast majority of functional studies of the DR have used Vglut3.

The authors also miss the chance to characterize the topography of Vglut2 and Gad2 starter cell expression within the DR and MR and emphasize the interesting differences between these two populations, which may be relevant to the differences in input and output connectivity.

We added more information of starter cells in Figure1—figure supplement 2. And we performed in situ hybridization and immumohistochemical staining to characterize the specificity of the labeled Vglut2+ starter cells. The labeled starter cells were Vglut2 positive, while a fraction of them was simultaneously Vglut3 positive (Figure 1B, C; Figure1—figure supplement 3,4).

As glutamatergic neurons in the DR and MR are mainly comprised of Vglut2+ neurons and Vglut3+ neurons, but numerous Vglut3+ neurons are also serotonergic (Huang et al. 2019. eLife, 8: e46464; Pinto et al. 2019. Nature Communications 10, 4633–4633; Sos et al. 2017. Brain Structure and Function, 222: 287–299.). The anatomical connections of serotonergic neurons in the DR and MR have been well studied (Pollak Dorocic et al. Neuron. 83: 663–678; Ren, et al.2019. eLife 8: e49424; Weissbourd et al. Neuron. 83: 645–662). DR and MR Vglut2+ neurons are relatively independent from Vglut3+ neurons. And they have been revealed to regulate multitudinous functions, such as emotional behaviors (Szőnyi et al.2019. Science 366: eaay8746), but their whole-brain connectivity remains incomplete. Thus, we choose to study the inputs and outputs of Vglut2+ neurons.

And there are differences between the distribution of Vglut2+ and Gad2+ neurons in the DR/MR (Figure 1—figure supplement 1), and these differences might be relevant to the differences in input and output connectivity, which are worth illustrating in our future studies.

2) The quantification throughout the manuscript refers to the relative proportion of inputs or outputs for each cell population and nucleus. The manuscript would be strengthened by also including total cell counts for starter cells in each group, as well as total numbers of input neurons. For example, is the Vglut2 population in DR much larger than the Gad2 population, and do DR Vglut2 neurons receive more inputs in total than DR Gad2 neurons? Including raw numbers would provide concrete information to contextualize connectivity patters between cell types and nuclei to the readers.

We added the number of input neurons in Supplementary File 2. As we discussed in lines 413-415, the monosynaptic rabies tracing technique might only label a portion of inputs, and the labeling could be biased toward specific neuron types and affected by many factors. Further, the ratio of the number of input neurons to starter cells variate in a vast range (Callaway and Luo. 2015. The Journal of Neuroscience, 35: 8979–8985). Thus, the larger population of specific neuron types might not indicate that they receive more inputs.

Author Response

Reviewer #2 (Public Review):

The manuscript by Ma et al, "Two RNA-binding proteins mediate the sorting of miR223 from mitochondria into exosomes" examines the contribution of two RNA-binding proteins on the exosomal loading of miR223. The authors conclude that YBX1 and YBAP1 work in tandem to traffic and load miR223 into the exosome. The manuscript is interesting and potentially impactful. It proposes the following scenario regarding the exosomal loading of miR223: (1) YBAP1 sequesters miR223 in the mitochondria, (2) YBAP1 then transfers miR223 to YBX1, and (3) YBX1 then delivers miR223 into the early endosome for eventual secretion within an exosome. While the authors propose plausible explanations for this phenomenon, they do not specifically test them and no mechanism by which miR223 is shuttled between YBAP1 and YBX1, and the exosome is shown. Thus, the paper is missing critical mechanistic experiments that could have readily tested the speculative conclusions that it makes.

Comments:

1) The major limitation of this paper is that it fails to explore the mechanism of any of the major changes it describes. For example, the authors propose that miR223 shuttles from mitochondrially localized YBAP1 to P-body-associated YBX1 to the exosome. This needs to be tested directly and could be easily addressed by showing a transfer of miR223 from YBAP1 to YBX1 to the exosome.

Testing this idea using fluorescently labeled miR223 would indeed be an ideal experiment. However, miRNA imaging presents challenges. As reviewer 1 pointed out, and we have now confirmed, the atto-647 dye itself localizes to mitochondria. We will continue our efforts to identify a suitable fluorescent label for miR223in order to be in a position to evaluate the temporal relationship between mitochondrial and endosomal miR223.

2) If YBAP1 retains miR223 in mitochondria, what is the trigger for YBAP1 to release it and pass it off to YBX1? The authors speculate in their discussion that sequestration of mito-miR223 plays a "role in some structural or regulatory process, perhaps essential for mitochondrial homeostasis, controlled by the selective extraction of unwanted miRNA into RNA granules and further by secretion in exosomes...". This is readily testable by altering mitochondria dynamics and/or integrity.

A previous study has reported that YBAP1 can be released from mitochondria to the cytosol during HSV-1 infection (Song et al., 2021). However, due to restrictions, we are unable to conduct experiments using HSV to verify this condition. We attempted to induce mitochondrial stress by using different concentrations of CCCP, but we did not observe the release of YBAP1 from mitochondria after CCCP treatment. We speculate that not all mitochondrial stress conditions can trigger YBAP1 release. Investigating the mechanism of mito-miR223 release from mitochondria is one of our interests that we aim to explore in future studies.

3) Much of the miRNA RT-PCR analysis is presented as a ratio of exosomal/cellular. This particular analysis assumes that cellular miRNA is unaffected by treatments. For example, Figure 1a shows that the presence of exosomal miR223 is significantly reduced when YBX1 is knocked out. This analysis does not consider the possibility that YBX1-KO alters (up or down-regulates) intracellular miR223 levels. Should that be the case, the ratiometric analysis is greatly skewed by intracellular miRNA changes. It would be better to not only show the intracellular levels of the miRs but also normalize the miRNA levels to the total amount of RNA isolated or an irrelevant/unchanged miRNA.

Our previous publications demonstrated that miR223 levels are increased in YBX1-KO cells and decreased in exosomes derived from YBX1 KO cells. However, no significant changes were observed in miR190 levels (Liu et al., 2021; Shurtleff et al., 2016). The repeated data has been included in Figure 1a.

For the analysis of other miRNAs by RT-PCR, we assessed changes in intracellular and exosomal miRNA levels in the corresponding figures. In the qPCR analysis, miRNA levels were normalized to the total amount of RNA.

4) In figure 1, the authors show that in YBX1-KO cells, miR223 levels are decreased in the exosome. They further suggest this is because YBX1 binds with high affinity to miR223. This binding is compared to miR190 which the authors state is not enriched in the exosome. However, no data showing that miR190 is not present in the exosome is shown. A figure showing the amount of cellular and exosomal miR223 and 190 should be shown together on the same graph.

In previous publications we demonstrated that miR190 is not localized in exosomes and not significantly changed in YBX1 knockout (KO) cells and exosomes derived from YBX1 KO cells (Liu et al., 2021; Shurtleff et al., 2016). The repeated data has been included in Figure 1a.

5) Figure 2 Supplement 1 - As to determine the nucleotides responsible for interacting with YBX1, the authors made several mutations within the miR223 sequence. However, no explanation is given regarding the mutant sequences used or what the ratios mean. Mutant sequences need to be included. How do the authors conclude that UCAGU is important when the locations of the mutations are unclear? Also, the interpretation of this data would benefit from a binding affinity curve as shown in Fig 2C.

The ratio is of labeled miR223/unlabeled miR223 (wt and mutant). All mutant sequences of miR223 have been included in Figure 2 supplement 1.

6) While the binding of miR223mut to YBX1 is reduced, there is still significant binding. Does this mean that the 5nt binding motif is not exact? Do the authors know if there are multiple nucleotide possibilities at these positions that could facilitate binding? Perhaps confirming binding "in vivo" via RIP assay would further solidify the UCAGU motif as critical for binding to YBX1.

The binding affinity of miR223mut with YBX1 is reduced approximately 27-fold compared to miR223. We speculate that the secondary structure of miR223 may contribute to the interaction with YBX1.

Our EMSA data, in vitro packaging data, and exosome analysis reinforce the conclusion that UCAGU is critical for YBX1 binding. These findings suggest that the presence of the UCAGU motif in miR223 is crucial for its interaction with YBX1 and subsequent sorting into exosomes.

7) Figures 2g, h - It would be nice to show that miR190mut also packages in the cell-free system. This would confirm that the sequence is responsible. Also, to confirm that the sorting of miR223 is YBX1-dependent, a cell-free reaction using cytosol and membranes from YBX1 KO cells is needed.

Although we have not performed the suggested experiment, we purified exosomes from cells overexpressing miR190sort and observed an increase in the enrichment of miR190sort in exosomes compared to miR190. This finding confirmed that the UCAGU motif facilitates miRNA sorting into exosomes.

Regarding the in vitro packaging assay, our previously published paper demonstrated that cytosol from YBX1 knockout (KO) cells significantly reduces the protection of miR223 from RNase digestion. We concluded that the sorting of miR223 into exosomes is dependent on YBX1 (Shurtleff et al., 2016).

8) In Figure 3a, the authors show that miR223 is mitochondrially localized. Does the sequence of miR223 (WT or Mut) matter for localization? Does it matter for shuttling between YBAP1 and YBX1?

The localization of miR223mut has not been tested in our current study. We plan to conduct these experiments in the future.

9) Supplement 3c - Is it strange that miR190 is not localized to any particular compartment? Is miR190 present ubiquitously and equally among all intracellular compartments?

Most mature miRNAs are predominantly localized in the cytoplasm. Although there is no specific subcellular localization reported for miR190 in the literature, our experimental findings indicate a relatively high expression of miR190 in 293T cells. It is likely that most of miR190 is localized in the cytosol. However, it is also possible that a small fraction of miR190 may associate with a membrane, which could explain its distribution in various subcellular structures. Importantly, we did not observe enrichment of miR190 in the mitochondria or exosomes.

10) Figure 3h - Why would the miR223 levels increase if you remove mitochondria? Does CCCP also cause miR223 upregulation? I would have thought miR223 would just be mis-localized to the cytosol.

We report that the levels of cytoplasmic miR223 increase following the removal of mitochondria using CCCP treatment. While we cannot rule out the possibility that upregulation of miR223 is directly caused by CCCP treatment, we suggest that miR223 becomes mis-localized to the cytosol upon mitochondrial removal. Our data suggests that mitochondria contribute to the secretion of miR223 into exosomes. When mitochondria are removed by mitophagy, cytosolic miR223 is not efficiently secreted, which provides an alternative explanation for the observed increase in miR223 level after mitochondrial removal.

11) Figure 3i - What is the meaning of "Urd" in the figure label? This isn't mentioned anywhere.

“Urd” represents Uridine. Uridine is now spelled out in figure 3i. The absence of mitochondria can impact the function of the mitochondrial enzyme dihydroorotate dehydrogenase, which plays a role in pyrimidine synthesis. To address this issue, one approach is to supplement the cell culture medium with Urd. A previous study demonstrated that primary fibroblasts showed positive responses when Urd was added to the cell culture medium, resulting in improved cell viability for extended periods of time (Correia-Melo et al., 2017).

12) Figure 3j - The data is presented as a ratio of EV/cell. Again, this inaccurately represents the amount of miR223 in the EV. This issue is apparent when looking at Figures 3h and 3j. In 3h, CCCP causes an upregulation of intracellular miR223. As such, the presumed decrease in EV miR233 after CCCP (3j) could be an artifact due to increased levels of intracellular miR223. Both intracellular and EV levels of miRs need to be shown.

Both the intracellular and exosomal levels of miR223 have been included in Figure 3j.

13) In Figure 4, the authors show that when overexpressed, YBX1 will pulldown YBAP1. Can the authors comment as to why none of the earlier purifications show this finding (Figure 1 for example)? Even more curious is that when YBAP1 is purified, YBX1 does not co-purify (Figure 4 supplement 1a, b).

In Figure 4a-b, human YBX1 fused with a Strep II tag was purified from 293T cells using Strep-Tactin® Sepharose® resin in a one-step purification process. Our data has shown that YBAP1 is expressed in 293T cells.

In Figure 1 and Figure 4 Supplement 1a, human YBX1 or YBAP1 fused with His and MBP tags were purified from insect cells using a three-step purification process involving Ni-NTA His-Pur resin, amylose resin, and Superdex-200 gel filtration chromatography.

One possibility is that human YBX1 or YBAP1 may not interact well with insect YBAP1 or YBX1, which could result in separate tagged forms of YBX1 or YBAP1 isolated from insect cells.

Another possibility is that the expression levels of insect YBAP1 and YBX1 may be too low. Consequently, tagged forms YBX1 or YBAP1 expressed in insect cells may copurify with partners not readily detected by Coomassie blue stain. However, in Figure 4 Supplement 1b, human YBX1 fused with His and MBP tags was co-expressed with non-tagged human YBAP1, and both bands of YBX1 and YBAP1 were visible on the Coomassie blue gel after purification using Ni-NTA His-Pur resin, amylose resin, and Superdex-200 gel filtration chromatography.

14) Figure 4f, g - The text associated with these figures is very confusing, as is the labeling for the input. Also, what is "miR223 Fold change" in this regard? Seeing as your IgG should not have IP'd anything, normalizing to IgG can amplify noise. As such, RIP assays are typically presented as % input or fold enrichment.

The RIP assay results have been calculated and presented as a % input in Figure 4g.

15) Figure 4h - The authors show binding between miR223 and YBAP1 however it is not clear how significant this binding is. There is more than a 30-fold difference in binding affinity between miR223 and YBX1 than between miR223 and YBAP1. Even more, when comparing the EMSAs and fraction bound from figures 1 and 2 to those of Figure 4h, the binding between miR223 and YBAP1 more closely resembles that of miR190 and YBX1, which the authors state is a non-binder of YBX1. The authors will need to reconcile these discrepancies.

We agree that the binding of YBAP and YBX1 differ quite significantly in the affinity of their interaction with miR223. It is difficult to draw conclusions from a comparison of the affinities of YBX1 for miR190 and YBAP1 for miR223. Nonetheless, a quantitative difference in the interaction of YBAP1 with miR223 and miR190 is apparent (Fig. 4 h, I, j) and we observed no enrichment miR190 in isolated mitochondria (Fig. 3 supplement 1a) whereas YBAP1 selectively IP’d miR223 from isolated mitochondria (Fig. 4 f and g).

16) Can the authors present the Kd values for EMSA data?

The Kd values for the EMSA data have been added to the respective figures.

17) Figure 5 - Does YBAP1-KO affect mitochondrial protein integrity or numbers?

We generated stable cell lines expressing 3xHA-GFP-OMP25 in both 293T WT and YBAP1-KO cells, but we did not observe any alterations in mitochondrial morphology (Author response image 1).

Author response image 1.

Additionally, we performed a comparison of different mitochondrial markers using immunoblot in 293T WT cells and YBAP1-KO cells and did not observe any changes in these markers (data has been included in Figure 5b.).

18) Figure 6a - Are the authors using YBAP1 as their mitochondrial marker? Please include TOM20 and/or 22.

In Figure 4c and 4e, our data clearly demonstrate that the majority of YBAP1 is localized in the mitochondria.

To further validate this localization, we performed immunofluorescence staining using antibodies against endogenous Tom20 and YBX1. The immunofluorescence images document YBX1 associated with mitochondria (Author response image 2 and new Fig 6a.).

Author response image 2.

19) Figure 6b - Rab5 is an early endosome marker and may not fully represent the organelles that become MVBs. Co-localization at this point does not suggest that associating proteins will be present in the exosome, and it is possible that the authors are looking at the precursor of a recycling endosome. Even more, exosome loading does not occur at the early endosome, but instead at the MVB. Perhaps looking at markers of the late endosome such as Rab7 or ideally markers of the MVB such as M6P or CD63 would help draw an association between YBX1, YBAP1, and the exosome. Also, If the authors want to make the claim that interactions at the early endosome leads to secretion as an exosome, the authors should show that isolated EVs from Rab5Q79L-expressing cells contain miR223.

We have previously used overexpressed Rab5(Q79L) to monitor the localization of exosomal content, specifically CD63 and YBX1, in enlarged endosomes (Liu et al. 2021, Fig. 4A, B). These endosomes exhibit a mixture of early and late endocytic markers, including CD63. (Wegner et al., 2010). Hence, the presence of Rab5(Q79L)-positive enlarged endosomes does not solely indicate early endosomes.

20) The mentioning of P-bodies is interesting but at no time is an association addressed. This is therefore an overly speculative conclusion. Either show an association or leave this out of the manuscript.

In a previous paper we demonstrated that YBX1 puncta colocalize with P-body markers EDC4, Dcp1 and DDX6 (Liu et al., 2021).

21) In lines 55-58, the authors make the comment "However, many of these studies used sedimentation at ~100,000 g to collect EVs, which may also collect RNP particles not enclosed within membranes which complicates the interpretation of these data." Do RNPs not dissolve when secreted? Can the authors give a reference for this statement?

In a previous paper, we demonstrated that the RNP Ago2 does not dissolve in the conditioned medium and is not in vesicles but sediments to the bottom of a density gradient (Temoche-Diaz et al., 2019).

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Strengths:

The study was designed as a 6-month follow-up, with repeated behavioral and EEG measurements through disease development, providing valuable and interesting findings on AD progression and the effect of early-life choline supplantation. Moreover, the behavioral data that suggest an adverse effect of low choline in WT mice are interesting and important beyond the context of AD.

Thank you for identifying several strengths.

Weaknesses:

(1) The multiple headings and subheadings, focusing on the experimental method rather than the narrative, reduce the readability.

We have reduced the number of headings.

(2) Quantification of NeuN and FosB in WT littermates is needed to demonstrate rescue of neuronal death and hyperexcitability by high choline supplementation and also to gain further insights into the adverse effect of low choline on the performance of WT mice in the behavioral test.

We agree and have added WT data for the NeuN and ΔFosB analyses. These data are included in the text and figures. For NeuN, the Figure is Figure 6. For ΔFosB it is Figure 7. In brief, the high choline diet restored NeuN and ΔFosB to the levels of WT mice.

Below is Figure 6 and its legend to show the revised presentation of data for NeuN. Afterwards is the revised figure showing data for ΔFosB. After that are the sections of the Results that have been revised.

Author response image 1.

Choline supplementation improved NeuN immunoreactivity (ir) in hilar cells in Tg2576 animals. A. Representative images of NeuN-ir staining in the anterior DG of Tg2576 animals. (1) A section from a Tg2576 mouse fed the low choline diet. The area surrounded by a box is expanded below. Red arrows point to NeuN-ir hilar cells. Mol=molecular layer, GCL=granule cell layer, HIL=hilus. Calibration for the top row, 100 µm; for the bottom row, 50 µm. (2) A section from a Tg2576 mouse fed the intermediate diet. Same calibrations as for 1. (3) A section from a Tg2576 mouse fed the high choline diet. Same calibrations as for 1. B. Quantification methods. Representative images demonstrate the thresholding criteria used to quantify NeuN-ir. (1) A NeuN-stained section. The area surrounded by the white box is expanded in the inset (arrow) to show 3 hilar cells. The 2 NeuN-ir cells above threshold are marked by blue arrows. The 1 NeuN-ir cell below threshold is marked by a green arrow. (2) After converting the image to grayscale, the cells above threshold were designated as red. The inset shows that the two cells that were marked by blue arrows are red while the cell below threshold is not. (3) An example of the threshold menu from ImageJ showing the way the threshold was set. Sliders (red circles) were used to move the threshold to the left or right of the histogram of intensity values. The final position of the slider (red arrow) was positioned at the onset of the steep rise of the histogram. C. NeuN-ir in Tg2576 and WT mice. Tg2576 mice had either the low, intermediate, or high choline diet in early life. WT mice were fed the standard diet (intermediate choline). (1) Tg2576 mice treated with the high choline diet had significantly more hilar NeuN-ir cells in the anterior DG compared to Tg2576 mice that had been fed the low choline or intermediate diet. The values for Tg2576 mice that received the high choline diet were not significantly different from WT mice, suggesting that the high choline diet restored NeuN-ir. (2) There was no effect of diet or genotype in the posterior DG, probably because the low choline and intermediate diet did not appear to lower hilar NeuN-ir.

Author response image 2.

Choline supplementation reduced ∆FosB expression in dorsal GCs of Tg2576 mice. A. Representative images of ∆FosB staining in GCL of Tg2576 animals from each treatment group. (1) A section from a low choline-treated mouse shows robust ∆FosB-ir in the GCL. Calibration, 100 µm. Sections from intermediate (2) and high choline (3)-treated mice. Same calibration as 1. B. Quantification methods. Representative images demonstrating the thresholding criteria established to quantify ∆FosB. (1) A ∆FosB -stained section shows strongly-stained cells (white arrows). (2) A strict thresholding criteria was used to make only the darkest stained cells red. C. Use of the strict threshold to quantify ∆FosB-ir. (1) Anterior DG. Tg2576 mice treated with the choline supplemented diet had significantly less ∆FosB-ir compared to the Tg2576 mice fed the low or intermediate diets. Tg2576 mice fed the high choline diet were not significantly different from WT mice, suggesting a rescue of ∆FosB-ir. (2) There were no significant differences in ∆FosB-ir in posterior sections. D. Methods are shown using a threshold that was less strict. (1) Some of the stained cells that were included are not as dark as those used for the strict threshold (white arrows). (2) All cells above the less conservative threshold are shown in red. E. Use of the less strict threshold to quantify ∆FosB-ir. (1) Anterior DG. Tg2576 mice that were fed the high choline diet had less ΔFosB-ir pixels than the mice that were fed the other diets. There were no differences from WT mice, suggesting restoration of ∆FosB-ir by choline enrichment in early life. (2) Posterior DG. There were no significant differences between Tg2576 mice fed the 3 diets or WT mice.

Results, Section C1, starting on Line 691:

“To ask if the improvement in NeuN after MCS in Tg256 restored NeuN to WT levels we used WT mice. For this analysis we used a one-way ANOVA with 4 groups: Low choline Tg2576, Intermediate Tg2576, High choline Tg2576, and Intermediate WT (Figure 5C). Tukey-Kramer multiple comparisons tests were used as the post hoc tests. The WT mice were fed the intermediate diet because it is the standard mouse chow, and this group was intended to reflect normal mice. The results showed a significant group difference for anterior DG (F(3,25)=9.20; p=0.0003; Figure 5C1) but not posterior DG (F(3,28)=0.867; p=0.450; Figure 5C2). Regarding the anterior DG, there were more NeuN-ir cells in high choline-treated mice than both low choline (p=0.046) and intermediate choline-treated Tg2576 mice (p=0.003). WT mice had more NeuN-ir cells than Tg2576 mice fed the low (p=0.011) or intermediate diet (p=0.003). Tg2576 mice that were fed the high choline diet were not significantly different from WT (p=0.827).”

Results, Section C2, starting on Line 722:

“There was strong expression of ∆FosB in Tg2576 GCs in mice fed the low choline diet (Figure 7A1). The high choline diet and intermediate diet appeared to show less GCL ΔFosB-ir (Figure 7A2-3). A two-way ANOVA was conducted with the experimental group (Tg2576 low choline diet, Tg2576 intermediate choline diet, Tg2576 high choline diet, WT intermediate choline diet) and location (anterior or posterior) as main factors. There was a significant effect of group (F(3,32)=13.80, p=<0.0001) and location (F(1,32)=8.69, p=0.006). Tukey-Kramer post-hoc tests showed that Tg2576 mice fed the low choline diet had significantly greater ΔFosB-ir than Tg2576 mice fed the high choline diet (p=0.0005) and WT mice (p=0.0007). Tg2576 mice fed the low and intermediate diets were not significantly different (p=0.275). Tg2576 mice fed the high choline diet were not significantly different from WT (p>0.999). There were no differences between groups for the posterior DG (all p>0.05).”

“∆FosB quantification was repeated with a lower threshold to define ∆FosB-ir GCs (see Methods) and results were the same (Figure 7D). Two-way ANOVA showed a significant effect of group (F(3,32)=14.28, p< 0.0001) and location (F(1,32)=7.07, p=0.0122) for anterior DG but not posterior DG (Figure 7D). For anterior sections, Tukey-Kramer post hoc tests showed that low choline mice had greater ΔFosB-ir than high choline mice (p=0.0024) and WT mice (p=0.005) but not Tg2576 mice fed the intermediate diet (p=0.275); Figure 7D1). Mice fed the high choline diet were not significantly different from WT (p=0.993; Figure 7D1). These data suggest that high choline in the diet early in life can reduce neuronal activity of GCs in offspring later in life. In addition, low choline has an opposite effect, suggesting low choline in early life has adverse effects.”

(3) Quantification of the discrimination ratio of the novel object and novel location tests can facilitate the comparison between the different genotypes and diets.

We have added the discrimination index for novel object location to the paper. The data are in a new figure: Figure 3. In brief, the results for discrimination index are the same as the results done originally, based on the analysis of percent of time exploring the novel object.

Below is the new Figure and legend, followed by the new text in the Results.

Author response image 3.

Novel object location results based on the discrimination index. A. Results are shown for the 3 months-old WT and Tg2576 mice based on the discrimination index. (1) Mice fed the low choline diet showed object location memory only in WT. (2) Mice fed the intermediate diet showed object location memory only in WT. (3) Mice fed the high choline diet showed memory both for WT and Tg2576 mice. Therefore, the high choline diet improved memory in Tg2576 mice. B. The results for the 6 months-old mice are shown. (1-2) There was no significant memory demonstrated by mice that were fed either the low or intermediate choline diet. (3) Mice fed a diet enriched in choline showed memory whether they were WT or Tg2576 mice. Therefore, choline enrichment improved memory in all mice.

Results, Section B1, starting on line 536:

“The discrimination indices are shown in Figure 3 and results led to the same conclusions as the analyses in Figure 2. For the 3 months-old mice (Figure 3A), the low choline group did not show the ability to perform the task for WT or Tg2576 mice. Thus, a two-way ANOVA showed no effect of genotype (F(1,74)=0.027, p=0.870) or task phase (F(1,74)=1.41, p=0.239). For the intermediate diet-treated mice, there was no effect of genotype (F(1,50)=0.3.52, p=0.067) but there was an effect of task phase (F(1,50)=8.33, p=0.006). WT mice showed a greater discrimination index during testing relative to training (p=0.019) but Tg2576 mice did not (p=0.664). Therefore, Tg2576 mice fed the intermediate diet were impaired. In contrast, high choline-treated mice performed well. There was a main effect of task phase (F(1,68)=39.61, p=<0.001) with WT (p<0.0001) and Tg2576 mice (p=0.0002) showing preference for the moved object in the test phase. Interestingly, there was a main effect of genotype (F(1,68)=4.50, p=0.038) because the discrimination index for WT training was significantly different from Tg2576 testing (p<0.0001) and Tg2576 training was significantly different from WT testing (p=0.0003).”

“The discrimination indices of 6 months-old mice led to the same conclusions as the results in Figure 2. There was no evidence of discrimination in low choline-treated mice by two-way ANOVA (no effect of genotype, (F(1,42)=3.25, p=0.079; no effect of task phase, F(1,42)=0.278, p=0.601). The same was true of mice fed the intermediate diet (genotype, F(1,12)=1.44, p=0.253; task phase, F(1,12)=2.64, p=0.130). However, both WT and Tg2576 mice performed well after being fed the high choline diet (effect of task phase, (F(1,52)=58.75, p=0.0001, but not genotype (F(1,52)=1.197, p=0.279). Tukey-Kramer post-hoc tests showed that both WT (p<0.0001) and Tg2576 mice that had received the high choline diet (p=0.0005) had elevated discrimination indices for the test session.”

(4) The longitudinal analyses enable the performance of multi-level correlations between the discrimination ratio in NOR and NOL, NeuN and Fos levels, multiple EEG parameters, and premature death. Such analysis can potentially identify biomarkers associated with AD progression. These can be interesting in different choline supplementation, but also in the standard choline diet.

We agree and added correlations to the paper in a new figure (Figure 9). Below is Figure 9 and its legend. Afterwards is the new Results section.

Author response image 4.

Correlations between IIS, Behavior, and hilar NeuN-ir. A. IIS frequency over 24 hrs is plotted against the preference for the novel object in the test phase of NOL. A greater preference is reflected by a greater percentage of time exploring the novel object. (1) The mice fed the high choline diet (red) showed greater preference for the novel object when IIS were low. These data suggest IIS impaired object location memory in the high choline-treated mice. The low choline-treated mice had very weak preference and very few IIS, potentially explaining the lack of correlation in these mice. (2) There were no significant correlations for IIS and NOR. However, there were only 4 mice for the high choline group, which is a limitation. B. IIS frequency over 24 hrs is plotted against the number of dorsal hilar cells expressing NeuN. The dorsal hilus was used because there was no effect of diet on the posterior hilus. (1) Hilar NeuN-ir is plotted against the preference for the novel object in the test phase of NOL. There were no significant correlations. (2) Hilar NeuN-ir was greater for mice that had better performance in NOR, both for the low choline (blue) and high choline (red) groups. These data support the idea that hilar cells contribute to object recognition (Kesner et al. 2015; Botterill et al. 2021; GoodSmith et al. 2022).

Results, Section F, starting on Line 801:

“F. Correlations between IIS and other measurements

As shown in Figure 9A, IIS were correlated to behavioral performance in some conditions. For these correlations, only mice that were fed the low and high choline diets were included because mice that were fed the intermediate diet did not have sufficient EEG recordings in the same mouse where behavior was studied. IIS frequency over 24 hrs was plotted against the preference for the novel object in the test phase (Figure 9A). For NOL, IIS were significantly less frequent when behavior was the best, but only for the high choline-treated mice (Pearson’s r, p=0.022). In the low choline group, behavioral performance was poor regardless of IIS frequency (Pearson’s r, p=0.933; Figure 9A1). For NOR, there were no significant correlations (low choliNe, p=0.202; high choline, p=0.680) but few mice were tested in the high choline-treated mice (Figure 9B2).

We also tested whether there were correlations between dorsal hilar NeuN-ir cell numbers and IIS frequency. In Figure 9B, IIS frequency over 24 hrs was plotted against the number of dorsal hilar cells expressing NeuN. The dorsal hilus was used because there was no effect of diet on the posterior hilus. For NOL, there was no significant correlation (low choline, p=0.273; high choline, p=0.159; Figure 9B1). However, for NOR, there were more NeuN-ir hilar cells when the behavioral performance was strongest (low choline, p=0.024; high choline, p=0.016; Figure 9B2). These data support prior studies showing that hilar cells, especially mossy cells (the majority of hilar neurons), contribute to object recognition (Botterill et al. 2021; GoodSmith et al. 2022).”

We also noted that all mice were not possible to include because they died or other reasons, such a a loss of the headset (Results, Section A, Lines 463-464): Some mice were not possible to include in all assays either because they died before reaching 6 months or for other reasons.

Reviewer #2 (Public Review):

Strengths:

The strength of the group was the ability to monitor the incidence of interictal spikes (IIS) over the course of 1.2-6 months in the Tg2576 Alzheimer's disease model, combined with meaningful behavioral and histological measures. The authors were able to demonstrate MCS had protective effects in Tg2576 mice, which was particularly convincing in the hippocampal novel object location task.

We thank the Reviewer for identifying several strengths.

Weaknesses:

Although choline deficiency was associated with impaired learning and elevated FosB expression, consistent with increased hyperexcitability, IIS was reduced with both low and high choline diets. Although not necessarily a weakness, it complicates the interpretation and requires further evaluation.

We agree and we revised the paper to address the evaluations that were suggested.

Reviewer #1 (Recommendations For The Authors):

(1) A reference directing to genotyping of Tg2576 mice is missing.

We apologize for the oversight and added that the mice were genotyped by the New York University Mouse Genotyping core facility.

Methods, Section A, Lines 210-211: “Genotypes were determined by the New York University Mouse Genotyping Core facility using a protocol to detect APP695.”

(2) Which software was used to track the mice in the behavioral tests?

We manually reviewed videos. This has been clarified in the revised manuscript. Methods, Section B4, Lines 268-270: Videos of the training and testing sessions were analyzed manually. A subset of data was analyzed by two independent blinded investigators and they were in agreement.

(3) Unexpectedly, a low choline diet in AD mice was associated with reduced frequency of interictal spikes yet increased mortality and spontaneous seizures. The authors attribute this to postictal suppression.

We did not intend to suggest that postictal depression was the only cause. It was a suggestion for one of many potential explanations why seizures would influence IIS frequency. For postictal depression, we suggested that postictal depression could transiently reduce IIS. We have clarified the text so this is clear (Discussion, starting on Line 960):

If mice were unhealthy, IIS might have been reduced due to impaired excitatory synaptic function. Another reason for reduced IIS is that the mice that had the low choline diet had seizures which interrupted REM sleep. Thus, seizures in Tg2576 mice typically started in sleep. Less REM sleep would reduce IIS because IIS occur primarily in REM. Also, seizures in the Tg2576 mice were followed by a depression of the EEG (postictal depression; Supplemental Figure 3) that would transiently reduce IIS. A different, radical explanation is that the intermediate diet promoted IIS rather than low choline reducing IIS. Instead of choline, a constituent of the intermediate diet may have promoted IIS.

However, reduced spike frequency is already evident at 5 weeks of age, a time point with a low occurrence of premature death. A more comprehensive analysis of EEG background activity may provide additional information if the epileptic activity is indeed reduced at this age.

We did not intend to suggest that premature death caused reduced spike frequency. We have clarified the paper accordingly. We agree that a more in-depth EEG analysis would be useful but is beyond the scope of the study.

(4) Supplementary Fig. 3 depicts far more spikes / 24 h compared to Fig. 7B (at least 100 spikes/24h in Supplementary Fig. 3 and less than 10 spikes/24h in Fig. 7B).

We would like to clarify that before and after a seizure the spike frequency is unusually high. Therefore, there are far more spikes than prior figures.

We clarified this issue by adding to the Supplemental Figure more data. The additional data are from mice without a seizure, showing their spikes are low in frequency.

All recordings lasted several days. We included the data from mice with a seizure on one of the days and mice without any seizures. For mice with a seizure, we graphed IIS frequency for the day before, the day of the seizure, and the day after. For mice without a seizure, IIS frequency is plotted for 3 consecutive days. When there was a seizure, the day before and after showed high numbers of spikes. When there was no seizure on any of the 3 days, spikes were infrequent on all days.

The revised figure and legend are shown below. It is Supplemental Figure 4 in the revised submission.

Author response image 5.

IIS frequency before and after seizures. A. Representative EEG traces recorded from electrodes implanted in the skull over the left frontal cortex, right occipital cortex, left hippocampus (Hippo) and right hippocampus during a spontaneous seizure in a 5 months-old Tg2576 mouse. Arrows point to the start (green arrow) and end of the seizure (red arrow), and postictal depression (blue arrow). B. IIS frequency was quantified from continuous video-EEG for mice that had a spontaneous seizure during the recording period and mice that did not. IIS frequency is plotted for 3 consecutive days, starting with the day before the seizure (designated as day 1), and ending with the day after the seizure (day 3). A two-way RMANOVA was conducted with the day and group (mice with or without a seizure) as main factors. There was a significant effect of day (F(2,4)=46.95, p=0.002) and group (seizure vs no seizure; F(1,2)=46.01, p=0.021) and an interaction of factors (F(2,4)=46.68, p=0.002)..Tukey-Kramer post-hoc tests showed that mice with a seizure had significantly greater IIS frequencies than mice without a seizure for every day (day 1, p=0.0005; day 2, p=0.0001; day 3, p=0.0014). For mice with a seizure, IIS frequency was higher on the day of the seizure than the day before (p=0.037) or after (p=0.010). For mice without a seizure, there were no significant differences in IIS frequency for day 1, 2, or 3. These data are similar to prior work showing that from one day to the next mice without seizures have similar IIS frequencies (Kam et al., 2016).

In the text, the revised section is in the Results, Section C, starting on Line 772:

“At 5-6 months, IIS frequencies were not significantly different in the mice fed the different diets (all p>0.05), probably because IIS frequency becomes increasingly variable with age (Kam et al. 2016). One source of variability is seizures, because there was a sharp increase in IIS during the day before and after a seizure (Supplemental Figure 4). Another reason that the diets failed to show differences was that the IIS frequency generally declined at 5-6 months. This can be appreciated in Figure 8B and Supplemental Figure 6B. These data are consistent with prior studies of Tg2576 mice where IIS increased from 1 to 3 months but then waxed and waned afterwards (Kam et al., 2016).”

(5) The data indicating the protective effect of high choline supplementation are valuable, yet some of the claims are not completely supported by the data, mainly as the analysis of littermate WT mice is not complete.

We added WT data to show that the high choline diet restored cell loss and ΔFosB expression to WT levels. These data strengthen the argument that the high choline diet was valuable. See the response to Reviewer #1, Public Review Point #2.

• Line 591: "The results suggest that choline enrichment protected hilar neurons from NeuN loss in Tg2576 mice." A comparison to NeuN expression in WT mice is needed to make this statement.

These data have been added. See the response to Reviewer #1, Public Review Point #2.

• Line 623: "These data suggest that high choline in the diet early in life can reduce hyperexcitability of GCs in offspring later in life. In addition, low choline has an opposite effect, again suggesting this maternal diet has adverse effects." Also here, FosB quantification in WT mice is needed.

These data have been added. See the response to Reviewer #1, Public Review Point #2.

(7) Was the effect of choline associated with reduced tauopathy or A levels?

The mice have no detectable hyperphosphorylated tau. The mice do have intracellular A before 6 months. This is especially the case in hilar neurons, but GCs have little (Criscuolo et al., eNeuro, 2023). However, in neurons that have reduced NeuN, we found previously that antibodies generally do not work well. We think it is because the neurons become pyknotic (Duffy et al., 2015), a condition associated with oxidative stress which causes antigens like NeuN to change conformation due to phosphorylation. Therefore, we did not conduct a comparison of hilar neurons across the different diets.

(8) Since the mice were tested at 3 months and 6 months, it would be interesting to see the behavioral difference per mouse and the correlation with EEG recording and immunohistological analyses.

We agree that would be valuable and this has been added to the paper. Please see response to Reviewer #1, Public Review Point #4.

Reviewer #2 (Recommendations For The Authors):

There were several areas that could be further improved, particularly in the areas of data analysis (particularly with images and supplemental figures), figure presentation, and mechanistic speculation.

Major points:

(1) It is understandable that, for the sake of labor and expense, WT mice were not implanted with EEG electrodes, particularly since previous work showed that WT mice have no IIS (Kam et al. 2016). However, from a standpoint of full factorial experimental design, there are several flaws - purists would argue are fatal flaws. First, the lack of WT groups creates underpowered and imbalanced groups, constraining statistical comparisons and likely reducing the significance of the results. Also, it is an assumption that diet does not influence IIS in WT mice. Secondly, with a within-subject experimental design (as described in Fig. 1A), 6-month-old mice are not naïve if they have previously been tested at 3 months. Such an experimental design may reduce effect size compared to non-naïve mice. These caveats should be included in the Discussion. It is likely that these caveats reduce effect size and that the actual statistical significance, were the experimental design perfect, would be higher overall.

We agree and have added these points to the Limitations section of the Discussion. Starting on Line 1050: In addition, groups were not exactly matched. Although WT mice do not have IIS, a WT group for each of the Tg2576 groups would have been useful. Instead, we included WT mice for the behavioral tasks and some of the anatomical assays. Related to this point is that several mice died during the long-term EEG monitoring of IIS.

(2) Since behavior, EEG, NeuN and FosB experiments seem to be done on every Tg2576 animal, it seems that there are missed opportunities to correlate behavior/EEG and histology on a per-mouse basis. For example, rather than speculate in the discussion, why not (for example) directly examine relationships between IIS/24 hours and FosB expression?

We addressed this point above in responding to Reviewer #1, Public Review Point #4.

(3) Methods of image quantification should be improved. Background subtraction should be considered in the analysis workflow (see Fig. 5C and Fig. 6C background). It would be helpful to have a Methods figure illustrating intermediate processing steps for both NeuN and FosB expression.

We added more information to improve the methods of quantification. We did use a background subtraction approach where ImageJ provides a histogram of intensity values, and it determines when there is a sharp rise in staining relative to background. That point is where we set threshold. We think it is a procedure that has the least subjectivity.

We added these methods to the Methods section and expanded the first figure about image quantification, Figure 6B. That figure and legend are shown above in response to Reviewer #1, Point #2.

This is the revised section of the Methods, Section C3, starting on Line 345:

“Photomicrographs were acquired using ImagePro Plus V7.0 (Media Cybernetics) and a digital camera (Model RET 2000R-F-CLR-12, Q-Imaging). NeuN and ∆FosB staining were quantified from micrographs using ImageJ (V1.44, National Institutes of Health). All images were first converted to grayscale and in each section, the hilus was traced, defined by zone 4 of Amaral (1978). A threshold was then calculated to identify the NeuN-stained cell bodies but not background. Then NeuN-stained cell bodies in the hilus were quantified manually. Note that the threshold was defined in ImageJ using the distribution of intensities in the micrograph. A threshold was then set using a slider in the histogram provided by Image J. The slider was pushed from the low level of staining (similar to background) to the location where staining intensity made a sharp rise, reflecting stained cells. Cells with labeling that was above threshold were counted.”

(4) This reviewer is surprised that the authors do not speculate more about ACh-related mechanisms. For example, choline deficiency would likely reduce Ach release, which could have the same effect on IIS as muscarinic antagonism (Kam et al. 2016), and could potentially explain the paradoxical effects of a low choline diet on reducing IIS. Some additional mechanistic speculation would be helpful in the Discussion.

We thank the Reviewer for noting this so we could add it to the Discussion. We had not because we were concerned about space limitations.

The Discussion has a new section starting on Line 1009:

“Choline and cholinergic neurons

There are many suggestions for the mechanisms that allow MCS to improve health of the offspring. One hypothesis that we are interested in is that MCS improves outcomes by reducing IIS. Reducing IIS would potentially reduce hyperactivity, which is significant because hyperactivity can increase release of A. IIS would also be likely to disrupt sleep since it represents aberrant synchronous activity over widespread brain regions. The disruption to sleep could impair memory consolidation, since it is a notable function of sleep (Graves et al. 2001; Poe et al. 2010). Sleep disruption also has other negative consequences such as impairing normal clearance of A (Nedergaard and Goldman 2020). In patients, IIS and similar events, IEDs, are correlated with memory impairment (Vossel et al. 2016).

How would choline supplementation in early life reduce IIS of the offspring? It may do so by making BFCNs more resilient. That is significant because BFCN abnormalities appear to cause IIS. Thus, the cholinergic antagonist atropine reduced IIS in vivo in Tg2576 mice. Selective silencing of BFCNs reduced IIS also. Atropine also reduced elevated synaptic activity of GCs in young Tg2576 mice in vitro. These studies are consistent with the idea that early in AD there is elevated cholinergic activity (DeKosky et al. 2002; Ikonomovic et al. 2003; Kelley et al. 2014; Mufson et al. 2015; Kelley et al. 2016), while later in life there is degeneration. Indeed, the chronic overactivity could cause the degeneration.

Why would MCS make BFCNs resilient? There are several possibilities that have been explored, based on genes upregulated by MCS. One attractive hypothesis is that neurotrophic support for BFCNs is retained after MCS but in aging and AD it declines (Gautier et al. 2023). The neurotrophins, notably nerve growth factor (NGF) and brain-derived neurotrophic factor (BDNF) support the health of BFCNs (Mufson et al. 2003; Niewiadomska et al. 2011).”

Minor points:

(1) The vendor is Dyets Inc., not Dyets.

Thank you. This correction has been made.

(2) Anesthesia chamber not specified (make, model, company).

We have added this information to the Methods, Section D1, starting on Line 375: The animals were anesthetized by isoflurane inhalation (3% isoflurane. 2% oxygen for induction) in a rectangular transparent plexiglas chamber (18 cm long x 10 cm wide x 8 cm high) made in-house.

(3) It is not clear whether software was used for the detection of behavior. Was position tracking software used or did blind observers individually score metrics?

We have added the information to the paper. Please see the response to Reviewer #1, Recommendations for Authors, Point #2.

(4) It is not clear why rat cages and not a true Open Field Maze were used for NOL and NOR.

We used mouse cages because in our experience that is what is ideal to detect impairments in Tg2576 mice at young ages. We think it is why we have been so successful in identifying NOL impairments in young mice. Before our work, most investigators thought behavior only became impaired later. We would like to add that, in our experience, an Open Field Maze is not the most common cage that is used.

(5) Figure 1A is not mentioned.

It had been mentioned in the Introduction. Figure B-D was the first Figure mentioned in the Results so that is why it might have been missed. We now have added it to the first section of the Results, Line 457, so it is easier to find.

6) Although Fig 7 results are somewhat complicated compared to Fig. 5 and 6 results, EEG comes chronologically earlier than NeuN and FosB expression experiments.

We have kept the order as is because as the Reviewer said, the EEG is complex. For readability, we have kept the EEG results last.

(7) Though the statistical analysis involved parametric and nonparametric tests, It is not clear which normality tests were used.

We have added the name of the normality tests in the Methods, Section E, Line 443: Tests for normality (Shapiro-Wilk) and homogeneity of variance (Bartlett’s test) were used to determine if parametric statistics could be used. We also added after this sentence clarification: When data were not normal, non-parametric data were used. When there was significant heteroscedasticity of variance, data were log transformed. If log transformation did not resolve the heteroscedasticity, non-parametric statistics were used. Because we added correlations and analysis of survival curves, we also added the following (starting on Line 451): For correlations, Pearson’s r was calculated. To compare survival curves, a Log rank (Mantel-Cox) test was performed.

Figures:

(1) In Fig. 1A, Anatomy should be placed above the line.

We changed the figure so that the word “Anatomy” is now aligned, and the arrow that was angled is no longer needed.

In Fig. 1C and 1D, the objects seem to be moved into the cage, not the mice. This schematic does not accurately reflect the Fig. 1C and 1D figure legend text.

Thank you for the excellent point. The figure has been revised. We also updated it to show the objects more accurately.

Please correct the punctuation in the Fig. 1D legend.

Thank you for mentioning the errors. We corrected the legend.

For ease of understanding, Fig. 1C and 1D should have training and testing labeled in the figure.

Thank you for the suggestion. We have revised the figure as suggested.

Author response image 6.

(2) In Figure 2, error bars for population stats (bar graphs) are not obvious or missing. Same for Figure 3.

We added two supplemental figures to show error bars, because adding the error bars to the existing figures made the symbols, colors, connecting lines and error bars hard to distinguish. For novel object location (Fig. 2) the error bars are shown in Supp. Fig. 2. For novel object recognition, the error bars are shown in Supplemental Fig. 3.

(3) The authors should consider a Methods figure for quantification of NeuN and deltaFOSB (expansions of Fig. 5C and Fig. 6C).

Please see Reviewer #1, Public Review Point #2.

(4) In Figure 5, A should be omitted and mentioned in the Methods/figure legend. B should be enlarged. C should be inset, zoomed-in images of the hilus, with an accompanying analysis image showing a clear reduction in NeuN intensity in low choline conditions compared to intermediate and high choline conditions. In D, X axes could delineate conditions (figure legend and color unnecessary). Figure 5C should be moved to a Methods figure.

We thank the review for the excellent suggestions. We removed A as suggested. We expanded B and included insets. We used different images to show a more obvious reduction of cells for the low choline group. We expanded the Methods schematics. The revised figure is Figure 6 and shown above in response to Reviewer 1, Public Review Point #2.

(5) In Figure 6, A should be eliminated and mentioned in the Methods/figure legend. B should be greatly expanded with higher and lower thresholds shown on subsequent panels (3x3 design).

We removed A as suggested. We expanded B as suggested. The higher and lower thresholds are shown in C. The revised figure is Figure 7 and shown above in response to Reviewer 1, Public Review Point #2.

(6) In Figure 7, A2 should be expanded vertically. A3 should be expanded both vertically and horizontally. B 1 and 2 should be increased, particularly B1 where it is difficult to see symbols. Perhaps colored symbols offset/staggered per group so that the spread per group is clearer.

We added a panel (A4) to show an expansion of A2 and A3. However, we did not see that a vertical expansion would add information so we opted not to add that. We expanded B1 as suggested but opted not to expand B2 because we did not think it would enhance clarity. The revised figure is below.

Author response image 7.

(7) Supplemental Figure 1 could possibly be combined with Figure 1 (use rounded corner rat cage schematic for continuity).

We opted not to combine figures because it would make one extremely large figure. As a result, the parts of the figure would be small and difficult to see.

(8) Supplemental Figure 2 - there does not seem to be any statistical analysis associated with A mentioned in the Results text.

We added the statistical information. It is now Supplemental Figure 4:

Author response image 8.

Mortality was high in mice treated with the low choline diet. A. Survival curves are shown for mice fed the low choline diet and mice fed the high choline diet. The mice fed the high choline diet had a significantly less severe survival curve. B. Left: A photo of a mouse after sudden unexplained death. The mouse was found in a posture consistent with death during a convulsive seizure. The area surrounded by the red box is expanded below to show the outstretched hindlimb (red arrow). Right: A photo of a mouse that did not die suddenly. The area surrounded by the box is expanded below to show that the hindlimb is not outstretched.

The revised text is in the Results, Section E, starting on Line 793:

“The reason that low choline-treated mice appeared to die in a seizure was that they were found in a specific posture in their cage which occurs when a severe seizure leads to death (Supplemental Figure 5). They were found in a prone posture with extended, rigid limbs (Supplemental Figure 5). Regardless of how the mice died, there was greater mortality in the low choline group compared to mice that had been fed the high choline diet (Log-rank (Mantel-Cox) test, Chi square 5.36, df 1, p=0.021; Supplemental Figure 5A).”

Also, why isn't intermediate choline also shown?

We do not have the data from the animals. Records of death were not kept, regrettably.

Perhaps labeling of male/female could also be done as part of this graph.

We agree this would be very interesting but do not have all sex information.

B is not very convincing, though it is understandable once one reads about posture.

We have clarified the text and figure, as well as the legend. They are above.

Are there additional animals that were seen to be in a specific posture?

There are many examples, and we added them to hopefully make it more convincing.

We also added posture in WT mice when there is a death to show how different it is.

Is there any relationship between seizures detected via EEG, as shown in Supplemental Figure 3, and death?

Several mice died during a convulsive seizure, which is the type of seizure that is shown in the Supplemental Figure.

(9) Supplemental Figure 3 seems to display an isolated case in which EEG-detected seizures correlate with increased IIEs. It is not clear whether there are additional documented cases of seizures that could be assembled into a meaningful population graph. If this data does not exist or is too much work to include in this manuscript, perhaps it can be saved for a future paper.

We have added other cases and revised the graph. This is now Supplemental Figure 4 and is shown above in response to Reviewer #1, Recommendation for Authors Point #4.

Frontal is misspelled.

We checked and our copy is not showing a misspelling. However, we are very grateful to the Reviewer for catching many errors and reading the manuscript carefully.

(10) Supplemental Figure 4 seems incomplete in that it does not include EEG data from months 4, 5, and 6 (see Fig. 7B).

We have added data for these ages to the Supplemental Figure (currently Supplemental Figure 6) as part B. In part A, which had been the original figure, only 1.2, 2, and 3 months-old mice were shown because there were insufficient numbers of each sex at other ages. However, by pooling 1.2 and 2 months (Supplemental Figure 6B1), 3 and 4 months (B2) and 5 and 6 months (B3) we could do the analysis of sex. The results are the same – we detected no sex differences.

Author response image 9.

A. IIS frequency was similar for each sex. A. IIS frequency was compared for females and males at 1.2 months (1), 2 months (2), and 3 months (3). Two-way ANOVA was used to analyze the effects of sex and diet. Female and male Tg2576 mice were not significantly different. B. Mice were pooled at 1.2 and 2 months (1), 3 and 4 months (2) and 5 and 6 months (3). Two-way ANOVA analyzed the effects of sex and diet. There were significant effects of diet for (1) and (2) but not (3). There were no effects of sex at any age. (1) There were significant effects of diet (F(2,47)=46.21, p<0.0001) but not sex (F(1,47)=0.106, p=0.746). Female and male mice fed the low choline diet or high choline diet were significantly different from female and male mice fed the intermediate diet (all p<0.05, asterisk). (2) There were significant effects of diet (F(2,32)=10.82, p=0.0003) but not sex (F(1,32)=1.05, p=0.313). Both female and male mice of the low choline group were significantly different from male mice fed the intermediate diet (both p<0.05, asterisk) but no other pairwise comparisons were significant. (3) There were no significant differences (diet, F(2,23)=1.21, p=0.317); sex, F(1,23)=0.844, p=0.368).

The data are discussed the Results, Section G, tarting on Line 843:

In Supplemental Figure 6B we grouped mice at 1-2 months, 3-4 months and 5-6 months so that there were sufficient females and males to compare each diet. A two-way ANOVA with diet and sex as factors showed a significant effect of diet (F(2,47)=46.21; p<0.0001) at 1-2 months of age, but not sex (F1,47)=0.11, p=0.758). Post-hoc comparisons showed that the low choline group had fewer IIS than the intermediate group, and the same was true for the high choline-treated mice. Thus, female mice fed the low choline diet differed from the females (p<0.0001) and males (p<0.0001) fed the intermediate diet. Male mice that had received the low choline diet different from females (p<0.0001) and males (p<0.0001) fed the intermediate diet. Female mice fed the high choline diet different from females (p=0.002) and males (p<0.0001) fed the intermediate diet, and males fed the high choline diet difference from females (p<0.0001) and males (p<0.0001) fed the intermediate diet.

For the 3-4 months-old mice there was also a significant effect of diet (F(2,32)=10.82, p=0.0003) but not sex (F(1,32)=1.05, p=0.313). Post-hoc tests showed that low choline females were different from males fed the intermediate diet (p=0.007), and low choline males were also significantly different from males that had received the intermediate diet (p=0.006). There were no significant effects of diet (F(2,23)=1.21, p=0.317) or sex (F(1,23)=0.84, p=0.368) at 5-6 months of age.

Author Response

Reviewer #1 (Public Review):

Weaknesses:

Gene expression level as a confounding factor was not well controlled throughout the study. Higher gene expression often makes genes less dispensable after gene duplication. Gene expression level is also a major determining factor of evolutionary rates (reviewed in http://www.ncbi.nlm.nih.gov/pubmed/26055156). Some proposed theories explain why gene expression level can serve as a proxy for gene importance (http://www.ncbi.nlm.nih.gov/pubmed/20884723, http://www.ncbi.nlm.nih.gov/pubmed/20485561). In that sense, many genomic/epigenomic features (such as replication timing and repressed transcriptional regulation) that were assumed "neutral" or intrinsic by the authors (or more accurately, independent of gene dispensability) cannot be easily distinguishable from the effect of gene dispersibility.

We thank the reviewer for this important comment. We totally agree that transcriptomic and epigenomic features cannot be easily distinguished from gene dispensability and do not think that these features of the elusive genes can be explained solely by intrinsic properties of the genomes. Our motivation for investigating the expression profiles of the elusive gene is to understand how they lost their functional indispensability (original manuscript L285-286 in Results). We also discussed the possibility that sequence composition and genomic location of elusive genes may be associated with epigenetic features for expression depression, which may result in a decrease of functional constraints (original manuscript L470-474 in Discussion). Nevertheless, we think that the original manuscript may have contained misleading wordings, and thus we have edited them to better convey our view that gene expression and epigenomic features are related to gene function.

(P.2, Introduction) This evolutionary fate of a gene can also be affected by factors independent of gene dispensability, including the mutability of genomic positions, but such features have not been examined well.

(P6, Introduction) These data assisted us to understand how intrinsic genomic features may affect gene fate, leading to gene loss by decreasing the expression level and eventually relaxing the functional importance of ʻelusiveʼ genes.

(P33, Discussion) Another factor is the spatiotemporal suppression of gene expression via epigenetic constraints. Previous studies showed that lowly expressed genes reduce their functional dispensability (Cherry, 2010; Gout et al., 2010), and so do the elusive genes.

Additionally, responding to the advices from Reviewers 1 and 2 [Rev1minor7 and Rev2-Major4], we have added a new section Elusive gene orthologs in the chicken microchromosomes in which we describe the relationship between the elusive genes and chicken microchromosomes. In this section, we also argue for the relationship between the genomic feature of the elusive genes and their transcriptomic and epigenomic characteristics. In the chicken genome, elusive genes did not show reduced pleiotropy of gene expression nor the epigenetic features relevant with the reduction, consistently with the moderation of nucleotide substitution rates. This also suggests that the relaxation of the ‘elusiveness’ is associated with the increase of functional indispensability.

(P27, Elusive gene orthologs in the chicken microchromosomes in Results) Our analyses indicates that the genomic features of the elusive genes such as high GC and high nucleotide substitutions do not always correlate with a reduction in pleiotropy of gene expression that potentially leads to an increase in functional dispensability, although these features have been well conserved across vertebrates. In addition, the avian orthologs of the elusive genes did not show higher KA and KS values than those of the non-elusive genes (Figure 3; Figure 3–figure supplement 1), likely consistent with similar expression levels between them (Figure 5–figure supplement 1) (Cherry, 2010; Zhang and Yang, 2015). With respect to the chicken genome, the sequence features of the elusive genes themselves might have been relaxed during evolution.

Ks was used by the authors to indicate mutation rates. However, synonymous mutations substantially affect gene expression levels (https://pubmed.ncbi.nlm.nih.gov/25768907/, https://pubmed.ncbi.nlm.nih.gov/35676473/). Thus, synonymous mutations cannot be simply assumed as neutral ones and may not be suitable for estimating local mutation rates. If introns can be aligned, they are better sequences for estimating the mutability of a genomic region.

We appreciate the reviewer for this meaningful suggestion. As a response, we have computed the differences in intron sequences between the human and chimpanzee genomes and compared them between the elusive and non-elusive genes. As expected, we found larger sequence differences in introns for the elusive genes than for the non-elusive genes. In Figure 2c of the revised manuscript, we have included the distribution of KI, sequence differences in introns between the human and chimpanzee genomes for the elusive and non-elusive genes. Additionally, we have added the corresponding texts to Results and the procedure to Methods as shown below.

(P11, Identification of human ‘elusive’ genes in Results) In addition, we computed nucleotide substitution rates for introns (KI) between human and chimpanzee (Pan troglodytes) orthologs and compared them between the elusive and non-elusive genes.

(P11, Identification of human ‘elusive’ genes in Results) Our analysis further illuminated larger KS and KI values for the elusive genes than in the non-elusive genes (Figure 2b, c; Figure 2–figure supplement 1). Importantly, the higher rate of synonymous and intronic nucleotide substitutions, which may not affect changes in amino acid residues, indicates that the elusive genes are also susceptible to genomic characteristics independent of selective constraints on gene functions.

(P39, Methods) To compute nucleotide sequence differences of the individual introns, we extracted 473 elusive and 4,626 non-elusive genes that harbored introns aligned with the chimpanzee genome assembly. The nucleotide differences were calculated via the whole genome alignments of hg38 and panTro6 retrieved from the UCSC genome browser.

The term "elusive gene" is not necessarily intuitive to readers.

We previously published a paper reporting the group of genes that we refer to as ‘elusive genes,’ lost in mammals and aves independently but retained by reptiles, in the gecko genome assembly (Hara et al., 2018, BMC Biology). We initially termed them with a more intuitive name (‘loss-prone genes’) but changed it because one of our peer-reviewers did not agree to use this name. Later on, we have continuously used this term in another paper (Hara et al., 2018, Nat. Ecol. Evol.). In addition, some other groups have used the word ‘elusive’ with a similar intention to ours (Prokop et al, 2014, PLOS ONE, doi: 10.1371/journal.pone.0092751; Ribas et al., 2011, BMC Genomics, doi: 10.1186/1471-2164-12-240). We would appreciate the reviewer’s understanding of this naming to ensure the consistency of our researches on gene loss. In the revised manuscript, we have added sentences to provide a more intuitive guide to ‘elusive genes’,

(P6, Introduction) We previously referred to the nature of genes prone to loss as ‘elusive’(Hara et al., 2018a, 2018b). In the present study, we define the elusive genes as those that are retained by modern humans but have been lost independently in multiple mammalian lineages. As a comparison of the elusive genes, we retrieved the genes that were retained by almost all of the mammalian species examined and defined them as ‘non-elusive’, representing those persistent in the genomes.

Reviewer #3 (Public Review):

Overall, the study is descriptive and adds incremental evidence to an existing body of extensive gene loss literature. The topic is specialised and will be of interest to a niche audience. The text is highly redundant, repeating the same false positive issue in the introduction, methods, and discussion sections, while no clear conclusion or interpretation of their main findings are presented.

Major comments

While some of the false discovery rate issues of gene loss detection were addressed in the presented pipeline, the authors fail to test one of the most severe cases of mis-annotating gene loss events: frameshift mutations which cause gene annotation pipelines to fail reporting these genes in the first place. Running a blastx or diamond blastx search of their elusive and non-elusive gene sets against all other genomes, should further enlighten the robustness of their gene loss detection approach

For the revised manuscript, we have refined the elusive gene set as the reviewer suggested. In the genome assemblies, we have searched for the orthologs of the elusive genes for the species in which they were missing. The search has been conducted by querying amino acid sequences of the elusive genes with tblastn as well as MMSeqs2 that performed superior to tblastn in sensitivity and computational speed. In addition, regarding another comment by Reviewer 3. we have searched for the orthologs by referring to existing ortholog annotations. We used the ortholog annotations implemented in RefSeq instead of those from the TOGA pipeline: both employ synteny conservation. We have coordinated the identified orthologs with our gene loss criteria–absence from all the species used in a particular taxon–and excluded 268 genes from the original elusive gene set. These genes contain those missing in the previous gene annotations used in the original manuscript but present in the latest ones, as well as those falsely missing due to incorrect inference of gene trees. Finally, the refined set of 813 elusive genes were subject to comparisons with the non-elusive genes. Importantly, these comparisons retained the significantly different trends of the particular genomic, transcriptomic, and epigenomic features between them except for very few cases (Table R1 included below). This indicates that both initial and revised sets of the elusive genes reflect the nature of the ‘elusiveness,’ though the initial set contained some noises. We have modified the numbers of elusive genes in the corresponding parts of the manuscript including figures and tables. Additionally, we have added the validation procedures in Methods.

Table R1. Difference in statistical significances across different elusive gene sets *The other features showed significantly different trends between the elusive and non-elusive genes for all of the elusive gene sets and thus are not included in this table.

(P38 in Methods) The gene loss events inferred by molecular phylogeny were further assessed by synteny-based ortholog annotations implemented in RefSeq, as well as a homolog search in the genome assemblies (Table S2) with TBLASTN v2.11.0+ (Altschul et al., 1997) and MMSeqs2 (Steinegger and Söding, 2017) referring to the latest RefSeq gene annotations (last accessed on 2 Dec, 2022). This procedure resulted in the identification of 813 elusive genes that harbored three or fewer duplicates. Similarly, we extracted 8,050 human genes whose orthologs were found in all the mammalian species examined and defined them as non-elusive genes.

The reviewer also suggested us investigating falsely-missing genes due to frameshift mutations (in this case we guess that the reviewer assumed the genome assembly that falsely included frameshift mutations). This requires us to search for the orthologs by revisiting the sequencing reads because the frameshift is sometimes caused by indels of erroneous basecalling. We have selected five elusive genes and searched for the fragments of orthologs in sequencing reads for the species in which they are missing. We have retrieved sequencing reads corresponding to the genome assemblies from NCBI SRA and performed sequence similarity search using the program Diamond against the amino acid sequences of the elusive genes and could not find the frameshift that potentially causes the mis-annotation of the elusive genes.

Along this line, we noticed that when annotation files were pooled together via CD-Hit clustering, a 100% identity threshold was chosen (Methods). Since some of the pooled annotations were drawn from less high quality assemblies which yield higher likelihoods of mismatches between annotations, enforcing a 100% identity threshold will artificially remove genes due to this strict constraint. It will be paramount for this study to test the robustness of their findings when 90% and 95% identity thresholds were selected.

cd-hit clustering with 100% sequence identity only clusters those with identical (and sometimes truncated) sequences, and, in the cluster, the sequences other than the representative are discarded. This means that the sequences remain if they are not identical to the other ones. If the similarity threshold is lowered, both identical and highly similar sequences are clustered with each other, and more sequences are discarded. Therefore, our approach that employs clustering with 100% similarity may minimize false positive gene loss.

While some statistical tests were applied (although we do recommend consulting a professional statistician, since some identical distributions tend to show significantly low p-values), the authors fail to discuss the fact that their elusive gene set comprises of ~5% of all human genes (assuming 21,000 genes), while their non-elusive set represents ~40% of all genes. In other words, the authors compare their sequence and genomic features against the genomic background rather than a biological signal (nonelusiveness). An analysis whereby 1,081 genes (same number as elusive set) are randomly sampled from the 21,000 gene pool is compared against the elusive and non-elusive distributions for all presented results will reveal whether the non-elusive set follows a background distribution (noise) or not.

Our study aims to elucidate the characteristics of genes that differentiate their fates, retention or loss. To achieve this, we put this characterization into the comparison between the elusive and non-elusive genes. This comparison highlighted clearly different phylogenetic signals for gene loss between elusive and non-elusive genes, allowing us to extract the features associated with the loss-prone nature. The random sampling set suggested by Reviewer may largely consists of the remainders that were not classified by the elusive and non-elusive genes. However, these remainders may contain a considerable number of genes with distinctive phylogenetic signatures rather than the intermediates between the elusive and nonelusive genes: the genes with multiple loss events in more restricted taxa than our criterion, the ones with frequent duplication, etc. Therefore, we think that a comparison of the elusive genes with the random-sampling set does not achieve our objective: the comparison of the clearly different phylogenetic signals.

We also wondered whether the authors considered testing the links between recombination rate / LD and the genomic locations of their elusive genes (again compared against randomly sampled genes)?

We have retrieved fine-scale recombination rate data of males and females from https://www.decode.com/addendum/ (Suppl. Data of Kong, A et al., Nature, 467:1099–1103, 2010) and have compared them between the gene regions of the elusive and non-elusive genes. Both comparisons show no significant differences: average 0.829 and 0.900 recombinations/kb for the elusive and non-elusive genes, respectively, p=0.898, for males; average 0.836 and 0.846 recombinations/kb for the elusive and non-elusive genes, respectively, p=0.256, for females).

Given the evidence presented in Figure 6b, we do not agree with the statement (l.334-336): "These observations suggest that the elusive genes are unlikely to be regulated by distant regulatory elements". Here, a data population of ~1k genes is compared against a data population of ~8k genes and the presented difference between distributions could be a sample size artefact. We strongly recommend retesting this result with the ~1k randomly sampled genes from the total ~21,000 gene pool and then compare the distributions.

Analogous random sampling analysis should be performed for Fig 6a,d

As described above, our study does not intend to extract signals from background. To make the comparison objectives clear, we have revised the corresponding sentence as below.

(P22, Transcriptomic natures of elusive genes in Results) These observations suggest that the elusive genes are unlikely to be regulated by distant regulatory elements compared with the non-elusive genes (Figure 6b).

We didn't see a clear pattern in Figure 7. Please quantify enrichments with statistical tests. Even if there are enriched regions, why did the authors choose a Shannon entropy cutoff configuration of <1 (low) and >1 (high)? What was the overall entropy value range? If the maximum entropy value was 10 or 100 or even more, then denoting <1 as low and >1 as high seems rather biased.

To use Figure 7 in a new section in Results, we have added an ideogram showing the distribution of the genes that retain the chicken orthologs in microchromosomes. In response to the comment by Reviewer 2, we have performed statistical tests and found that the elusive genes were significantly more abundant in orthologs in microchromosomes than the non-elusive genes. Furthermore, the observation that the elusive genes prefer to be located in gene-rich regions was already statistically supported (Figure 2f).

As shown in Figure 5, Shannon’s H' ranged from zero to approximately 4 (exact maximum value is 3.97) and 5 (5.11) for the GTEx and Descartes gene expression datasets, respectively. Although the threshold H'=1 was an arbitrarily set, we think that it is reasonable to classify the genes with high pleiotropy from those with low pleiotropy.

Author Response:

Reviewer #1:

The dependence of cell volume growth rate on cell size and cell cycle is a long-standing fundamental question that has traditionally been addressed by using unicellular model organisms with simple geometry, for which rough volume estimates can be obtained from bright field images. While it became soon apparent that the volume growth rate depends on cell volume, the experimental error associated with such measurements made it difficult to determine the exact dependencies. This challenge is even more significant for animal cells, whose complex and dynamic geometry makes accurate volume measurements extremely difficult. Other measures for cell size, including mass or fluorescent reporters for protein content, partially bypassed this problem. However, it becomes increasingly clear that cell mass and volume are not strictly coupled, making accurate volume measurements essential. In their previous work, Cadart and colleagues established a 'fluorescent exclusion method', which allows accurate volume measurements of cells with complex geometry. In the present manuscript, Cadart et al. now take the next step and measure the growth trajectories of 1700 HeLa cell cycles with further improved accuracy, providing new insights into animal cell growth.

They convincingly demonstrate that throughout large parts of the cell cycle, individual cells exhibit exponential growth, with the volume-normalized specific growth rate moderately increasing after G1-phase. At the very early stages of the cell cycle, cells exhibit a more complex growth behavior. The authors then go on and analyze the growth rate fluctuations of individual cells, identifying a decrease of the variance of the specific growth rate with cell volume and observed time scale. The authors conclude that the observed growth fluctuations are consistent with additive noise of the absolute growth rate.

The experiments and analysis presented by Cadart et al. are carefully and well executed, and the insights provided (as well as the method established) are an important contribution to our understanding of cell growth. My major concern is that the observed fluctuation pattern seems largely consistent with what would be expected if the fluctuations stem from experimental measurement noise. This fact is appropriately acknowledged, and the authors aim to address this issue by analyzing background noise. However, further controls may be necessary to unambiguously attribute the measured noise to biological fluctuations, rather than experimental error.

We thank the reviewer for their positive feedback and for the appreciation of our work. We performed a series of experimental controls to address the main issue regarding the measured fluctuation pattern, which indicate that it should be of biological origin.

1.) To address whether the observed fluctuations could be due to experimental error, the authors analyze the fluctuations recorded in a cell-sized area of the background, and find that the background fluctuations are small compared to the fluctuations of the volume measurements. I think this is a very important control that supports the interpretation of the authors. However, I am not convinced that the actual measurement error is necessarily of the same amplitude as the fluctuations of the background. The background control will control for example for variations of light intensity and fluctuations of the fluorophore intensity. But what about errors in the cell segmentation? Or movement of the cells in 3D, which could be relevant because the collected light might be dependent on the distance from the surface? Is cell autofluorescence relevant at all? I am aware that accurately estimating the experimental error is exceptionally difficult, and I am also not entirely sure what would be the perfect control (if it even exists). Nevertheless, I think more potential sources of error should be addressed before the measured noise can be confidently attributed to biological sources. Maybe the authors could measure objects with constant volume over time, for example vesicles? As long as the segmented area contains the complete cell, the measured volume should not change if the area is increased. Is this the case?

We are grateful to the reviewer for all these useful suggestions. We performed all these controls on the sources of noise, and we discuss them in the revised manuscript.

2.) I am particularly puzzled by the fact that even at the timescale of the frame rate, fluctuations seem not to be correlated between 2 consecutive time points (Fig. 5-S2b). This seems plausible for (some) sources of experimental error. Maybe an experiment with fast time resolution would reveal the timescale over which the fluctuations persist - which could then give us a hint about the source?

We performed this analysis, finding an autocorrelation time of a few minutes, and we report our results below:

In the main text and in the new Figure 5 – Supplement 3, we report the results of newly performed 20 sec timelapse experiments over one hour to investigate the timescale of volume fluctuations. The autocvariance function analysis on the detrended curves shows that fluctuations decay over a few minutes (Figure 5 – Supplement 3a-c), a timescale that matches the analysis of the 10 min timelapse experiments.

Copy of Figure 5 – Supplement 3: Autocovariance analysis shows that the timescale of volume fluctuation is around 760 seconds. a) Cells measured every 20 sec (n=177) and linearly detrended reach a covariance of 0 at a lag of 760 sec. b) As a control, the background fluctuations are not autocorrelated (20 sec, n=92), providing further evidence that cell volume fluctuations likely have biological origin. c) The autocovariance analysis for cells measured every 10 min confirms that fluctuations covary for a lag of 10-20 min.

3.) The authors use automated smoothing of the measurement and removed outliers based on an IQR-criteria. While this seems reasonable if the aim is to get a robust measurement of the average behavior, I find it questionable with respect to the noise measurements. Since no minimum time scale has been associated with the fluctuations interpreted as biological in origin, what is the justification of removing 'outliers', i.e. the feature that the authors are actually interested in? Why would the largest fluctuations be of technical origin, and the smaller fluctuations exclusively biological?

The IQR-criteria is designed to remove only rare and obvious outliers (i.e. a jump in volume of more than 15% in 1 frame -10 minutes- which arguably cannot happen biologically). Fluctuations of smaller range are kept (see examples below). We looked back at the raw data and calculated that the IQR filtering removes a total of 337 measurement points out of 99935 initial points (0.03% of the points).

Figure D: Three examples of single cell trajectories with raw volume measurement (red dots) and points removed with the IQR filtering (blue dots). The IQR criteria is very stringent and removes only the very large ‘bumps’ in cell volume measured (2 left plots) while it keeps fluctuations of smaller amplitude (right plot).

4.) If I understood correctly, each volume trajectory spans one complete cell cycle. If this is the case, does Fig. 1e imply that many cell cycles take less than 2-3 hours? Is this really the case, and if so, what are the implications for some of the interpretations (especially the early cell cycle part)?

In this study, we performed experiments on a time scale comparable to the cell cycle time (~ 24hours) and recorded single-cell volume trajectories. Since the cells are not synchronized, we have very few complete cell cycles (~ 100, Fig. 1f). Fig. 1e shows the distribution of the duration of all individual curves, regardless of the fraction of the cell cycle they span, hence the very short duration for some cells.

Reviewer #2:

In this paper, the authors use a volume exclusion-based measurements to quantify single cell trajectories of volume increase in HeLa cells. The study represents one of the most careful measurements on volume regulation in animal cells and presents evidence for feedback mechanisms that slow the growth of larger cells. This is an important demonstration of cell autonomous volume regulation.

While the subject matter of the present study is important, the insights provided are significantly limited because the authors did not place their findings in the context of previous literature. The authors present what seems to be remarkably accurate single cell growth trajectories. In animal cells, a joint dependency of growth rate on cell size and cell cycle stage has been previously reported (see Elife 2018 PMID: 29889021 and Science 2009 PMID: 19589995). In Ginzberg et al, it is reported "Our data revealed that, twice during the cell cycle, growth rates are selectively increased in small cells and reduced in large cells". Nonetheless, these previous studies do not negate the novelty in Cadart et al. While both Cadart and Ginzberg investigate a dependency of cellular growth rate on cell size and cell cycle stage, the two studies are complimentary. This is because, while Ginzberg characterise the growth in cell mass, Cadart characterise the growth in cell volume. The authors should compare the findings from these previous studies with their own and draw conclusions from the similarities and differences. Are the cell cycle stage dependent growth rate similar or different when cell size is quantified as mass or volume? Does the faster growth of smaller cells (the negative correlation of growth rate and cell size) occur in different cell cycle stages when growth is quantified by volume as compared to mass?

We are grateful to the reviewer for their appreciation of the value of our study. Following their remarks, we have extended our Discussion section to incorporate a more careful discussion of these findings. We believe that the main contribution of our study is finding evidence of phase- dependent regulation of growth rate and identifying an additive noise on volume steps, this noise has constant amplitude, hence fluctuations of specific growth rate decrease with volume, but specific growth rate (in the bulk of the cell cycle) does not decrease.

Author Response:

Reviewer #1 (Public Review):

In this manuscript, the authors leverage novel computational tools to detect, classify and extract information underlying sharp-wave ripples, and synchronous events related to memory. They validate the applicability of their method to several datasets and compare it with a filtering method. In summary, they found that their convolutional neural network detection captures more events than the commonly used filter method. This particular capability of capturing additional events which traditional methods don't detect is very powerful and could open important new avenues worth further investigation. The manuscript in general will be very useful for the community as it will increase the attention towards new tools that can be used to solve ongoing questions in hippocampal physiology.

We thank the reviewer for the constructive comments and appreciation of the work.

Additional minor points that could improve the interpretation of this work are listed below:

• Spectral methods could also be used to capture the variability of events if used properly or run several times through a dataset. I think adjusting the statements where the authors compare CNN with traditional filter detections could be useful as it can be misleading to state otherwise.

We thank the reviewer for this suggestion. We would like to emphasize that we do not advocate at all for disusing filters. We feel that a combination of methods is required to improve our understanding of the complex electrophysiological processes underlying SWR. We have adjusted the text as suggested. In particular, a) we removed the misleading sentence from the abstract, and instead declared the need for new automatic detection strategies; b) we edited the introduction similarly, and clarified the need for improved online applications.

• The authors show that their novel method is able to detect "physiological relevant processes" but no further analysis is provided to show that this is indeed the case. I suggest adjusting the statement to "the method is able to detect new processes (or events)".

We have corrected text as suggested. In particular, we declare that “The new method, in combination with community tagging efforts and optimized filter, could potentially facilitate discovery and interpretation of the complex neurophysiological processes underlying SWR.” (page 12).

• In Fig.1 the authors show how they tune the parameters that work best for their CNN method and from there they compare it with a filter method. In order to offer a more fair comparison analogous tuning of the filter parameters should be tested alongside to show that filters can also be tuned to improve the detection of "ground truth" data.

Thank you for this comment. As explained before, see below the results of the parameter study for the filter in the very same sessions used for training the CNN. The parameters chosen (100- 300Hz band, order 2) provided maximal performance in the test set. Therefore, both methods are similarly optimized along training. This is now included (page 4): “In order to compare CNN performance against spectral methods, we implemented a Butterworth filter, which parameters were optimized using the same training set (Fig.1-figure supplement 1D).”

• Showing a manual score of the performance of their CNN method detection with false positive and false negative flags (and plots) would be clarifying in order to get an idea of the type of events that the method is able to detect and fails to detect.

We have added information of the categories of False Positives for both the CNN and the filter in the new Fig.4F. We have also prepared an executable figure to show examples and to facilitate understanding how the CNN works. See new Fig.5 and executable notebook https://colab.research.google.com/github/PridaLab/cnn-ripple-executable-figure/blob/main/cnn-ripple-false-positive-examples.ipynb

• In fig 2E the authors show the differences between CNN with different precision and the filter method, while the performance is better the trends are extremely similar and the numbers are very close for all comparisons (except for the recall where the filter clearly performs worse than CNN).

This refers to the external dataset (Grosmark and Buzsaki 2016), which is now in the new Fig.3E. To address this point and to improve statistical report, we have added more data resulting in 5 sessions from 2 rats. Data confirm better performance of CNN model versus the filter. The purpose of this figure is to show the effect of the definition of the ground truth on the performance by different methods, and also the proper performance of the CNN on external datasets without retraining. Please, note that in Grosmark and Buzsaki, SWR detection was conditioned on the

coincidence of both population synchrony and LFP definition thus providing a “partial ground truth” (i.e. SWR without population firing were not annotated in the dataset).

• The authors acknowledge that various forms of SWRs not consistent with their common definition could be captured by their method. But theoretically, it could also be the case that, due to the spectral continuum of the LFP signals, noisy features of the LFP could also be passed as "relevant events"? Discussing this point in the manuscript could help with the context of where the method might be applied in the future.

As suggested, we have mentioned this point in the revised version. In particular: “While we cannot discard noisy detection from a continuum of LFP activity, our categorization suggest they may reflect processes underlying buildup of population events (de la Prida et al., 2006). In addition, the ability of CA3 inputs to bring about gamma oscillations and multi-unit firing associated with sharp-waves is already recognized (Sullivan et al., 2011), and variability of the ripple power can be related with different cortical subnetworks (Abadchi et al., 2020; Ramirez- Villegas et al., 2015). Since the power spectral level operationally defines the detection of SWR, part of this microcircuit intrinsic variability may be escaping analysis when using spectral filters” (page 16).

• In fig. 5 the authors claim that there are striking differences in firing rate and timings of pyramidal cells when comparing events detected in different layers (compare to SP layer). This is not very clear from the figure as the plots 5G and 5H show that the main differences are when compare with SO and SLM.

We apologize for generating confusion. We meant that the analysis was performed by comparing properties of SWR detected at SO, SR and SLM using z- values scored by SWR detected at SP only). We clarified this point in the revised version: “We found larger sinks and sources for SWR that can be detected at SLM and SR versus those detected at SO (Fig.7G; z-scored by mean values of SWR detected at SP only).” (page 14).

• Could the above differences be related to the fact that the performance of the CNN could have different percentages of false-positive when applied to different layers?

The rate of FP is similar/different across layers: 0.52 ± 0.21 for SO, 0.50 ± 0.21 for SR and 0.46 ± 0.19 for SLM. This is now mentioned in the text: “No difference in the rate of False Positives between SO (0.52 ± 0.21), SR (0.50 ± 0.21) and SLM (0.46 ± 0.19) can account for this effect.” (page 12)

Alternatively, could the variability be related to the occurrence (and detection) of similar events in neighboring spectral bands (i.e., gamma events)? Discussion of this point in the manuscript would be helpful for the readers.

We have discussed this point: “While we cannot discard noisy detection from a continuum of LFP activity, our categorization suggest they may reflect processes underlying buildup of population events (de la Prida et al., 2006). In addition, the ability of CA3 inputs to bring about gamma oscillations and multi-unit firing associated with sharp-waves is already recognized (Sullivan et al., 2011), and variability of the ripple power can be related with different cortical subnetworks (Abadchi et al., 2020; Ramirez-Villegas et al., 2015).” (Page 16)

Overall, I think the method is interesting and could be very useful to detect more nuance within hippocampal LFPs and offer new insights into the underlying mechanisms of hippocampal firing and how they organize in various forms of network events related to memory.

We thank the reviewer for constructive comments and appreciation of the value of our work.

Reviewer #2 (Public Review):

Navas-Olive et al. provide a new computational approach that implements convolutional neural networks (CNNs) for detecting and characterizing hippocampal sharp-wave ripples (SWRs). SWRs have been identified as important neural signatures of memory consolidation and retrieval, and there is therefore interest in developing new computational approaches to identify and characterize them. The authors demonstrate that their network model is able to learn to identify SWRs by showing that, following the network training phase, performance on test data is good. Performance of the network varied by the human expert whose tagging was used to train it, but when experts' tags were combined, performance of the network improved, showing it benefits from multiple input. When the network trained on one dataset is applied to data from different experimental conditions, performance was substantially lower, though the authors suggest that this reflected erroneous annotation of the data, and once corrected performance improved. The authors go on to analyze the LFP patterns that nodes in the network develop preferences for and compare the network's performance on SWRs and non-SWRs, both providing insight and validation about the network's function. Finally, the authors apply the model to dense Neuropixels data and confirmed that SWR detection was best in the CA1 cell layer but could also be detected at more distant locations.

The key strengths of the manuscript lay in a convincing demonstration that a computational model that does not explicitly look for oscillations in specific frequency bands can nevertheless learn to detect them from tagged examples. This provides insight into the capabilities and applications of convolutional neural networks. The manuscript is generally clearly written and the analyses appear to have been carefully done.

We thank the reviewer for the summary and for highlighting the strengths of our work.

While the work is informative about the capabilities of CNNs, the potential of its application for neuroscience research is considerably less convincing. As the authors state in the introduction, there are two potential key benefits that their model could provide (for neuroscience research): 1. improved detection of SWRs and 2. providing additional insight into the nature of SWRs, relative to existing approaches. To this end, the authors compare the performance of the CNN to that of a Butterworth filter. However, there are a number of major issues that limit the support for the authors' claims:

Please, see below the answers to specific questions, which we hope clarify the validity of our approach

• Putting aside the question of whether the comparison between the CNN and the filter is fair (see below), it is unclear if even as is, the performance of the CNN is better than a simple filter. The authors argue for this based on the data in Fig. 1F-I. However, the main result appears to be that the CNN is less sensitive to changes in the threshold, not that it does better at reasonable thresholds.

This comment now refers to the new Fig.2A (offline detection) and Fig.2C,D (online detection). Starting from offline detection, yes, the CNN is less sensitive than the filter and that has major consequences both offline and online. For the filter to reach it best performance, the threshold has to be tuned which is a time-consuming process. Importantly, this is only doable when you know the ground truth. In practical terms, most lab run a semi-automatic detection approach where they first detect events and then they are manually validated. The fact that the filter is more sensible to thresholds makes this process very tedious. Instead, the CNN is more stable.

In trying to be fair, we also tested the performance of the CNN and the filter at their best performance (i.e. looking for the threshold f¡providing the best matching with the ground truth). This is shown at Fig.3A. There are no differences between methods indicating the CNN meet the gold standard provided the filter is optimized. Note again this is only possible if you know the ground truth because optimization is based in looking for the best threshold per session.

Importantly, both methods reach their best performance at the expert’s limit (gray band in Fig.3A,B). They cannot be better than the individual ground truth. This is why we advocate for community tagging collaborations to consolidate sharp-wave ripple definitions.

Moreover, the mean performance of the filter across thresholds appears dramatically dampened by its performance on particularly poor thresholds (Fig. F, I, weak traces). How realistic these poorly tested thresholds are is unclear. The single direct statistical test of difference in performance is presented in Fig. 1H but it is unclear if there is a real difference there as graphically it appears that animals and sessions from those animals were treated as independent samples (and comparing only animal averages or only sessions clearly do not show a significant difference).

Please, note this refers to online detection. We are not sure to understand the comment on whether the thresholds are realistic. To clarify, we detect SWR online using thresholds we similarly optimize for the filter and the CNN over the course of the experiment. This is reported in Fig.2C as both, per session and per animals, reaching statistical differences (we added more experiments to increase statistical power). Since, online defined thresholds may still not been the best, we then annotated these data and run an additional posthoc offline optimization analysis which is presented in Fig.2D. We hope this is now more clear in the revised version.

Finally, the authors show in Fig. 2A that for the best threshold the CNN does not do better than the filter. Together, these results suggest that the CNN does not generally outperform the filter in detecting SWRs, but only that it is less sensitive to usage of extreme thresholds.

We hope this is now clarified. See our response to your first bullet point

Indeed, I am not convinced that a non-spectral method could even theoretically do better than a spectral method to detect events that are defined by their spectrum, assuming all other aspects are optimized (such as combining data from different channels and threshold setting)

As can be seen in the responses to the editor synthesis, we have optimized the filter parameter similarly (new Fig.1-supp-1D) and there is no improvement by using more channels (see below). In any case, we would like to emphasize that we do not advocate at all for disusing filters. We feel that a combination of methods is required to improve our understanding of the complex electrophysiological processes underlying SWR.

• The CNN network is trained on data from 8 channels but it appears that the compared filter is run on a single channel only. This is explicitly stated for the online SWR detection and presumably, that is the case for the offline as well. This unfair comparison raises the possibility that whatever improved performance the CNN may have may be due to considerably richer input and not due to the CNN model itself. The authors state that a filter on the data from a single channel is the standard, but many studies use various "consensus" heuristics, e.g. in which elevated ripple power is required to be detected on multiple channels simultaneously, which considerably improves detection reliability. Even if this weren't the case, because the CNN learns how to weight each channel, to argue that better performance is due to the nature of the CNN it must be compared to an algorithm that similarly learns to optimize these weights on filtered data across the same number of channels. It is very likely that if this were done, the filter approach would outperform the CNN as its performance with a single channel is comparable.

We appreciate this comment. Using one channel to detect SWR is very common for offline detection followed by manual curation. In some cases, a second channel is used either to veto spurious detections (using a non-ripple channel) or to confirm detection (using a second ripple channel and/or a sharp-wave) (Fernandez-Ruiz et al., 2019). Many others use detection of population firing together with the filter to identify replay (such as in Grosmark and Buzsaki 2019, where ripples were conditioned on the coincidence of both population firing and LFP detected ripples). To address this comment, we compared performance using different combinations of channels, from the standard detection at the SP layer (pyr) up to 4 and 8 channels around SP using the consensus heuristics. As can be seen filter performance is consistent across configurations and using 8 channels is not improving detection. We clarify this in the revised version: ”We found no effect of the number of channels used for the filter (1, 4 and 8 channels), and chose that with the higher ripple power” (see caption of Fig.1-supp-1D).

• Related to the point above, for the proposed CNN model to be a useful tool in the neuroscience field it needs to be amenable to the kind of data and computational resources that are common in the field. As the network requires 8 channels situated in close proximity, the network would not be relevant for numerous studies that use fewer or spaced channels. Further, the filter approach does not require training and it is unclear how generalizable the current CNN model is without additional network training (see below). Together, these points raise the concern that even if the CNN performance is better than a filter approach, it would not be usable by a wide audience.

Thank you for this comment. To handle with different input channel configurations, we have developed an interpolation approach, which transform any data into 8-channel inputs. We are currently applying the CNN without re-training to data from several labs using different electrode number and configurations, including tetrodes, linear silicon probes and wires. Results confirm performance of the CNN. Since we cannot disclose these third-party data here, we have looked for a new dataset from our own lab to illustrate the case. See below results from 16ch silicon probes (100 um inter-electrode separation), where the CNN performed better than the filter (F1: p=0.0169; Precision, p=0.0110; 7 sessions, from 3 mice). We found that the performance of the CNN depends on the laminar LFP profile, as Neuropixels data illustrate.

• A key point is whether the CNN generalizes well across new datasets as the authors suggest. When the model trained on mouse data was applied to rat data from Grosmark and Buzsaki, 2016, precision was low. The authors state that "Hence, we evaluated all False Positive predictions and found that many of them were actually unannotated SWR (839 events), meaning that precision was actually higher". How were these events judged as SWRs? Was the test data reannotated?

We apologize for not explaining this better in the original version. We choose Grosmark and Buzsaki 2016 because it provides an “incomplete ground truth”, since (citing their Methods) “Ripple events were conditioned on the coincidence of both population synchrony events, and LFP detected ripples”. This means there are LFP ripples not included in their GT. This dataset provides a very good example of how the experimental goal (examining replay and thus relying in population firing plus LFP definitions) may limit the ground truth.

Please, note we use the external dataset for validation purposes only. The CNN model was applied without retraining, so it also helps to exemplify generalization. Consistent with a partial ground truth, the CNN and the filter recalled most of the annotated events, but precision was low. By manually validating False Positive detections, we re-annotated the external dataset and both the CNN and the filter increased precision.

To make the case clearer, we now include more sessions to increase the data size and test for statistical effects (Fig.3E). We also changed the example to show more cases of re-annotated events (Fig.3D). We have clarified the text: “In that work, SWR detection was conditioned on the coincidence of both population synchrony and LFP definition, thus providing a “partial ground truth” (i.e. SWR without population firing were not annotated in the dataset).” (see page 7).

• The argument that the network improves with data from multiple experts while the filter does not requires further support. While Fig. 1B shows that the CNN improves performance when the experts' data is combined and the filter doesn't, the final performance on the consolidated data does not appear better in the CNN. This suggests that performance of the CNN when trained on data from single experts was lower to start with.

This comment refers to the new Fig.3B. We apologize for not have had included a between- method comparison in the original version. To address this, we now include a one-way ANOVA analysis for the effect of the type of the ground truth on each method, and an independent one- way ANOVA for the effect of the method in the consolidated ground truth. To increase statistical power we have added more data. We also detected some mistake with duplicated data in the original figure, which was corrected. Importantly, the rationale behind experts’ consolidated data is that there is about 70% consistency between experts and so many SWR remain not annotated in the individual ground truths. These are typically some ambiguous events, which may generate discussion between experts, such as sharp-wave with population firing and few ripple cycles. Since the CNN is better in detecting them, this is the reason supporting they improve performance when data from multiple experts are integrated.

Further, regardless of the point in the bullet point above, the data in Fig. 1E does not convincingly show that the CNN improves while the filter doesn't as there are only 3 data points per comparison and no effect on F1.

Fig.1E shows an example, so we guess the reviewer refers to the new Fig.2C, which show data on online operation, where we originally reported the analysis per session and per animal separately with only 3 mice. We have run more experiments to increase the data size and test for statistical effects (8 sessions, 5 mice; per sessions p=0.0047; per mice p=0.033; t-test). This is now corrected in the text and Fig.1C, caption. Please, note that a posthoc offline evaluation of these online sessions confirmed better performance of the CNN versus the filter, for all normalized thresholds (Fig.2D).

• Apart from the points above regarding the ability of the network to detect SWRs, the insight into the nature of SWRs that the authors suggest can be achieved with CNNs is limited. For example, the data in Fig. 3 is a nice analysis of what the components of the CNN learn to identify, but the claim that "some predictions not consistent with the current definition of SWR may identify different forms of population firing and oscillatory activities associated to sharp-waves" is not thoroughly supported. The data in Fig. 4 is convincing in showing that the network better identifies SWRs than non-SWRs, but again the insight is about the network rather than about SWRs.

In the revised version, have now include validation of all false positives detected by the CNN and the filter (Fig.4F). To facilitate the reader examining examples of True Positive and False Positive detection we also include a new figure (Fig.5), which comes with the executable code (see page 9). We also include comparisons of the features of TP events detected by both methods (Fig.2B), where is shown that SWR events detected by the CNN exhibited features more similar to those of the ground truth (GT), than those detected by the filter. We feel the entire manuscript provides support to these claims.

Finally, the application of the model on Neuropixels data also nicely demonstrates the applicability of the model on this kind of data but does not provide new insight regarding SWRs.

We respectfully disagree. Please, note that application to ultra-dense Neuropixels not only apply the model to an entirely new dataset without retraining, but it shows that some SWR with larger sinks and sources can be actually detected at input layers (SO, SR and SLM). Importantly, those events result in different firing dynamics providing mechanistic support for heterogeneous behavior underlying, for instance, replay.

In summary, the authors have constructed an elegant new computational tool and convincingly shown its validity in detecting SWRs and applicability to different kinds of data. Unfortunately, I am not convinced that the model convincingly achieves either of its stated goals: exceeding the performance of SWR detection or providing new insights about SWRs as compared to considerably simpler and more accessible current methods.

We thank you again for your constructive comments. We hope you are now convinced on the value of the new method in light to the new added data.

Author Response:

Reviewer #1:

The authors found a switch between "retrospective", sensory recruitment-like representations in visual regions when a motor response could not be planned in advance, and "prospective" action-like representations in motor regions when a specific button response could be anticipated. The use of classifiers trained on multiple tasks - an independent spatial working memory task, spatial localizer, and a button-pressing task - to decode working memory representations makes this a strong study with straightforward interpretations well-supported by the data. These analyses provide a convincing demonstration that not only are different regions involved when a retrospective code is required (or alternatively when a prospective code can be used), but the retrospective representations resemble those evoked by perceptual input, and the prospective representations resemble those evoked by actual button presses.

I have just a couple of points that could be elaborated on:

1. While there is a clear transition from representations in visual cortex to representations in sensorimotor regions when a button press can be planned in advance, the visual cortex representations do not disappear completely (Figs 2B and C). Is the most plausible interpretation that participants just did not follow the cue 100% of the time, or that some degree of sensory recruitment is happening in visual cortex obligatorily (despite being unnecessary for the task) and leading to a more distributed, and potentially more robust code?

This is a very good point, and indeed could be considered surprising. While previous work suggests that sensory recruitment is not obligatory when an item can be dropped from memory entirely (e.g., Harrison & Tong, 2009; Lewis-Peacock et al., 2012; Sprague et al., 2014, Sprague et al., 2016; Lorenc et al., 2020), other work suggests that an item which might still be relevant later in a trial (i.e., a socalled “unattended memory item”) can still be decoded during the delay (see the re-analyses in Iamshchinina et al., 2021 from the original Christophel et al. 2018 paper). In short, we cannot exclude that in our paradigm there is some low-grade sensory recruitment happening in visual cortex, even when an action-oriented code can theoretically be used. This would be consistent with a more distributed code, which could potentially increase the overall robustness of working memory.

At the same time, as the reviewer points out, there is a possibility that on some fraction of trials, participants failed to perfectly encode the cue, or forgot the cue, which might mean they were using a sensory-like code even on some trials in the informative cue condition. This is a reasonable possibility given that we used a trial-by-trial interleaved design, where participants needed to pay close attention on each trial in order to know the current condition. Since we averaged decoding performance across all trials, the above-chance decoding accuracy could be driven by a small fraction of trials during which spatial strategies were used despite the informative nature of the preview disk.

Finally, another factor is the averaging of data across multiple TRs from the delay period. In Figure 2B, the decoding was performed using data that was averaged over several TRs around the middle of the delay period (8-12.8 seconds from trial start). This interval is early enough that the process of re-coding a representation from sensory to motor cortex may not be complete yet, so this might be an explanation for the relatively high decoding accuracy seen in the informative condition in Figure 2B. Indeed, the time-resolved analyses (Figure 2C, Figure 2 – figure supplement 1) show that the decoding accuracy for the informative condition continues to decline later in the delay period, though it does not go entirely to chance (with the possible exception of area V1).

Of course, our ability to decode spatial position despite participants having the option to use a pure action-oriented code may be due to a combination of all of the above: some amount of low-grade obligatory sensory recruitment, as well as occasional trials with higher-precision spatial memory due to a missed cue. We have added a paragraph to the discussion to now acknowledge these possibilities.

Finally, although it is conceptually important to consider the reasons why decoding in the uninformative condition did not drop entirely to chance, we also note that whether the decoding goes to chance in one condition is not critical to the main findings of our paper. The data show a robust difference between the spatial decoding accuracy in visual cortex between the two conditions, which indicates that the relative amount of information in visual cortex was modulated by the task condition, regardless of what the absolute information content was in each condition.

1. To what extent might the prospective code reflect an actual finger movement (even just increased pressure on the button to be pressed) in advance of the button press? For instance, it could be the case that the participant with extremely high button press-trained decoding performance in 4B, especially, was using such a strategy. I know that participants were instructed not to make overt button presses in advance, but I think it would be helpful to elaborate a bit on the evidence that these action-related representations are truly "working memory" representations.

This is a good point, and we acknowledge the possibility of some amount of preparatory motor activity during the delay period on trials in the informative condition. However, we still interpret the delayperiod representations during the informative condition as a signature of working memory, for several reasons.

First, the participants were explicitly instructed to withhold overt finger movements until the final probe disk was shown. We monitored participants closely during their task training phase, which took place outside the scanner, for early button presses, and ensured that they understood and followed the directive to withhold a button press until the correct time. We also confirmed that participants were not engaging in any noticeable motor rehearsal behaviors, such as tapping their fingers just above the buttons. During the scans, we also monitored participants using a video feed that was positioned in a way that allowed us to see their hands on the response box and confirmed that participants were not making any overt finger movements during the delay period. Additionally, most of our participants were relatively experienced, having participated in at least one other fMRI study with our group in the past, and therefore we expect them to have followed the task instructions accurately.

The distribution of response times for trials in the informative condition also provides some evidence against the idea that participants were already making a button press ahead of the response window. The earliest presses occurred around 250 ms (see below figure, left panel). This response time is consistent with the typical range of human choice response times observed experimentally (e.g. Luce, 1991), suggesting that participants did not execute a physical response in advance of the probe disk appearance, but waited until the response disk stimulus appeared to begin motor response execution.

Finally, even if we assume that some amount of low-grade motor preparatory activity was occurring, this is still broadly consistent with the way that working memory has been defined in past literature. Past work has distinguished between retrospective and prospective working memory, with retrospective memory being similar in format to previously encountered sensory stimuli, and prospective memory being more closely aligned with upcoming events or actions (Funahashi, Chafee, & Goldman-Rakic, 1993; Rainer, Rao & D’Esposito, 1999; Curtis, Rao, & D’Esposito, 2004; Rahmati et al., 2018; Nobre & Stokes, 2019). Indeed, the transformation of a memory representation from a retrospective code to prospective memory code is often associated with increased engagement of circuits directly related to motor control (Schneider, Barth, & Wascher, 2017; Myers, Stokes, & Nobre, 2017). According to this framework, covert motor preparation could be considered a representation at the extreme end of the prospective memory continuum. Also consistent with this idea, past work has demonstrated that the selection and manipulation of items in working memory can be accompanied by systematic eye movements biased to the locations at which memoranda were previously presented (Spivey & Geng, 2001; Ferreira et al., 2008; van Ede et al., 2019b; van Ede et al. 2020). These physical eye movements may indeed play a functional role in the retrieval of items from memory (Ferreira et al., 2008; van Ede et al., 2019b). These findings suggest that working memory is tightly linked with both the planning and execution of motor actions, and that the mnemonic representations in our task, even if they include some degree of covert motor preparatory activity, are within the realm of representations that can be defined as working memory.

We have now included a discussion of this issue in the text of our manuscript.

Reviewer #2:

Henderson, Rademaker and Serences use fMRI to arbitrate between theories of visual working memory proposing fixed x flexible loci for maintaining information. By comparing activation patterns in tasks with predictable x unpredictable motor responses, they find different extents of information retrieval in sensory- x motor-related areas, thus arguing that the amount/format of retrospective sensory-related x prospective motor-related information maintained depends on what is strategically beneficial for task performance.

I share the importance of this fundamental question and the enthusiasm for the conclusions, and I applaud the advanced methodology. I did, however, struggle with some aspects of the experimental design and (therefore) the logic of interpretation. I hope these are easily addressable.

Conceptual points:

1. The main informative x non-informative conditions differ more than just in the knowledge about the response. In the informative case, participants could select both the relevant sensory information (light, dark shade) and the corresponding response. In essence, their task was done, and they just needed to wait for a later go signal - the second disk. (The activity in the delay could be considered to be one of purely motor preparation or of holding a decision/response.) In the uninformative condition, neither was sensory information at the spatial location relevant and nor could the response be predicted. Participants had, instead, to hold on to the spatial location to apply it to the second disk. These conditions are more different than the authors propose and therefore it is not straightforward to interpret findings in the framework set up by the authors. A clear demonstration for the question posed would require participants to hold the same working-memory content for different purposes, but here the content that needs to be held differs vastly between conditions. The authors may argue this is, nevertheless, the essence of their point, but this is a weak strawman to combat.

It is true that the conditions in our task differ in several respects, including the content of the representation that must be stored. The uninformative condition trials required the participant to maintain a high-precision, sensory-like spatial representation of the target stimulus, without the ability to plan a motor response or re-code the representation into a coarser format. In contrast, the informative condition trials allowed the participant to re-code their representation into a more actionoriented format than the representation needed for the uninformative condition trials, and the code is also binary (right or left) rather than continuous.

However, we do not think these differences present an issue for the interpretation of our study. The primary goal of our study was to demonstrate that the brain regions and representational formats utilized for working memory storage may differ depending on parameters of the task, rather than having fixed loci or a single underlying neural mechanism. To achieve this, we intentionally created conditions that are meant to sit at fairly extreme ends of the continuum of working memory task paradigms employed in past work. Our uninformative condition is similar to past studies of spatial working memory with human participants that encourage high-precision, sensory-like codes (i.e., Bays & Husain, 2008; Sprague et al., 2014; Sprague et al., 2016; Rahmati et al., 2018) and our informative condition is more similar to classic delayed-saccade task studies in non-human primates, which often allowed explicit motor planning (Funahashi et al., 1989; Goldman-Rakic, 1995). By having the same participants perform these distinct task conditions on interleaved trials, we can better understand the relationship between these task paradigms and how they influence the mechanisms of working memory.

Importantly, it is not trivial or guaranteed that we should have found a difference in neural representations across our task conditions. In particular, an alternative perspective presented in past work is that the memory representations detected in early visual cortex in various tasks are actually not essential to mnemonic storage (Leavitt, Mendoza-Halliday, & Martinez-Trujillo, 2017; Xu, 2020). On this view, if visual cortex representations are not functionally relevant for the task, one might have predicted that our spatial decoding accuracy in early visual areas would have been similar across conditions, with visual cortex engaged in an obligatory manner regardless of the exact format of the representation required. Instead, we found a dramatic difference in decoding accuracy across our task conditions. This finding underscores the functional importance of early visual cortex in working memory maintenance, because its engagement appears to be dependent on the format of the representation required for the current task.

Relatedly, some past work has also suggested that in the context of an oculomotor delayed response task, the maintenance of action-oriented motor codes can be associated with topographically specific patterns of activation in early visual cortex which resemble those recorded during sensory-like spatial working memory maintenance (Saber et al., 2015; Rahmati et al., 2018). This is true for both prosaccade trials, in which saccade goals are linked to past sensory inputs, and anti-saccade trials, in which motor plans are dissociated from past sensory inputs. These findings indicate that even for task conditions which on the surface would appear to require very different cognitive strategies, there can, at least in some contexts, be a substantial degree of overlap between the neural mechanisms supporting sensory-like and action-oriented working memory. This again highlights the novelty of our findings, in which we demonstrate a robust dissociation between the brain areas and neural coding format that support working memory maintenance for different task conditions, rather than overlapping mechanisms for all types of working memory.

Additionally, there are important respects in which the task conditions have similarities, rather than being entirely different. As pointed out by Reviewer #1, the decoding of spatial information in early visual cortex regions did not drop entirely to chance in the informative condition, even by the end of the delay period (Figure 2C, Figure 2 – figure supplement 1). As discussed above in our reply to R1, this finding may suggest that the neural code in the informative condition continues to rely on visual cortex activation to some extent, even when an action-oriented coding strategy is available. This possibility of a partially distributed code suggests that while the two conditions in our task appear different in terms of the optimal strategy associated with each one, in practice the neural mechanisms supporting the tasks may be somewhat overlapping (although the different mechanisms are differentially recruited based on task demands, which is our main point).

Another aspect of our results which suggests a degree of similarity between the task conditions is that the univariate delay period activation in early visual cortex (V1-hV4) was not significantly different between conditions (Figure 1 – figure supplement 1). Thus, it is not simply the case that the participants switched from relying purely on visual cortex to purely on motor cortex – the change in information content instead reflects a much more strategically graded change to the pattern of neural activation. This point is elaborated further in the response to point (2) below.

1. Given the nature of the manipulation and the fact that the nature of the upcoming trial (informative x uninformative) was cued, how can effects of anticipated difficulty, arousal, or other nuisance variables be discounted? Although pattern-based analyses suggest the effects are not purely related to general effects (authors argue this in the discussion, page 14), general variables can interact with specific aspects of information processing, leading to modulation of specific effects.

There are several aspects of our results which suggest that our results are not due to effects such as anticipated difficulty or general arousal. First, we designed our experiment using a randomly interleaved trial order, such that participants could not anticipate experimental condition on a trialby-trial basis. Participants only learned which condition each trial was in when the condition cue (color change at fixation; Figure 1A) appeared, which happened 1.5 seconds into the delay period. Thus, any potential effects of anticipated difficulty could not have influenced the initial encoding of the target stimulus, and would have had to take effect later in the trial. Second, as the reviewer pointed out, we did not observe any statistically significant modulation of the univariate delay period BOLD signal in early visual ROIs V1-hV4 between task conditions (Figure 1D, Figure 1 – figure supplement 1), which argues against the idea that there is a global modulation of early visual cortex induced by arousal or changes in difficulty.

Additionally, our results demonstrate a dissociation between univariate delay period activation in IPS and sensorimotor cortex ROIs as a function of task condition (Figure 1D, Figure 1 – figure supplement 1). In each IPS subregion (IPS0-IPS3), the average BOLD signal was significantly greater during the uninformative versus the informative condition at several timepoints in the delay period, while in S1, M1, and PMc, average signal was significantly greater for the informative than the uninformative condition at several timepoints. If a global change in mean arousal or anticipated difficulty were a main driving factor in our results, then we would have expected to see an increase in the univariate response throughout the brain for the more difficult task condition (i.e., the uninformative condition). Instead, we observed effects of task condition on univariate BOLD signal that were specific to particular ROIs. This indicates that modulations of neural activation in our task reflect a more finegrained change in neural processing, rather than a global change in arousal or anticipated difficulty.

Furthermore, to determine whether the changes in decoding accuracy in early visual cortex were specific to the memory representation or reflected a more general change in signal-to-noise ratio, we provide a new analysis assessing the possibility that processing of incoming sensory information differed between our two conditions. As mentioned above, initial sensory processing of the memory target stimulus was equated across conditions, since participants didn’t know the task condition until the cue was presented 1.5s into the trial. However, because the “preview disk” was presented after the cue, it is possible that the preview disk stimulus was processed differently as a function of task condition. If evidence for differential processing of the preview disk stimulus is present, this might suggest that non-mnemonic factors – such as arousal – might influence the observed differences in decoding accuracy because they should interact with the processing of all stimuli. However, a lack of evidence for differential processing of the preview disk would be consistent with a mnemonic source of differences between task conditions.

As shown in the new figure below (now Figure 2 – figure supplement 3), we used a linear decoder to measure the representation of the “preview disk” stimulus that was shown to participants early in the delay period, just after the condition cue (Figure 1A). This disk has a light and dark half separated by a linear boundary whose orientation can span a range of 0°-180°. To measure the representation of the disk’s orientation, we binned the data into four bins centered at 0°, 45°, 90°, and 135°, and trained two binary decoders to discriminate the bins that were 90° apart (an adapted version of the approach shown in Figure 2A; similar to Rademaker et al., 2019). Importantly, the orientation of this disk was random with respect to the memorized spatial location, allowing us to run this analysis independently from the spatial-position decoding in the main manuscript text.

We found that in both conditions, the orientation of the preview disk boundary could be decoded from early visual cortex (all p-values<0.001 for V1-hV4 in both conditions; evaluated using nonparametric statistics as described in Methods), with no significant difference between our two task conditions (all p-values>0.05 for condition difference in V1-hV4). This indicates that in both task conditions, the incoming sensory stimulus (“preview disk”) was represented with similar fidelity in early visual cortex. At the same time, and in the same regions, the representation of the remembered spatial stimulus was significantly stronger in the uninformative condition than the informative condition. Therefore, the difference between task conditions appears to be specific to the quality of the spatial memory representation itself, rather than a change in the overall signal-to-noise ratio of representations in early visual cortex. This suggests that the difference between task conditions in early visual cortex reflects a difference in the brain networks that support memory maintenance in the two conditions, rather than extra processing of the preview disk in one condition over the other, a more general effect of arousal, or anticipated difficulty.

This result is also relevant to the concerns raised by the reviewer in point (1) regarding the possibility that the selection of relevant sensory information (i.e., the light/dark side of the disk) was different between the two task conditions. Since the decoding accuracy for the preview disk orientation did not differ between task conditions, this argues against the idea that differential processing of the preview disk may have contributed to the difference in memory decoding accuracy that we observed.

1. I see what the authors mean by retrospective and prospective codes, but in a way all the codes are prospective. Even the sensory codes, when emphasized, are there to guide future discriminations or to add sensory granularity to responses, etc. Perhaps casting this in terms of sensory/perceptual x motor/action~ may be less problematic.

This is a good point, and we agree that in some sense all the memory codes could be considered prospective because in both conditions, the participant has some knowledge of the way that their memory will be probed in the future, even when they do not know their exact response yet. We have changed our language in the text to reflect the suggested terms “perceptual” and “action”, which will hopefully also make the difference between the conditions clearer to the reader.

1. In interpreting the elevated univariate activation in the parietal IPSO-3 area, the authors state "This pattern is consistent with the use of a retrospective spatial code in the uninformative condition and a prospective motor code in the informative condition". (page 6) (Given points 1 and 3 above) Instead, one could think of this as having to hold onto a different type of information (spatial location as opposed to shading) in uninformative condition, which is prospectively useful for making the necessary decision down the line.

It is true that a major difference between the two conditions was the type of information that the participants had to retain, with a sensory-like spatial representation being required for the uninformative condition, and a more action-oriented (i.e., left or right finger) representation being required for the informative condition. To clarify, the participant never had to explicitly hold onto the shading (light or dark gray side of the disk), since the shading was always linked to a particular finger, and this mapping was known in advance at the start of each task run (although we did change this mapping across task runs within each participant to counterbalance the mapping of light/dark and the left/right finger – one mapping used in the first scanner session, the other mapping used in the second scanning session). We have clarified this sentence and we have removed the use of the terms “retrospective” and “prospective” as suggested in the previous comment. The sentence now reads: “This pattern is consistent with the use of a spatial code in the uninformative condition and a motor code in the informative condition.”

Other points to consider:

1. Opening with the Baddeley and Hitch 1974 reference when defining working memory implicitly implies buying into that particular (multi-compartmental) model. Though Baddeley and Hitch popularised the term, the term was used earlier in more neutral ways or in different models. It may be useful to add a recent more neutral review reference too?

This is a nice suggestion. We have added a few more references to the beginning of the manuscript, which should together present a more neutral perspective (Atkinson & Shiffron, 1968; and Jonides, Lacey and Nee, 2005).

1. The body of literature showing attention-related selection/prioritisation in working memory linked to action preparation is also relevant to the current study. There's a nice review by Heuer, Ohl, Rolfs 2020 in Visual Cognition.

We thank the reviewer for pointing out this interesting body of work, which is indeed very relevant here. We have added a new paragraph to our discussion which includes a discussion of this paper and its relation to our work.

Author Response:

Reviewer #2:

Weaknesses of the Methods and Results:

1) In my view, the experiment does not allow to unambiguously disentangle self vs. other distinction (as mentioned in the abstract "..we investigated how affect sharing and self-other distinction interact.."). For example, genuine vs. pretended pain could be distinguished from the participants own experience in a comparable way. The higher rating of unpleasantness for genuine pain in others does not necessary mean that the participants cannot separate own from others experiences.

We thank the reviewer for raising this issue and for prompting us to further clarify and better state our research purpose. In terms of its original theoretical foundation and motivation, the current study aimed to investigate whether and how neural signatures underlying two essential components of empathy, namely affect sharing and self-other distinction, track individual responses to genuine vs. pretended pain. We agree though that our experimental design does not allow to disentangle unequivocally the precise aspects of self- and other-related processing in the two main conditions of interest (genuine pain or pretended pain). We thus modified any wording suggesting otherwise, so as to avoid further misunderstanding by readers.

Accordingly, we have provided a more elaborate theoretical clarification in the Abstract and Introduction about our particular interest in studying self-other distinction and its neural correlates in the right supramarginal gyrus (rSMG) during empathy. We also mention as a potential limitation that our design did not aim to explicitly quantify self-other distinction.

Action taken: In the manuscript, we have made the following changes:

1) We modified the sentence "[...] we investigated how affect sharing and self-other distinction interact [...]" to

“[...] we investigated how the brain network involved in affect sharing and self-other distinction underpinned [...] ” in the Abstract (P. 1).

Besides, we modified another sentence “[...] to investigate the hypothesized distinct interactions between affective response and self-other distinction [...]” to

“[...] to investigate the hypothesized brain patterns of affective responses and self-other distinction [...]” in the Introduction (P. 4).

2) We added sentences in the Discussion (P. 13): “An additional limitation was that our study design did not aim to explicitly quantify self-other distinction. Rather, in line with previous research and based on our theoretical framework and rationale, we inferred the engagement of this process from the experimental conditions and the associated behavioral and neural responses. We expect our findings to prompt and inform future research designed to quantify and experimentally disentangle self- and other-related processes more explicitly.”

2) The experimental design does not unambiguously allows to disentangle genuine vs pretended pain from other factors, such as the differences in pain expression, painful feeling in others and higher unpleasantness in these two conditions. I understand that the intensity pain expression, painful feeling in others and unpleasantness for others is inherently tied to genuine vs. pretended pain. But the author already saw that the instruction of "genuine vs. pretented" influenced the ratings of pain expression. Hence, this allows two interpretation of the results: either the influence from the anterior Insula on the rSMG is driven by higher perceived pain expression, painful feeling in others and unpleasantness or by the conditions of genuine vs. pretended pain. Or (more likely) by an interaction between these factors. It would, for example help to explore the association between the aIns-rSMG interaction pain expression ratings (or painful feeling in others or higher unpleasantness) in videos with genuine pain und pretended pain separately. The author should further discuss this point that different factors (pain expression, etc) contribute to the differences between genuine vs. pretended pain.

We thank the reviewer for the thoughtful consideration of different factors that might contribute to disentangle genuine pain vs. pretend pain. One thing we would like to address beforehand: to disentangle the specific contributors underlying the manipulation is not the main focus for the current study, as 1) our primary aim was to study the effects of the experimental manipulation as a whole; we thus used the three behavioral ratings mainly to collect additional information on and to interpret the expected effects of the manipulation, and 2) these factors (and their behavioral measures) are inherently (cor)related and hard to be disentangled precisely anyways, as mentioned by the reviewer and as shown by extensive previous research both by our and other groups.

Action taken: Nonetheless, in the revised manuscript, we have now:

1) discussed how different factors possibly interact and in this way contribute to the differences (in the modulatory effect) between genuine vs. pretended pain, in the Discussion (P. 11):

“We speculate that a dynamic interaction between sensory-driven and control processes is underlying the modulatory effect: when individuals realized after an initial sensory-driven response to the facial expression that it was not genuinely expressing pain, control and appraisal processes led to a reappraisal of the triggered emotional response, and thus a dampening of the unpleasantness.”

2) performed additional linear regression models and model comparison (see details in the response to comment #3) to investigate whether an interaction between behavioral measures could be a potential contributor to the modulatory effect of genuine pain and pretended pain; in short, the model without interactions is the winning model both for genuine pain and pretended pain.

We have now discussed this result (P. 11):

“Model comparison showed that the best model to explain the inhibitory effect with the behavioral ratings for both the genuine and pretended pain is the model without interactions between ratings. That is, if any behavioral rating contributed to the modulation of aIns to rSMG, the effect would be more likely coming from single ratings rather than their interactions. Specifically, we found [...]”

We thank the reviewer for this suggestion for further analysis.

We performed additional linear regression models (with and without interaction) and model comparison to explore whether any interaction between behavioral ratings heavily contributed to the modulatory effect. Results showed that the model without interaction was the most efficient model for both conditions.

We report the additional analyses as follows:

In the Methods section (P. 24-25): “Considering that interactions between behavioral ratings might contribute to the regression model, we tested five regression models (with and without interaction; see Supplementary Table 1) for both genuine pain and pretended pain. Results showed that for both genuine pain and pretend pain, the model without any interaction outperformed other models.”

Supplementary Table 1. Model comparison of linear regression models with three behavioral ratings (independent variables) and the inhibitory effect (dependent variable) for genuine pain and pretended pain. Smaller AIC/BIC indicates better model fit. Results showed that M1 (without interaction; highlighted with underlining) was the best fitting model for both genuine pain and pretended pain.

Accordingly, we now report the results of the winning model of the multiple regression analyses, instead of the original stepwise regression. These analyses found that only the rating of painful feelings in others was significant for genuine pain, while no significant effects whatsoever were found for pretended pain.

Action taken:

In the manuscript, we have made the following changes:

1) We modified “stepwise linear regression” to “multiple linear regression” in the Methods, Results, and Figure 3 legend (P. 24, P. 7, and P. 37)

2) We added the sentence “The results of the winning multiple regression model are reported in the Results section.” in the Methods (P. 25).

3) We added the results of the multiple regression analyses for genuine pain and pretended pain, in the Results section (P. 7-8): “For the genuine pain condition, we find that the modulatory effect was significantly related to the rating of painful feelings in others (t = 2.317, p = 0.026) but not related to the rating of either painful expressions in others (t = -1.492, p = 0.144) or unpleasantness in self (t = 0.058, p = 0.954). For the pretended pain condition, none of the ratings was significantly related to the modulatory effect (Figure 3D).”

4) We moved the results of the original stepwise regression analyses with behavioral ratings into the supplementary data (see Supplementary File 2):

“Results of the stepwise regression analyses on modulatory effects and behavioral ratings are shown below. Note that this analysis reflects our original analysis approach; prompted by a reviewer comment, we however changed the analysis plan and performed and reported the findings of multiple regression analyses in the main text. Importantly, the conclusions of the two analysis approaches are consistent.

To examine how the modulatory effects from the DCM were related to the behavioral ratings, we computed two stepwise linear regression models for each condition. The regression model was significant for the genuine pain condition (F model (1, 41) = 4.639, p = 0.037, R2 = 0.104), when painful feelings in others were added to the model and the other two ratings were excluded (B = 0.079, beta = 0.322, p = 0.037). However, the model was not significant for the pretended pain condition. The variance inflation factors (VIFs) for three ratings in both models were calculated to diagnose collinearity, showing no severe collinearity problem (all VIFs < 5; the smallest VIF =1.132 and the largest VIF = 4.387).”

3) The multiple regression analyses revealed an association between the unpleasantness for the participants and the aIns, when accounting for the painful expression and the pain experienced by the other. This, however, does not reveal the specificity of the aIns for encoding the unpleasantness for the participants. It might well be that variance is shared in the association between the aIns and pain expression and pain by the other and unpleasantness for the participants, but simply strongest for unpleasantness. Such ambiguity could be resolved by additional multiple regressions of 1) pain expression (controlling for pain by the other and unpleasantness for the participants) and 2) pain for the other (controlling for pain expression and unpleasantness for the participants).

We thank the reviewer for this comment. As an overall premise, please note that we would not want to claim that the aIns is specifically engaged in encoding affective activities without any engagement of other processes; instead, we are entirely aware that the aIns activation participates in a variety of affective and cognitive processes. Nonetheless, our original multiple regression models were performed as a second-level group analysis with all three ratings as independent variables. Results showed that only the rating of “unpleasantness in self” was significant, rather than all ratings that were universally influenced by domain-general factors.

As the reviewer suggested, we additionally performed five multiple regression analyses with all possible orders of three behavioral measures to test whether the order matters. In the end, we found consistent results across all six regression analyses, suggesting that the selective correlation of aIns and the rating of unpleasantness in self was robust.

Action taken: In the manuscript, we have:

1) Modified “specifically” to “selectively” in the Results (P. 6).

2) Added the content in the Methods (P. 22) “To test whether the order of entering ratings into the regression model influence the results, we performed five additional regression analyses with all possible orders of three ratings. The results were consistent across all six regression models, and we only showed the result for one regression (i.e., expression + feeling + unpleasantness) in the Results section.

3) Modified the sentence in the Results (P. 6) “We found significant clusters in bilateral aIns, visual cortex, and cerebellum (Figure 2B); notably, when statistically accounting for ratings of painful expressions in others and painful feelings in others, all three clusters were exclusively explained by the ratings of self-unpleasantness.” to

“We found significant clusters in bilateral aIns, visual cortex, and cerebellum that could be selectively explained by the ratings of self-unpleasantness and could not be explained by either the ratings of painful expressions in others or painful feelings in others (Figure 2B).”

4) Modified the sentence in the Discussion (P. 9) “[...] but the increased activation in aIns was also selectively correlated with ratings of self-oriented unpleasantness (i.e., after statistically accounting for painful expressions and painful feelings in others) [...]” to

“[...] but the increased activation in aIns was also selectively correlated with ratings of self- oriented unpleasantness and was not correlated with neither other-related painful expressions nor painful feelings in terms of the regression analysis [...]”

and added the sentence “[...] (otherwise the increased aIns activation should also be explained by other behavioral ratings in the sense of shared influence by domain-general effects).”

5) Modified the legend for Figure 3 (P. 37) “[...] revealed a positive correlation between the inhibitory effect and painful feelings in others (after accounting for the other two ratings) for genuine pain [...]” to

“[...] revealed a positive correlation between the inhibitory effect and painful feelings in others and not with other two ratings for genuine pain [...]”

4) Is the regression biased by the differences between conditions in the aIns in both fMRI signals and the ratings?

We thank the reviewer for this comment. The reason that we compared the differences between conditions was mainly aimed to control for potential effects of perceptual salience. This aim was consistent for both fMRI signals and behavioral ratings. Note that, as the aIns activation and all behavioral ratings were higher for genuine pain as opposed to pretended pain, the current result could not be explained by an inverse effect (i.e., higher aIns activation and higher ratings of unpleasantness in self for pretended pain). Therefore, we do not consider it is problematic to use differences between conditions when performing the multiple regression analysis.

Action taken:

1) We have more explicitly specified “differences between conditions for” three behavioral ratings as independent variables for the multiple regression model in the Methods (P. 22).

2) We added the sentence “The reason that we used the comparison between conditions for both brain signals and behavioral ratings was to control for potential effects of perceptual salience.” In the Methods (P. 22).

5) The inclusion of the rSMG into the DCM model is not straight forward for me. It could have been based on previous literature, but then the aMCC should have been added as well. Furthermore, while the implication of the rSMG in distinction of self vs. others is established, the actual process in this experiment cannot be revealed. The authors state that the rSMG is involved in action observation or imitating emotions (page 9, line 200).

We appreciate the reviewer’s comment that shows we seemed not to convey clearly why we have postulated a role of rSMG. We have now made our rationale more explicit and clear.

Action taken:

We have now:

1) Modified the clarification of rSMG in the Discussion (P. 10): “The inferior parietal lobule was shown to be generally engaged in selective attention, action observation and imitating emotions (Bach et al., 2010; Pokorny et al., 2015; Gola et al., 2017; Hawco et al., 2017). Importantly, a specific role in affective rather than cognitive self-other distinction has been consistently identified for rSMG (Silani et al., 2013; Steinbeis et al., 2015; Bukowski et al., 2020). [...]”

2) Added further clarification in the Discussion (P. 12) after the sentence “ [...] the correlation findings provide further evidence that the modulation of aIns to rSMG is implicated in encoding others’ emotional states,”

with “which serves as a functional foundation for self-other processing [...] This regulation cannot be totally attributed to domain-general processes, otherwise other ratings should have also explained this variation.”

Additionally, we agree re: aMCC, which we also predicted to play a role; but it was not the case at least in our data. In fact, we have already addressed this in the original version of the ms. (maintained on P. 7 of revised ms.): “Our original analysis plan was to include aMCC in the DCM analyses, but based on the fact that aMCC did not show as strong evidence (in terms of the multiple regression analysis) as the aIns of being involved in our task, we decided to use a more parsimonious DCM model without the aMCC.”

Whether Results support their conclusions:

The results support the distinction between the experimental conditions of genuine vs. pretended pain in the aIns and as a modulatory influence on the connectivity between the aIns and the rSMG. However, the authors aimed to test if genuine vs. pretended pain modulate regulatory influences from the aIns on the rSMG that are connected to self-other distinction (as proposed in the discussion page 8, line 170). Yet, any insights about self-other distinction are only inferred reversely, since there is no outcome that indicates how well participants distinguished between themselves and the other person. For example in the discussion the authors state that: " we thus propose that the higher rSMG engagement in genuine pain conditions reflects an increasing demand for self-other distinction imposed by the stronger shared negative affect experiences in this condition". This is not supported by the results. Furthermore, the title mentioned automated responses to pretended pain, which I could not understand, given the current results.

We thank the reviewer for this comment, which somewhat follows up on similar arguments made and replied to in comment #1 above. Indeed, we fully agree that our design did not allow us to quantify self-other distinction, but that we inferred its engagement based on a strong theoretical motivation and the replication of previous findings on rSMG involvement during self-other distinction. As outlined above (cf. #1), this limitation was added to the revised manuscript.

We also adjusted the way of reasoning for which we put the theoretical explanation ahead of the inference so that readers can better realize this statement is supported by stronger theoretical motivation in the Discussion (P. 10):

First “Theoretical models of empathy [...]” and then “Concerning the current finding, we thus propose that [...]”

We thank the reviewer for pointing out the potential ambiguity in the title. We agree it may be somewhat “imprecise”, and have revised the title accordingly (P. 1):

“Neural dynamics between anterior insular cortex and right supramarginal gyrus dissociate genuine affect sharing from perceptual saliency of pretended pain”.

Likely impact of the work on the field:

These results are expected to advance the field, since they allow to disentangle visual expressions of pain from genuine pain in others. Thereby, this work could resolves the question about neural processes that are specific to pain in others beyond other salient cues.

We thank the reviewer for this positive acclaim of our study.

Author Response

Reviewer #1 (Public Review):

This paper by Zhuang and colleagues seeks to answer an important clinical question by trying to come up with novel predictive biomarkers to predict high-risk T1 colorectal cancers that are at risk for nodal involvement. The current clinical features may both miss patients who underwent local therapy and who should have gone on to have surgery and patients for whom surgery was done based on risk features but perhaps unnecessarily. Using a training and validation set, they developed a protein-based classifier with an AUC of 0.825 based on mass spec analyses and proteomic analyses of patients with and without LN importantly linking biological rationale to the proteomic discoveries.

In the training cohort, they took 105 candidate proteins reduced to 55, and did a validation in the training cohort first and then in two validation cohorts (one of which was prospective). They also looked at a 9-protein classifier which also performed well and furthermore looked at IHC for clinical ease.

We appreciate the reviewers for the positive review and valuable comments. We have revised the manuscript according to the comments.

Reviewer #2 (Public Review):

The authors utilized a label-free LC-MS/MS analysis in formalin-fixed paraffin-embedded (FFPE) tumors from 143 LNM-negative and 78 LNM-positive patients with T1 CRC to identify protein biomarkers to determine LNM in T1 CRC.

The authors used a fair number of clinical samples for the proteomics investigation. The experimental design is reasonable, and the statistical methods used in this manuscript are solid.

The authors largely achieved their aims and the results supported their conclusion. The method used in this proteomic study can also be used for the proteomics analysis of other cancer types to identify diagnostic and prognostic biomarkers. In addition, the 9-marker panel has a potential clinical diagnosis practice in determining LNM in T1 CRC.

Nevertheless, the authors need to justify their standards in selecting the biomarkers. For example, a p-value cut-off of 0.1 is not a usual criterion in similar proteomic studies. In addition, an identification frequency of 30% in patients seems not preferable for biomarker identification. The authors also need to justify the definition of fold change in the three subtypes with Kruskal-Walli's test. The authors need to describe more details on how they identified the 13 proteins from a 55-protein database. In addition, what is the connection between the final 9 proteins and the 19 proteins? What is the criterion to select 5 proteins for IHC validation from the 9 proteins?

We appreciate the reviewers for the positive review and valuable comments. We have revised the manuscript according to the comments.

The criteria and details of our standards in selecting are as follows.

1) About p-value cut-off of 0.1:

The purpose of this step is to screen appropriate variables for subsequent machine learning, rather than comparing differences between groups. The p-value cut-off of 0.1 is also a reliable strategy for variable selection in proteomics research. For example, it has been used in studies to predict the response to tumor necrosis factor-α inhibitors in rheumatoid arthritis (PMID: 28650254); the research about circadian clock in mouse liver (PMID: 29674717); the proteomic biomarker discovery in atherosclerosis (PMID: 15496433); and the proteomics and transcriptomics analysis in bacillus subtilis (PMID: 19948795).

Based on reviewer’s suggestion, we used a cutoff of p-value 0.05 to screen for variables. In a training set of 70 lymph node-negative and 62 lymph node-positive cases, we identified 355 protein markers. We further incorporated these proteins into a lasso regression analysis and ultimately developed a lymph node metastasis prediction model consisting of 52 protein markers. We validated the model in VC1 and VC2, with AUC values of 1.000, 0.824, and 0.918 for the training set, VC1, and VC2, respectively, the predictive performance was slightly inferior to that of the model developed in this study (Figure 3- figure supplement 1C).

2) About identification frequency of 30%:

The analysis focusing on the proteins identified in > 30% of the samples has been applied in the previous published studies. For instance, the study of using proteomic biomarkers to build diagnostic model in lung cancer (PMID: 29576497), proteins identified in > 30% cohort samples were used for downstream analysis. In the study on the impact of Reptin on protein-protein interaction (PMID: 30862565) have demonstrated that proteins were required to have at least in > 30% of samples in order to be included in the proteome dataset.

We compared our cohort with Jun Qin et al. and Bing Zhang et al., study published in Nature (PMID: 25043054), according to the number of the proteins detected in more than 10%, 20%, 30%, 40%, 50%, 60%, 70%, 80%, 90%, 100% of samples, respectively (Figure 2- figure supplement 1). The proportion proteins detected at different cutoff of the samples in the three cohort were, 10% (0.60, 0.94, 0.48), 20% (0.52, 0.83, 0.38), 30% (0.46,0.75, 0.31), 40% (0.41, 0.69, 0.26), 50% (0.37, 0.63, 0.23), 60% (0.33, 0.57, 0.18), 70% (0.29, 0.52, 0.15), 80% (0.25, 0.45, 0.11), 90% (0.19, 0.37, 0.11), 100% (0.07, 0.23, 0.10), respectively. The results showed that our cohort was reliable.

To investigate the impacts of protein identification frequency cutoff in our study, we performed comparative pathway enrichment analysis of the differential expressed proteins (LNM+ vs. LNM-: p-value < 0.05, Wilcoxon rank-sum tests) under different observation percentiles, which were detected in more than 10%, more than 30% and more than 50% of samples, respectively. The results revealed that proteins from three thresholds (10%, 30% and 50%) represented similar pathway enrichment, such as mTOR signaling pathway and amino acid metabolism pathways were dominant in LNM-negative patients, coagulation cascades and Lipid metabolism pathways were overrepresented in the LNM-positive patients (Figure 2- figure supplement 1)

Based on reviewer’s suggestion, we used a cutoff of 50% as identification frequency for variables. The lasso regression was carried out in training cohort (70 LNM-negative and 62 LNM-positive), with AUC of 0.999. The model was validated in VC1 and VC2, with AUC of 0.812 and 0.886, respectively. (Figure 2- figure supplement 1).

3) About identification of the 13 proteins and the criterion to select 5 proteins for IHC validation from 55-protein database:

The process of reducing the number of proteins from 55 to 13 and finally establishing a 5-molecule classifier based on the IHC score is as shown in Figure 1- figure supplement 2 in the revision. We first selected 19 proteins with [log2FC] > 1 or < -1 and p<0.05 (Wilcoxon rank-sum test) between the LNM-negative and LNM-positive in 221 patients from 55 proteins. Then we started looking for antibodies to these 19 proteins. We finally obtained 13 antibodies for further immunohistochemistry. We did immunohistochemical staining to the FFPE samples with 13 antibodies, and got the IHC score of each protein to build the single molecular prediction model by SPSS on ROC curve. For the principles of MS based proteomic and IHC stain are different, not all identified proteins can be converted into IHC. Finally, 5 IHC makers with p-value of IHC score less than 0.05 (Student’s t-test) were selected to build the IHC classifier using Logistic Regression. We also updated the description in the “Result” section in the revised manuscript (line 718-722, page 34-35 in the revision).

4) About the connection between the final 9 proteins and the 19 proteins:

To facilitate the clinical translation of the model, Multiple Logistic Regression was used to obtain 9 core proteins from 19 proteins (Figure 1- figure supplement 2 in the revision). We first performed logistic regression in 19 proteins, and eliminated 10 proteins with insignificant Estimate Std. Error z value (Pr (>|z|) > 0.05, and obtained 9 proteins with Pr(>|z|) < 0.05. After that, we carried out Binary Logistic Regression calculation again with 9 proteins to build the simplified classifier. We also updated the description in the “Materials and methods” section in the revised manuscript (line 1092, page 51 in the revision).

5) About the definition of fold change in the three subtypes with Kruskal-Walli's test:

The fold change in the three subtypes is the ratio of the mean of the expressions in each group (well to moderately differentiated adenocarcinoma, poorly differentiated adenocarcinoma and mucinous adenocarcinoma) to the mean of the other two group. Kruskal-Walli's test was performed between three subtypes.

We also updated the description in the “Result” section in the revised manuscript (line 506-517, page 25 in the revision), and “Figure 1- figure supplement 2H in the revision”.

Reviewer #3 (Public Review):

This work provides a proteomic analysis of 132 early-stage (pT1) colorectal cancers (CRC) to attempt to identify proteins (or a signature pattern thereof) that might be used to predict the patient risk of lymph node metastases (LNM) and potentially stratify patients for further treatment or surveillance. The generated dataset is extensive and the methods appear solid. The work identifies a 55-protein signature that is strongly predictive of LNM in the training cohort and two validation cohorts and then generates two simplified classifiers: a 9-protein proteomic and a 5-protein immunohistochemical classifier. These also perform very well in predicting LNM. Loss of the small GTPase RHOT2 is identified as a poor prognostic factor and validated in a migration assay. The findings could allow better prognostication in CRC and, if confirmed and better validated and contextualized, might impact patient care.

Strengths:

A large training cohort of resected early-stage (pT1M0) CRCs was analyzed by rigorous methods including careful quantitative analysis. The data generated are unbiased and potentially useful. A number of proteins are found to be different between CRCs with and without lymph node metastases, which are used to train a machine learning model that performs flawlessly in predicting LNM in the training cohort and very well in predicting LNM in two validation cohorts. The authors then develop two simplified classifiers that might be more readily extended into clinical care: a 9-protein proteomic assay and a 5-protein immunohistochemical assay; both of these also perform well in predicting LNM. Because LNM is a key prognostic factor, and colectomy (which includes removal of lymph nodes needed to assess LNM) carries significant risk and morbidity, particularly in rectal cancer, classifiers like these are potentially interesting. Finally, the authors identify the loss of expression of RHOT2 as a novel prognostic factor.

Weaknesses:

Major points:

The data are limited by a number of assumptions about metastasis, minimal contextualization of the results, and claims that are too strong given the data. Critically, the authors use the presence or absence of LNM as the study's only outcome; while LNM is a key predictor in CRC, it is uncommon in T1 CRC (generally 3-10%, 12% in this study), stochastic, inefficient, and incompletely identified by histologic evaluation. Larger resection (here, colectomy) removes both identified and occult LNM, which is probably best studied in randomized trials of lymphadenectomy in Japanese gastric cancer cohorts and should be better discussed. Critically, patient survival or disease-free survival would be more relevant outcomes. Further, absent longer-term data, many patients without identified LNM might nonetheless be high-risk and skew the cohorts. It is also not clear whether these findings would be generalizable to other early-stage colon cancers.

The data are also not correlated with the genetics of the cases, which were not discussed.

The results would benefit from the inclusion of standard-of-care MSI status. The classifiers would also be much more impactful if they were generalizable beyond T1 CRCs; this could be readily tested in public datasets.

The authors explain the data as mechanistic, but, aside from one experiment modulating RHOT2 levels, they are fundamentally correlative and should be described as such.

Although they focused on areas containing >80% tumor as judged by the reading pathologist, it is unclear whether the identified proteomic changes originate from the tumor or the microenvironment.

The authors fail to properly contextualize the results or overstate the novelty of their study. A number of examples - the study is claimed as "the first proteomic study of T1 CRC" and "the first comprehensive proteomics study to focus on LNM in patients with submucosal T1 CRCs"; neither of these appears to be true, for example, Steffen et al. (Journal of Proteome Research, 2021, reference 18) may satisfy both of these, although the numbers are smaller. Many other results are reported without context, for example, proteomic characterization of mucinous carcinomas has been performed previously, a modest correlation in mucinous carcinoma is ascribed a large mechanistic role, and PDPN is discussed but is not contextualized as a protein that has been well-studied in the context of metastasis.

The data on RHOT2 are promising but very preliminary. RHOT2 is described as ubiquitous in colorectal cancer cell lines; a brief search in Human Protein Atlas shows RHOT2 RNA and proteins are ubiquitously expressed throughout the body. While its loss appears potentially prognostic, it is unclear whether this is simply a surrogate for other features, such as loss of differentiation state, and whether this is unique to CRC; multivariate analysis would be important.

We appreciate the reviewer for the constructive and insightful comments, which help to improve the quality of this manuscript. Here, we summarized the reviewer’s comments as following: (1) Lack of longer-term data and micrometastasis; (2) test the classifier in public datasets; (3) inclusion of standard genetics and gene alterations; (4) about the tumor purity of all tumor samples and whether the results were influenced by the tumor microenvironment; (5) contextualize the results; (6) multivariate analysis of RHOT2.

1) Lack of longer-term data and micrometastasis:

Thank the reviewer for the comments. We fully acknowledge the limitations of our study, including the uncertainty associated with the detection of lymph node micrometastasis and the lack of long-term survival data, which can impact the strength of our conclusions. We agree that LNM is a key predictor in CRC and that it is uncommon in T1 CRC, with a reported incidence of 3-10%. We acknowledge that larger resections, such as colectomy, are generally recommended for patients with T1 CRC with LNM due to the potential risk of metastasis. However, our study aimed to establish a predictive model for LNM in T1 CRC, which could potentially help guide clinical decision-making on whether additional surgery is needed after endoscopic resection, according to the current NCCN guidelines.

We have taken following methods to address these limitations:

• We matched propensity-score of patients to reduce confounding biases in our training cohort, and patients were prospectively enrolled in our validation cohort, which was designed as a single-blinded prospective study to enhance the rigor and reliability of our findings.

• For the influence of micrometastases in our study. According to reviewer's suggestion, we discussed the reports related to lymph nodes micrometastases in Japanese gastric cancer cohorts (PMID: 17377930, 9070482), and at the same time, we consulted the articles about micrometastases in T1 CRC (PMID: 17661146, 16412600). There were about 5% pT1N0 gastric cancer patients have ITCs in LN, and 10% in pT1Nx CRC. The effect of MMs on prognosis in pT1N0 CRC is still unclear. The present of ITCs/MMs in LN may explain why there are nearly 13% (29 of 221) LNM-negative patients were classified into high-risk group by the prediction model in our study.

We have also added a section to the “Discussion” in the revised manuscript to discuss the potential impact of these limitations on the interpretation of our findings (line 856-873, page 41) in the revision, as follow:

“In this study, to ensure the accuracy of LN status of the enrolled patients, the dissected number of LN in all patients including both surgical resection and ESD was more than 12. However, the longer-term follow-up data, including DFS, PFS, etc., are not available, due to limitations in sample collection time and the prognosis of such patients needs to be tracked over long periods of time, and may impact the strength of our conclusions. To address this limitation, we used propensity-score matching to reduce confounding biases in our training cohort. Patients were prospectively enrolled in our validation cohort (VC2), which was designed as a single-blinded prospective study to enhance the rigor and reliability of our findings. Furthermore, the presence of isolated tumor cells (ITCs) or micrometastases (MMs) within regional LN are not considered, due to conventional histopathologic examination cannot detected them. According to previous studies, there were about 5% pT1N0 gastric cancer patients have ITCs in LN, and 10% in pT1Nx CRC. The effect of MMs on prognosis in pT1N0 CRC is still unclear. The present of ITCs/MMs in LN may explain why there are nearly 13% (29 of 221) LNM-negative patients were classified into high-risk group by the prediction model in our study. Our study would provide a valuable database and could help for clinical decision-making in the context of T1 CRC. We will continuously follow the prognosis of the patients, and the ITCs/MMs in LN also need to be further validated in the future studies.”

In conclusion, we appreciate reviewer’s comments and acknowledge the limitations of our study. We believe that our study provides valuable insights into the development of a predictive model for LNM in T1 CRC, which could potentially aid in clinical decision-making according to the current NCCN guidelines.

2) Test the classifier in public datasets:

According to reviewer’s suggestions, we tested our classifier in two different public datasets, including the colon and rectal cancer study from CPTAC published in Nature (PMID: 25043054), and the metastatic colorectal cancer study published in Cancer Cell (PMID: 32888432). The detail was further discussed in “point-to-point responses R3 Q2.”.

3) Standard genetics and gene alterations:

According to reviewer’s suggestions, we assessed MSI status and CRC-associated gene mutations (RAS, BRAF and PIK3CA) in our cohort. The detail was further discussed in “point-to-point responses R3 Q1.”

4) The influence of microenvironment:

We apologized for not explaining it clearly. To the question of whether the differences between two groups (LNM+ and LNM-) are caused by tumor microenvironment or the tumor tissues, we firstly, used xCell (PMID: 29141660) to study the composition of the tumor microenvironment (Figure2-source data 4 in the revision). The results showed that there was no difference in the tumor microenvironment between the LNM-positive and negative groups (P > 0.05, Wilcoxon rank-sum test) (Figure RL1A). However, when we compared the xCell algorism-based cell deconvolution results between the LNM-positive and -negative groups, we found 8 microenvironment associated cell features differed in two groups (p<0.05) (Figure RL1B). LNM-positive patients were featured with Chondrocytes and Th1 cells. And the remaining 6 features are all high in LNM-negative patients, including, B cells, cDC, Myocytes, etc. Correspondingly, 7 immune cell markers were also observed to be significantly different between the two groups (Log2FC>1 or <-1, P > 0.05, Wilcoxon rank-sum test) (Figure RL1C).

Secondly, we checked the expression profile of the signature proteins detected in our study by The Human Protein Atlas (HPA). Among 9404 identified proteins, 7852 (83.4%) have HPA’s CRC IHC staining data, and 6249 (79.6%) showed medium to high tumor-specific staining in CRC samples (Figure RL1D). Of the signature proteins up-regulated in LNM-positive patients (LNM+ vs. LNM-: log2FC > 1 and p<0.05, Wilcoxon rank-sum test), 76 of 84 (90.5%) have IHC staining data in HPA, and 63 (82.9%) showed medium to high tumor-specific staining in CRC samples (Figure RL1E). For specific proteins of LNM-negative patients (LNM+ vs. LNM-: log2FC <-1 and p<0.05, Wilcoxon rank-sum test), 72 of 82 (87.8%) have IHC staining data in HPA, and 60 (83.3%) showed medium to high tumor-specific staining in CRC samples (Figure RL1F).

Finally, we reviewed again all H&E-stained slides of tumor tissues of patients involved in the study, and supplemented tumor purity values of tumor samples of all the patients in Figure1-source data 1. We compared the tumor purity between the LNM-positive (with average 87.75%) and negative patients (with average 88.27%). The result showed there was no difference between the two groups (P = 0.46, Student’s t-test), demonstrating the high purity and quality of the tumor tissues. (Figure1-supplementary figure 1J in the revision).

These results indicate that, in our study the differences between LNM-positive and LNM-negative groups are mainly caused by tumor tissues. However, the tumor microenvironment may also play a critical but not direct role in T1 CRC development and progression.

Figure RL1. A. Comparison of xCell scores of immune and microenvironment between the LNM-negative group (n= 143) and LNM-positive group (n= 78). B&C. Immune/stromal signatures identified from xCell, together with derived relative abundance of immune and stromal cell types. D, E, F. Identified signature proteins (D), LNM-positive group up-regulated proteins (E) and LNM-negative group up-regulated proteins (F) were mostly validated by HPA IHC Staining Data. G. Barplot for tumor purity between LNM-negative and -positive patients.

5) Contextualize the results:

According to the reviewer’s advice, we have made corresponding adjustments in the revised manuscript, for example:

• “We have made a comprehensive proteomic study of T1 CRC and provides a reliable data source for future research. “(line 342, page 17 in the revision)

-“Here, we present a comprehensive proteomic study to focus on LNM in patients with submucosal T1 CRCs.” (line 788, page 37 in the revision)

With regard to the problem of results are reported without context, we have provided supplementary descriptions of the context of the results in the “Result” section of the revised manuscript, for example:

• “Mucinous adenocarcinoma was considered to be a significant risk factor of LNM in T1 CRC (PMID: 31620912).” (line 498, page 24 in the revision)

• “Mucinous adenocarcinoma of the colorectal is a lethal cancer with unknown molecular etiology and a high propensity to lymph node metastasis. Previous proteomic studies on mucinous adenocarcinoma have found the proteins associated with treatment response in rectal mucinous adenocarcinoma and mechanisms of metastases in mucinous salivary adenocarcinoma.” (PMID: 34990823, 28249646) (line 534-538, page 26 in the revision)

• “Previous studies have shown that PDPN expression correlated with LNM in numerous cancers, especially in early oral squamous cell carcinomas.” (PMID: 21105028).” (line 570, page 27 in the revision)

6) Multivariate analysis of RHOT2:

RHOT2 and its paralog RHOT1 plays an important role in mitochondrial trafficking (PMID: 16630562). Although the function of RHOT2 in cancer is still unknown, the expression of RHOT1 affects metastasis in a variety of tumors, including pancreatic cancer (PMID: 26101710), gastric cancer (PMID: 35170374), small cell lung cancer (PMID: 33515563), etc. In addition, previous studies have found that Myc regulation of mitochondrial trafficking through RHOT1 and RHOT2 enables tumor cell motility and metastasis (PMID: 31061095).

As shown in Figure 4, in our analysis of previous version, we found RHOT2 was significant down-regulated (Log2FC=-1.35; p=0.003, Wilcoxon rank-sum test) in LNM-positive patients compared with LNM-negative patients in our T1 CRC cohort and the low level of RHOT2 is related to low overall survival of patients with colon cancer in TCGA cohort. Knockdown of RHOT2 expression could markedly enhance the migration ability of colon cancer cells.

In order to further explore the influence of RHOT2 on T1 CRC LNM, in addition to the previous results, we carried out the following analysis as shown in Figure4 in the revision.

We, firstly, calculated the correlations between the expression of RHOT2 and other proteins in our cohort (Figure 4). 1,508 proteins were correlated significantly (P < 0.05, Spearman) with RHOT2, and 1,354 proteins showed a positive correlation (coefficient >0) with RHOT2, and 154 proteins were negatively correlated with RHOT2 (coefficient <0). However, when we performed GSEA in RHOT2-associated proteins to identify biological signatures impacted by RHOT2, most of the obtained pathways (p<0.01) showed NES less than 0, which means these pathways were mainly enriched in RHOT2-negative-correlated group, only “mitochondrion” (GOCC) had a positive correlation (Figure 4). As we known RHOT2 is an important protein involved in the regulation of mitochondrial dynamics and mitophagy (PMID: 16630562). This result indicates that the involvement of RHOT2 in regulation of mitochondrial function might contribute to the pathogenesis of metastasis in cancer, especially in early-stage CRC. Consistent with the previous results, RHOT2-negative-correlated group was significantly enriched for EMT (HALLMARK) and complement and coagulation cascades pathways. Proteins up-regulated in LNM-positive group (LNM+ vs. LNM-: Log2FC >0; p<0.05, Wilcoxon rank-sum test) were negatively correlated with RHOT2(p < 0.05, coefficient<0, Spearman), including CAP2, COL6A3, COL6A2, TNC, DPYSL3, PCOLCE and BGN in pathway EMT; and GUCY1B3, VWF and F13A1 in pathway complement and coagulation cascades (Figure 2E, L; Figure 4D in the revision). ECM, focal adhesion and Dilated cardiomyopathy (DCM) pathways were also enriched in negative-correlated group. Degradation of RHOT2 has already been reported to be associated with DCM (PMID: 31455181). Overall, combined with the previous results, RHOT2 may play an important role in T1 CRC LNM (Figure 4D in the revision.).

As reviewer mentioned the data on RHOT2 are promising, but the understanding of it is preliminary. More analytical studies and experiments are needed in our future researches to understand the specific role and mechanism of RHOT2 in the process of tumor metastasis. In the revision, we discussed these limitations of our research.

Author Response

Reviewer #1 (Public Review):

The central claim that the R400Q mutation causes cardiomyopathy in humans require(s) additional support.

We regret that the reviewer interpreted our conclusions as described. Because of the extreme rarity of the MFN2 R400Q mutation our clinical data are unavoidably limited and therefore insufficient to support a conclusion that it causes cardiomyopathy “in humans”. Importantly, this is a claim that we did not make and do not believe to be the case. Our data establish that the MFN2 R400Q mutation is sufficient to cause lethal cardiomyopathy in some mice (Q/Q400a; Figure 4) and predisposes to doxorubicin-induced cardiomyopathy in the survivors (Q/Q400n; new data, Figure 7). Based on the clinical association we propose that R400Q may act as a genetic risk modifier in human cardiomyopathy.

To avoid further confusion we modified the manuscript title to “A human mitofusin 2 mutation can cause mitophagic cardiomyopathy” and provide a more detailed discussion of the implications and limitations of our study on page 11).

First, the claim of an association between the R400Q variant (identified in three individuals) and cardiomyopathy has some limitations based on the data presented. The initial association is suggested by comparing the frequency of the mutation in three small cohorts to that in a large database gnomAD, which aggregates whole exome and whole genome data from many other studies including those from specific disease populations. Having a matched control population is critical in these association studies.

We have added genotyping data from the matched non-affected control population (n=861) of the Cincinnati Heart study to our analyses (page 4). The conclusions did not change.

For instance, according to gnomAD the MFN2 Q400P variant, while not observed in those of European ancestry, has a 10-fold higher frequency in the African/African American and South Asian populations (0.0004004 and 0.0003266, respectively). If the authors data in table one is compared to the gnomAD African/African American population the p-value drops to 0.029262, which would not likely survive correction for multiple comparison (e.g., Bonferroni).

Thank you for raising the important issue of racial differences in mutant allele prevalence and its association with cardiomyopathy. Sample size for this type of sub-group analysis is limited, but we are able to provide African-derived population allele frequency comparisons for both the gnomAD population and our own non-affected control group.

As now described on page 4, and just as with the gnomAD population we did not observe MFN2 R400Q in any Caucasian individuals, either cardiomyopathy or control. Its (heterozygous only) prevalence in African American cardiomyopathy is 3/674. Thus, the R400Q minor allele frequency of 3/1,345 in AA cardiomyopathy compares to 10/24,962 in African gnomAD, reflecting a statistically significant increase in this specific population group (p=0.003308; Chi2 statistic 8.6293). Moreover, all African American non-affected controls in the case-control cohort were wild-type for MFN2 (0/452 minor alleles).

(The source and characteristics of the subjects used by the authors in Table 1 is not clear from the methods.)

The details of our study cohorts were inadvertently omitted during manuscript preparation. As now reported on pages 3 and 4, the Cincinnati Heart Study is a case-control study consisting of 1,745 cardiomyopathy (1,117 Caucasian and 628 African American) subjects and 861 non-affected controls (625 Caucasian and 236 African American) (Liggett et al Nat Med 2008; Matkovich et al JCI 2010; Cappola et al PNAS 2011). The Houston hypertrophic cardiomyopathy cohort [which has been screened by linkage analysis, candidate gene sequencing or clinical genetic testing) included 286 subjects (240 Caucasians and 46 African Americans) (Osio A et al Circ Res 2007; Li L et al Circ Res 2017).

Relatedly, evaluation in a knock-in mouse model is offered as a way of bolstering the claim for an association with cardiomyopathy. Some caution should be offered here. Certain mutations have caused a cardiomyopathy in mice when knocked in have not been observed in humans with the same mutation. A recent example is the p.S59L variant in the mitochondrial protein CHCHD10, which causes cardiomyopathy in mice but not in humans (PMID: 30874923). While phenocopy is suggestive there are differences in humans and mice, which makes the correlation imperfect.

We understand that a mouse is not a man, and as noted above we view the in vitro data in multiple cell systems and the in vivo data in knock-in mice as supportive for, not proof of, the concept that MFN2 R400Q can be a genetic cardiomyopathy risk modifier. As indicated in the following responses, we have further strengthened the case by including results from 2 additional, previously undescribed human MFN2 mutation knock-in mice.

Additionally, the argument that the Mfn2 R400Q variant causes a dominant cardiomyopathy in humans would be better supported by observing of a cardiomyopathy in the heterozygous Mfn2 R400Q mice and not just in the homozygous Mfn2 R400Q mice.

We are intrigued that in the previous comment the reviewer warns that murine phenocopies are not 100% predictive of human disease, and in the next sentence he/she requests that we show that the gene dose-phenotype response is the same in mice and humans. And, we again wish to note that we never argued that MFN2 R400Q “causes a dominant cardiomyopathy in humans.” Nevertheless, we understand the underlying concerns and in the revised manuscript we present data from new doxorubicin challenge experiments comparing cardiomyopathy development and myocardial mitophagy in WT, heterozygous, and surviving (Q/Q400n) homozygous Mfn2 R400Q KI mice (new Figure 7, panels E-G). Homozygous, but not heterozygous, R400Q mice exhibited an amplified cardiomyopathic response (greater LV dilatation, reduced LV ejection performance, exaggerated LV hypertrophy) and an impaired myocardial mitophagic response to doxorubicin. These in vivo data recapitulate new in vitro results in H9c2 rat cardiomyoblasts expressing MFN2 R400Q, which exhibited enhanced cytotoxicity (cell death and TUNEL labelling) to doxorubicin associated with reduced reactive mitophagy (Parkin aggregation and mitolysosome formation) (new Figure 7, panels A-D). Thus, under the limited conditions we have explored to date we do not observe cardiomyopathy development in heterozygous Mfn2 R400Q KI mice. However, we have expanded the association between R400Q, mitophagy and cardiomyopathy thereby providing the desired additional support for our argument that it can be a cardiomyopathy risk modifier.

Relatedly, it is not clear what the studies in the KI mouse prove over what was already known. Mfn2 function is known to be essential during the neonatal period and the authors have previously shown that the Mfn2 R400Q disrupts the ability of Mfn2 to mediate mitochondrial fusion, which is its core function. The results in the KI mouse seem consistent with those two observations, but it's not clear how they allow further conclusions to be drawn.

We strenuously disagree with the underlying proposition of this comment, which is that “mitochondrial fusion (is the) core function” of mitofusins. We also believe that our previous work, alluded to but not specified, is mischaracterized.

Our seminal study defining an essential role for Mfn2 for perinatal cardiac development (Gong et al Science 2015) reported that an engineered MFN2 mutation that was fully functional for mitochondrial fusion, but incapable of binding Parkin (MFN2 AA), caused perinatal cardiomyopathy when expressed as a transgene. By contrast, another engineered MFN2 mutant transgene that potently suppressed mitochondrial fusion, but constitutively bound Parkin (MFN2 EE) had no adverse effects on the heart.

Our initial description of MFN2 R400Q and observation that it exhibited impaired fusogenicity (Eschenbacher et al PLoS One 2012) reported results of in vitro studies and transgene overexpression in Drosophila. Importantly, a role for MFN2 in mitophagy was unknown at that time and so was not explored.

A major point both of this manuscript and our work over the last decade on mitofusin proteins has been that their biological importance extends far beyond mitochondrial fusion. As introduced/discussed throughout our manuscript, MFN2 plays important roles in mitophagy and mitochondrial motility. Because this central point seems to have been overlooked, we have gone to great lengths in the revised manuscript to unambiguously show that impaired mitochondrial fusion is not the critical functional aspect that determines disease phenotypes caused by Mfn2 mutations. To accomplish this we’ve re-structured the experiments so that R400Q is compared at every level to two other natural MFN2 mutations linked to a human disease, the peripheral neuropathy CMT2A. These comparators are MFN2 T105M in the GTPase domain and MFN2 M376A/V in the same HR1 domain as MFN2 R400Q. Each of these human MFN2 mutations is fusion-impaired, but the current studies reveal that that their spectrum of dysfunction differs in other ways as summarized in Author response table 1:

Author response table 1.

We understand that it sounds counterintuitive for a mutation in a “mitofusin” protein to evoke cardiac disease independent of its appellative function, mitochondrial fusion. But the KI mouse data clearly relate the occurrence of cardiomyopathy in R400Q mice to the unique mitophagy defect provoked in vitro and in vivo by this mutation. We hope the reviewer will agree that the KI models provide fresh scientific insight.

Additionally, the authors conclude that the effect of R400Q on the transcriptome and metabolome in a subset of animals cannot be explained by its effect on OXPHOS (based on the findings in Figure 4H). However, an alternative explanation is that the R400Q is a loss of function variant but does not act in a dominant negative fashion. According to this view, mice homozygous for R400Q (and have no wildtype copies of Mfn2) lack Mfn2 function and consequently have an OXPHOS defect giving rise to the observed transcriptomic and metabolomic changes. But in the rat heart cell line with endogenous rat Mfn2, exogenous of the MFN2 R400Q has no effect as it is loss of function and is not dominant negative.

Our results in the original submission, which are retained in Figures 1D and 1E and Figure 1 Figure Supplement 1 of the revision, exclude the possibility that R400Q is a functional null mutant for, but not a dominant suppressor of, mitochondrial fusion. We have added additional data for M376A in the revision, but the original results are retained in the main figure panels and a new supplemental figure:

Figure 1D reports results of mitochondrial elongation studies (the morphological surrogate for mitochondrial fusion) performed in Mfn1/Mfn2 double knock-out (DKO) MEFs. The baseline mitochondrial aspect ratio in DKO cells infected with control (b-gal containing) virus is ~2 (white bar), and increases to ~6 (i.e. ~normal) by forced expression of WT MFN2 (black bar). By contrast, aspect ratio in DKO MEFs expressing MFN2 mutants T105M (green bar), M376A and R400Q (red bars in main figure), R94Q and K109A (green bars in the supplemental figure) is only 3-4. For these results the reviewer’s and our interpretation agree: all of the MFN2 mutants studied are non-functional as mitochondrial fusion proteins.

Importantly, Figure 1E (left panel) reports the results of parallel mitochondrial elongation studies performed in WT MEFs, i.e. in the presence of normal endogenous Mfn1 and Mfn2. Here, baseline mitochondrial aspect ratio is already normal (~6, white bar), and increases modestly to ~8 when WT MFN2 is expressed (black bar). By comparison, aspect ratio is reduced below baseline by expression of four of the five MFN2 mutants, including MFN2 R400Q (main figure and accompanying supplemental figure; green and red bars). Only MFN2 M376A failed to suppress mitochondrial fusion promoted by endogenous Mfns 1 and 2. Thus, MFN2 R400Q dominantly suppresses mitochondrial fusion. We have stressed this point in the text on page 5, first complete paragraph.

Additionally, as the authors have shown MFN2 R400Q loses its ability to promote mitochondrial fusion, and this is the central function of MFN2, it is not clear why this can't be the explanation for the mouse phenotype rather than the mitophagy mechanism the authors propose.

Please see our response #7 above beginning “We strenuously disagree...”

Finally, it is asserted that the MFN2 R400Q variant disrupts Parkin activation, by interfering with MFN2 acting a receptor for Parkin. The support for this in cell culture however is limited. Additionally, there is no assessment of mitophagy in the hearts of the KI mouse model.

The reviewer may have overlooked the studies reported in original Figure 5, in which Parkin localization to cultured cardiomyoblast mitochondria is linked both to mitochondrial autophagy (LC3-mitochondria overlay) and to formation of mito-lysosomes (MitoQC staining). These results have been retained and expanded to include MFN2 M376A in Figure 6 B-E and Figure 6 Figure Supplement 1 of the revised manuscript. Additionally, selective impairment of Parkin recruitment to mitochondria was shown in mitofusin null MEFs in current Figure 3C and Figure 3 Figure Supplement 1, panels B and C.

The in vitro and in vivo doxorubicin studies performed for the revision further strengthen the mechanistic link between cardiomyocyte toxicity, reduced parkin recruitment and impaired mitophagy in MFN2 R400Q expressing cardiac cells: MFN2 R400Q-amplified doxorubicin-induced H9c2 cell death is associated with reduced Parkin aggregation and mitolysosome formation in vitro, and the exaggerated doxorubicin-induced cardiomyopathic response in MFN2 Q/Q400 mice was associated with reduced cardiomyocyte mitophagy in vivo, measured with adenoviral Mito-QC (new Figure 7).

Reviewer #2 (Public Review):

In this manuscript, Franco et al show that the mitofusin 2 mutation MFN2 Q400 impaires mitochondrial fusion with normal GTPase activity. MFN2 Q400 fails to recruit Parkin and further disrupts Parkin-mediated mitophagy in cultured cardiac cells. They also generated MFN2 Q400 knock-in mice to show the development of lethal perinatal cardiomyopathy, which had an impairment in multiple metabolic pathways.

The major strength of this manuscript is the in vitro study that provides a thorough understanding in the characteristics of the MFN2 Q400 mutant in function of MFN2, and the effect on mitochondrial function. However, the in vivo MFN2 Q/Q400 knock-in mice are more troubling given the split phenotype of MFN2 Q/Q400a vs MFN2 Q/Q400n subtypes. Their main findings towards impaired metabolism in mutant hearts fail to distinguish between the two subtypes.

Thanks for the comments. We do not fully understand the statement that “impaired metabolism in mutant hearts fails to distinguish between the two (in vivo) subtypes.” The data in current Figure 5 and its accompanying figure supplements show that impaired metabolism measured both as metabolomic and transcriptomic changes in the subtypes (orange Q400n vs red Q400a in Figure 5 panels A and D) are reflected in the histopathological analyses. Moreover, newly presented data on ROS-modifying pathways (Figure 5C) suggest that a central difference between Mfn2 Q/Q400 hearts that can compensate for the underlying impairment in mitophagic quality control (Q400n) vs those that cannot (Q400a) is the capacity to manage downstream ROS effects of metabolic derangements and mitochondrial uncoupling. Additional support for this idea is provided in the newly performed doxorubicin challenge experiments (Figure 7), demonstrating that mitochondrial ROS levels are in fact increased at baseline in adult Q400n mice.

While the data support the conclusion that MFN2 Q400 causes cardiomyopathy, several experiments are needed to further understand mechanism.

We thank the reviewer for agreeing with our conclusion that MFN2 Q400 can cause cardiomyopathy, which was the major issue raised by R1. As detailed below we have performed a great deal of additional experimentation, including on two completely novel MFN2 mutant knock-in mouse models, to validate the underlying mechanism.

This manuscript will likely impact the field of MFN2 mutation-related diseases and show how MFN2 mutation leads to perinatal cardiomyopathy in support of previous literature.

Thank you again. We think our findings have relevance beyond the field of MFN2 mutant-related disease as they provide the first evidence (to our knowledge) that a naturally occurring primary defect in mitophagy can manifest as myocardial disease.

Author Response:

Evaluation Summary:

This study investigates the mechanisms by which distributed systems control rhythmic movements of different speeds. The authors train an artificial recurrent neural network to produce the muscle activity patterns that monkeys generate when performing an arm cycling task at different speeds. The dominant patterns in the neural network do not directly reflect muscle activity and these dominant patterns do a better job than muscle activity at capturing key features of neural activity recorded from the monkey motor cortex in the same task. The manuscript is easy to read and the data and modelling are intriguing and well done.

We thank the editor and reviewers for this accurate summary and for the kind words.

Further work should better explain some of the neural network assumptions and how these assumptions relate to the treatment of the empirical data and its interpretation.

The manuscript has been revised along these lines.

Reviewer #1 (Public Review):

In this manuscript, Saxena, Russo et al. study the principles through which networks of interacting elements control rhythmic movements of different speeds. Typically, changes in speed cannot be achieved by temporally compressing or extending a fixed pattern of muscle activation, but require a complex pattern of changes in amplitude, phase, and duty cycle across many muscles. The authors train an artificial recurrent neural network (RNN) to predict muscle activity measured in monkeys performing an arm cycling task at different speeds. The dominant patterns of activity in the network do not directly reflect muscle activity. Instead, these patterns are smooth, elliptical, and robust to noise, and they shift continuously with speed. The authors then ask whether neural population activity recorded in motor cortex during the cycling task closely resembles muscle activity, or instead captures key features of the low-dimensional RNN dynamics. Firing rates of individual cortical neurons are better predicted by RNN than by muscle activity, and at the population level, cortical activity recapitulates the structure observed in the RNN: smooth ellipses that shift continuously with speed. The authors conclude that this common dynamical structure observed in the RNN and motor cortex may reflect a general solution to the problem of adjusting the speed of a complex rhythmic pattern. This study provides a compelling use of artificial networks to generate a hypothesis on neural population dynamics, then tests the hypothesis using neurophysiological data and modern analysis methods. The experiments are of high quality, the results are explained clearly, the conclusions are justified by the data, and the discussion is nuanced and helpful. I have several suggestions for improving the manuscript, described below.

This is a thorough and accurate summary, and we appreciate the kind comments.

It would be useful for the authors to elaborate further on the implications of the study for motor cortical function. For example, do the authors interpret the results as evidence that motor cortex acts more like a central pattern generator - that is, a neural circuit that transforms constant input into rhythmic output - and less like a low-level controller in this task?

This is a great question. We certainly suspect that motor cortex participates in all three key components: rhythm generation, pattern generation, and feedback control. The revised manuscript clarifies how the simulated networks perform both rhythm generation and muscle-pattern generation using different dimensions (see response to Essential Revisions 1a). Thus, the stacked-elliptical solution is consistent with a solution that performs both of these key functions.

We are less able to experimentally probe the topic of feedback control (we did not deliver perturbations), but agree it is important. We have thus included new simulations in which networks receive (predictable) sensory feedback. These illustrate that the stacked-elliptical solution is certainly compatible with feedback impacting the dynamics. We also now discuss that the stacked-elliptical structure is likely compatible with the need for flexible responses to unpredictable perturbations / errors:

"We did not attempt to simulate feedback control that takes into account unpredictable sensory inputs and produces appropriate corrections (Stavisky et al. 2017; Pruszynski and Scott 2012; Pruszynski et al. 2011; Pruszynski, Omrani, and Scott 2014). However, there is no conflict between the need for such control and the general form of the solution observed in both networks and cortex. Consider an arbitrary feedback control policy: 𝑧 = 𝑔 𝑐 (𝑡, 𝑢 𝑓 ) where 𝑢 is time-varying sensory input arriving in cortex and is a vector of outgoing commands. The networks we 𝑓 𝑧 trained all embody special cases of the control policy where 𝑢 is either zero (most simulations) or predictable (Figure 𝑓 9) and the particulars of 𝑧 vary with monkey and cycling direction. The stacked-elliptical structure was appropriate in all these cases. Stacked-elliptical structure would likely continue to be an appropriate scaffolding for control policies with greater realism, although this remains to be explored."

The observation that cortical activity looks more like the pattern-generating modes in the RNN than the EMG seem to be consistent with this interpretation. On the other hand, speed-dependent shifts for motor cortical activity in walking cats (where the pattern generator survives the removal of cortex and is known to be spinal) seems qualitatively similar to the speed modulation reported here, at least at the level of single neurons (e.g., Armstrong & Drew, J. Physiol. 1984; Beloozerova & Sirota, J. Physiol. 1993). More generally, the authors may wish to contextualize their work within the broader literature on mammalian central pattern generators.

We agree our discussion of this topic was thin. We have expanded the relevant section of the Discussion. Interestingly, Armstrong 1984 and Beloozerova 1993 both report quite modest changes in cortical activity with speed during locomotion (very modest in the case of Armstrong). The Foster et al. study agrees with those earlier studies, although the result is more implicit (things are stacked, but separation is quite small). Thus, there does seem to be an intriguing difference between what is observed in cortex during cycling (where cortex presumably participates heavily in rhythm/pattern generation) and during locomotion (where it likely does not, and concerns itself more with alterations of gait). This is now discussed:

"Such considerations may explain why (Foster et al. 2014), studying cortical activity during locomotion at different speeds, observed stacked-elliptical structure with far less trajectory separation; the ‘stacking’ axis captured <1% of the population variance, which is unlikely to provide enough separation to minimize tangling. This agrees with the finding that speed-based modulation of motor cortex activity during locomotion is minimal (Armstrong and Drew 1984) or modest (Beloozerova and Sirota 1993). The difference between cycling and locomotion may reflect cortex playing a less-central role in the latter. Cortex is very active during locomotion, but that may reflect cortex being ‘informed’ of the spinally generated locomotor rhythm for the purpose of generating gait corrections if necessary (Drew and Marigold 2015; Beloozerova and Sirota 1993). If so, there would be no need for trajectories to be offset between speeds because they are input-driven, and need not display low tangling."

For instance, some conclusions of this study seem to parallel experimental work on the locomotor CPG, where a constant input (electrical or optogenetic stimulation of the MLR at a frequency well above the stepping rate) drives walking, and changes in this input smoothly modulate step frequency.

We now mention this briefly when introducing the simulated networks and the modeling choices that we made:

"Speed was instructed by the magnitude of a simple static input. This choice was made both for simplicity and by rough analogy to the locomotor system; spinal pattern generation can be modulated by constant inputs from supraspinal areas (Grillner, S. 1997). Of course, cycling is very unlike locomotion and little is known regarding the source or nature of the commanding inputs. We thus explore other possible input choices below."

If the input to the RNN were rhythmic, the network dynamics would likely be qualitatively different. The use of a constant input is reasonable, but it would be useful for the authors to elaborate on this choice and its implications for network dynamics and control. For example, one might expect high tangling to present less of a problem for a periodically forced system than a time-invariant system. This issue is raised in line 210ff, but could be developed a bit further.

To investigate, we trained networks (many, each with a different initial weight initialization) to perform the same task but with a periodic forcing input. The stacked-elliptical solution often occurred, but other solutions were also common. The non-stacking solutions relied strongly on the ‘tilt’ strategy, where trajectories tilt into different dimensions as speed changes. There is of course nothing wrong with the ‘tilting’ strategy; it is a perfectly good way to keep tangling low. And of course it was also used (in addition to stacking) by both the empirical data and by graded-input networks (see section titled ‘Trajectories separate into different dimensions’). This is now described in the text (and shown in Figure 3 - figure supplement 2):

"We also explored another plausible input type: simple rhythmic commands (two sinusoids in quadrature) to which networks had to phase-lock their output. Clear orderly stacking with speed was prominent in some networks but not others (Figure 3 - figure supplement 2a,b). A likely reason for the variability of solutions is that rhythmic-input-receiving networks had at least two “choices”. First, they could use the same stacked-elliptical solution, and simply phase-lock that solution to their inputs. Second, they could adopt solutions with less-prominent stacking (e.g., they could rely primarily on ‘tilting’ into new dimensions, a strategy we discuss further in a subsequent section)."

This addition is clarifying because knowing that there are other reasonable solutions (e.g., pure tilt with little stacking), as it makes it more interesting that the stacked-elliptical solution was observed empirically. At the same time, the lesson to be drawn from the periodically forced networks isn’t 100% clear. They sometimes produced solutions with realistic stacking, so they are clearly compatible with the data. On the other hand, they didn’t do so consistently, so perhaps this makes them a bit less appealing as a hypothesis. Potentially more appealing is the hypothesis that both input types (a static, graded input instructing speed and periodic inputs instructing phase) are used. We strongly suspect this could produce consistently realistic solutions. However, in the end we decided we didn’t want to delve too much into this, because neither our data nor our models can strongly constrain the space of likely network inputs. This is noted in the Discussion:

"The desirability of low tangling holds across a broad range of situations (Russo et al. 2018). Consistent with this, we observed stacked-elliptical structure in networks that received only static commands, and in many of the networks that received rhythmic forcing inputs. Thus, the empirical population response is consistent with motor cortex receiving a variety of possible input commands from higher motor areas: a graded speed-specifying command, phase-instructing rhythmic commands, or both.."

The use of a constant input should also be discussed in the context of cortical physiology, as motor cortex will receive rhythmic (e.g., sensory) input during the task. The argument that time-varying input to cortex will itself be driven by cortical output (475ff) is plausible, but the underlying assumption that cortex is the principal controller for this movement should be spelled out. Furthermore, this argument would suggest that the RNN dynamics might reflect, in part, the dynamics of the arm itself, in addition to those of the brain regions discussed in line 462ff. This could be unpacked a bit in the Discussion.


We agree this is an important topic and worthy of greater discussion. We have also added simulations that directly address this topic. These are shown in the new Figure 9 and described in the new section ‘Generality of the network solution’:

"Given that stacked-elliptical structure can instantiate a wide variety of input-output relationships, a reasonable question is whether networks continue to adopt the stacked-elliptical solution if, like motor cortex, they receive continuously evolving sensory feedback. We found that they did. Networks exhibited the stacked-elliptical structure for a variety of forms of feedback (Figure 9b,c, top rows), consistent with prior results (Sussillo et al. 2015). This relates to the observation that “expected” sensory feedback (i.e., feedback that is consistent across trials) simply becomes part of the overall network dynamics (M. G. Perich et al. 2020). Network solutions remained realistic so long as feedback was not so strong that it dominated network activity. If feedback was too strong (Figure 9b,c, bottom rows), network activity effectively became a representation of sensory variables and was no longer realistic."

We agree that the observed dynamics may “reflect, in part, the dynamics of the arm itself, in addition to those of the brain regions discussed”, as the reviewer says. At the same time, it seems to us quite unlikely that they primarily reflect the dynamics of the arm. We have added the following to the Discussion to outline what we think is most likely:

"This second observation highlights an important subtlety. The dynamics shaping motor cortex population trajectories are widely presumed to reflect multiple forms of recurrence (Churchland et al. 2012): intracortical, multi-area (Middleton and Strick 2000; Wang et al. 2018; Guo et al. 2017; Sauerbrei et al. 2020) and sensory reafference (Lillicrap and Scott 2013; Pruszynski and Scott 2012). Both conceptually (M. G. Perich et al. 2020) and in network models (Sussillo et al. 2015), predictable sensory feedback becomes one component supporting the overall dynamics. Taken to an extreme, this might suggest that sensory feedback is the primary source of dynamics. Perhaps what appear to be “neural dynamics” merely reflect incoming sensory feedback mixed with outgoing commands. A purely feedforward network could convert the former into the latter, and might appear to have rich dynamics simply because the arm does (Kalidindi et al. 2021). While plausible, this hypothesis strikes us as unlikely. It requires sensory feedback, on its own, to create low-tangled solutions across a broad range of tasks. Yet there exists no established property of sensory signals that can be counted on to do so. If anything the opposite is true: trajectory tangling during cycling is relatively high in somatosensory cortex even at a single speed (Russo et al. 2018). The hypothesis of purely sensory-feedback-based dynamics is also unlikely because population dynamics begin unfolding well before movement begins (Churchland et al. 2012). To us, the most likely possibility is that internal neural recurrence (intra- and inter-area) is adjusted during learning to ensure that the overall dynamics (which will incorporate sensory feedback) provide good low-tangled solutions for each task. This would mirror what we observed in networks: sensory feedback influenced dynamics but did not create its dominant structure. Instead, the stacked-elliptical solution emerged because it was a ‘good’ solution that optimization found by shaping recurrent connectivity."

As the reviewer says, our interpretation does indeed assume M1 is central to movement control. But of course this needn’t (and probably doesn’t) imply dynamics are only due to intra-M1 recurrence. What is necessarily assumed by our perspective is that M1 is central enough that most of the key signals are reflected there. If that is true, tangling should be low in M1. To clarify this reasoning, we have restructured the section of the Discussion that begins with ‘Even when low tangling is desirable’.

The low tangling in the dominant dimensions of the RNN is interpreted as a signature of robust pattern generation in these dimensions (lines 207ff, 291). Presumably, dimensions related to muscle activity have higher tangling. If these muscle-related dimensions transform the smooth, rhythmic pattern into muscle activity, but are not involved in the generation of this smooth pattern, one might expect that recurrent dynamics are weaker in these muscle-related dimensions than in the first three principal components. That is, changes along the dominant, pattern-generating dimensions might have a strong influence on muscle-related dimensions, while changes along muscle-related dimensions have little impact on the dominant dimensions. Is this the case?


A great question and indeed it is the case. We have added perturbation analyses of the model showing this (Figure 3f). The results are very clear and exactly as the reviewer intuited.

It would be useful to have more information on the global dynamics of the RNN; from the figures, it is difficult to determine the flow in principal component space far from the limit cycle. In Fig. 3E (right), perturbations are small (around half the distance to the limit cycle for the next speed); if the speed is set to eight, would trajectories initialized near the bottom of the panel converge to the red limit cycle? Visualization of the vector field on a grid covering the full plotting region in Fig. 3D-E with different speeds in different subpanels would provide a strong intuition for the global dynamics and how they change with speed.


We agree that both panels in Figure 3e were hard to visually parse. We have improved it, but fundamentally it is a two-dimensional projection of a flow-field that exists in many dimensions. It is thus inevitable that it is hard to follow the details of the flow-field, and we accept that. What is clear is that the system is stable: none of the perturbations cause the population state to depart in some odd direction, or fall into some other attractor or limit cycle. This is the main point of this panel and the text has been revised to clarify this point:

"When the network state was initialized off a cycle, the network trajectory converged to that cycle. For example, in Figure 3e (left) perturbations never caused the trajectory to depart in some new direction or fall into some other limit cycle; each blue trajectory traces the return to the stable limit cycle (black).

Network input determined which limit cycle was stable (Figure 3e, right)."

One could of course try and determine more about the flow-fields local to the trajectories. E.g., how quickly do they return activity to the stable orbit? We now explore some aspects of this in the new Figure 3f, which gets at a property that is fundamental to the elliptical solution. At the same time, we stress that some other details will be network specific. For example, networks trained in the presence of noise will likely have a stronger ‘pull’ back to the canonical trajectory. We wish to avoid most of these details to allow us to concentrate on features of the solution that 1) were preserved across networks and 2) could be compared with data.

What was the goodness-of-fit of the RNN model for individual muscles, and how was the mean-squared error for the EMG principal components normalized (line 138)? It would be useful to see predicted muscle activity in a similar format as the observed activity (Fig. 2D-F), ideally over two or three consecutive movement cycles.

The revision clarifies that the normalization is just the usual one we are all used to when computing the R^2 (normalization by total variance). We have improved this paragraph:

"Success was defined as <0.01 normalized mean-squared error between outputs and targets (i.e., an R^2 > 0.99). Because 6 PCs captured ~95% of the total variance in the muscle population (94.6 and 94.8% for monkey C and D), linear readouts of network activity yielded the activity of all recorded muscles with high fidelity."

Given this accuracy, plotting network outputs would be redundant with plotting muscle activity as they would look nearly identical (and small differences would of course be different for every network.

A related issue is whether the solutions are periodic for each individual node in the 50-dimensional network at each speed (as is the case for the first few RNN principal components and activity in individual cortical neurons and the muscles). If so, this would seem to guarantee that muscle decoding performance does not degrade over many movement cycles. Some additional plots or analysis might be helpful on this point: for example, a heatmap of all dimensions of v(t) for several consecutive cycles at the same speed, and recurrence plots for all nodes. Finally, does the period of the limit cycle in the dominant dimensions match the corresponding movement duration for each speed?


These are good questions; it is indeed possible to obtain ‘degenerate’ non-periodic solutions if one is not careful during training. For example, if during training, you always ask for 3 cycles, it becomes possible for the network to produce a periodic output based on non-periodic internal activity. To ensure this did not happen, we trained networks with variable number of cycles. Inspection confirmed this was successful: all neurons (and the ellipse that summarizes their activity) showed periodic activity. These points are now made in the text:

"Networks were trained across many simulated “trials”, each of which had an unpredictable number of cycles. This discouraged non-periodic solutions, which would be likely if the number of cycles were fixed and small.

Elliptical network trajectories formed stable limit cycles with a period matching that of the muscle activity at each speed."

We also revised the relevant section of the Methods to clarify how we avoided degenerate solutions, see section beginning with:

“One concern, during training, is that networks may learn overly specific solutions if the number of cycles is small and stereotyped”.

How does the network respond to continuous changes in input, particularly near zero? If a constant input of 0 is followed by a slowly ramping input from 0-1, does the solution look like a spring, as might be expected based on the individual solutions for each speed? Ramping inputs are mentioned in the Results (line 226) and Methods (line 805), but I was unable to find this in the figures. Does the network have a stable fixed point when the input is zero?


For ramping inputs within the trained range, it is exactly as the reviewer suggests. The figure below shows a slowly ramping input (over many seconds) and the resulting network trajectory. That trajectory traces a spiral (black) that traverses the ‘static’ solutions (colored orbits).

It is also true that activity returns to baseline levels when the input is turned off and network output ceases. For example, the input becomes zero at time zero in the plot below.

The text now notes the stability when stopping:

"When the input was returned to zero, the elliptical trajectory was no longer stable; the state returned close to baseline (not shown) and network output ceased."

The text related to the ability to alter speed ‘on the fly’ has also been expanded:

"Similarly, a ramping input produced trajectories that steadily shifted, and steadily increased in speed, as the input ramped (not shown). Thus, networks could adjust their speed anywhere within the trained range, and could even do so on the fly."

The Discussion now notes that this ramping of speed results in a helical structure. The Discussion also now notes, informally, that we have observed this helical structure in motor cortex. However, we don’t want to delve into that topic further (e.g., with direct comparisons) as those are different data from a different animal, performing a somewhat different task (point-to-point cycling).

As one might expect, network performance outside the trained range of speeds (e.g., during an input is between zero and the slowest trained speed) is likely to be unpredictable and network-specific. There is likely is a ‘minimum speed’ below which networks can’t cycle. This appeared to also be true of the monkeys; below ~0.5 Hz their cycling became non-smooth and they tended to stop at the bottom. (This is why our minimum speed is 0.8 Hz). However, it is very unclear whether there in any connection between these phenomena and we thus avoid speculating.

Why were separate networks trained for forward and backward rotations? Is it possible to train a network on movements in both directions with inputs of {-8, …, 8} representing angular velocity? If not, the authors should discuss this limitation and its implications.


Yes, networks can readily be trained to perform movements in both directions, each at a range of speeds. This is now stated:

"Each network was trained to produce muscle activity for one cycling direction. Networks could readily be trained to produce muscle activity for both cycling directions by providing separate forward- and backward-commanding inputs (each structured as in Figure 3a). This simply yielded separate solutions for forward and backward, each similar to that seen when training only that direction. For simplicity, and because all analyses of data involve within-direction comparisons, we thus consider networks trained to produce muscle activity for one direction at a time."

As noted, networks simply found independent solutions for forward and backward. This is consistent with prior work where the angle between forward and backward trajectories in state space is sizable (Russo et al. 2018) and sometimes approaches orthogonality (Schroeder et al. 2022).

It is somewhat difficult to assess the stability of the limit cycle and speed of convergence from the plots in Fig. 3E. A plot of the data in this figure as a time series, with sweeps from different initial conditions overlaid (and offset in time so trajectories are aligned once they're near the limit cycle), would aid visualization. Ideally, initial conditions much farther from the limit cycle (especially in the vertical direction) would be used, though this might require "cutting and pasting" the x-axis if convergence is slow. It might also be useful to know the eigenvalues of the linearized Poincaré map (choosing a specific phase of the movement) at the fixed point, if this is computationally feasible.

See response to comment 4 above. The new figure 3f now shows, as a time series, the return to the stable orbit after two types of perturbations. This specific analysis was suggested by the reviewer above, and we really like it because it gets at how the solution works. One could of course go further and try to ascertain other aspects of stability. However, we want to caution that is a tricky and uncertain path. We found that the overall stacked-elliptical solution was remarkably consistent among networks (it was shown by all networks that received a graded speed-specifying input). The properties documented in Figure 3f are a consistent part of that consistent solution. However, other detailed properties of the flow field likely won’t be. For example, some networks were trained in the presence of noise, and likely have a much more rapid return to the limit cycle. We thus want to avoid getting too much into those specifics, as we have no way to compare with data and determine which solutions mimic that of the brain.

Reviewer #2 (Public Review):

The study from Saxena et al "Motor cortex activity across movement speeds is predicted by network-level strategies for generating muscle activity" expands on an exciting set of observations about neural population dynamics in monkey motor cortex during well trained, cyclical arm movements. Their key findings are that as movement speed varies, population dynamics maintain detangled trajectories through stacked ellipses in state space. The neural observations resemble those generated by in silico RNNs trained to generate muscle activity patterns measured during the same cycling movements produced by the monkeys, suggesting a population mechanism for maintaining continuity of movement across speeds. The manuscript was a pleasure to read and the data convincing and intriguing. I note below ideas on how I thought the study could be improved by better articulating assumptions behind interpretations, defense of the novelty, and implications could be improved, noting that the study is already strong and will be of general interest.

We thank the reviewer for the kind words and nice summary of our results.

Primary concerns/suggestions:

1 Novelty: Several of the observations seem an incremental change from previously published conclusions. First, detangled neural trajectories and tangled muscle trajectories was a key conclusion of a previous study from Russo et al 2018. The current study emphasizes the same point with the minor addition of speed variance. Better argument of the novelty of the present conclusions is warranted. Second, the observations that motor cortical activity is heterogenous are not new. That single neuronal activity in motor cortex is well accounted for in RNNs as opposed to muscle-like command patterns or kinematic tuning was a key conclusion of Sussillo et al 2015 and has been expanded upon by numerous other studies, but is also emphasized here seemingly as a new result. Again, the study would benefit from the authors more clearly delineating the novel aspects of the observations presented here.

The extensive revisions of the manuscript included multiple large and small changes to address these points. The revisions help clarify that our goal is not to introduce a new framework or hypothesis, but to test an existing hypothesis and see whether it makes sense of the data. The key prior work includes not only Russo and Sussillo but also much of the recent work of Jazayeri, who found a similar stacked-elliptical solution in a very different (cognitive) context. We agree that if one fully digested Russo et al. 2018 and fully accepted its conclusions,then many (but certainly not all) of the present results are expected/predicted in their broad strokes. (Similarly, if one fully digested Sussillo et al. 2015, much of Russo et al. is expected in its broad strokes). However, we see this as a virtue rather than a shortcoming. One really wants to take a conceptual framework and test its limits. And we know we will eventually find those limits, so it is important to see how much can be explained before we get there. This is also important because there have been recent arguments against the explanatory utility of network dynamics and the style of network modeling we use to generate predictions. Iit has been argued that cortical dynamics during reaching simply reflect sequence-like bursts, or arm dynamics conveyed via feedback, or kinematic variables that are derivatives of one another, or even randomly evolving data. We don’t want to engage in direct tests of all these competing hypotheses (some are more credible than others) but we do think it is very important to keep adding careful characterizations of cortical activity across a range of behaviors, as this constrains the set of plausible hypotheses. The present results are quite successful in that regard, especially given the consistency of network predictions. Given the presence of competing conceptual frameworks, it is far from trivial that the empirical data are remarkably well-predicted and explained by the dynamical perspective. Indeed, even for some of the most straightforward predictions, we can’t help but remain impressed by their success. For example, in Figure 4 the elliptical shape of neural trajectories is remarkably stable even as the muscle trajectories take on a variety of shapes. This finding also relates to the ‘are kinematics represented’ debate. Jackson’s preview of Russo et al. 2018 correctly pointed out that the data were potentially compatible with a ‘position versus velocity’ code (he also wisely noted this is a rather unsatisfying and post hoc explanation). Observing neural activity across speeds reveals that the kinematic explanation isn’t just post hoc, it flat out doesn’t work. That hypothesis would predict large (~3-fold) changes in ellipse eccentricity, which we don’t observe. This is now noted briefly (while avoiding getting dragged too far into this rabbit hole):

"Ellipse eccentricity changed modestly across speeds but there was no strong or systematic tendency to elongate at higher speeds (for comparison, a ~threefold elongation would be expected if one axis encoded cartesian velocity)."

Another result that was predicted, but certainly didn’t have to be true, was the continuity of solutions across speeds. Trajectories could have changed dramatically (e.g., tilted into completely different dimensions) as speed changed. Instead, the translation and tilt are large enough to keep tangling low, while still small enough that solutions are related across the ~3-fold range of speeds tested. While reasonable, this is not trivial; we have observed other situations where disjoint solutions are used (e.g., Trautmann et al. COSYNE 2022). We have added a paragraph on this topic:

"Yet while the separation across individual-speed trajectories was sufficient to maintain low tangling, it was modest enough to allow solutions to remain related. For example, the top PCs defined during the fastest speed still captured considerable variance at the slowest speed, despite the roughly threefold difference in angular velocity. Network simulations (see above) show both that this is a reasonable strategy and also that it isn’t inevitable; for some types of inputs, solutions can switch to completely different dimensions even for somewhat similar speeds. The presence of modest tilting likely reflects a balance between tilting enough to alter the computation while still maintaining continuity of solutions."

As the reviewer notes, the strategy of simulating networks and comparing with data owes much to Sussillo et al. and other studies since then. At the same time, there are aspects of the present circumstances that allow greater predictive power. In Sussillo, there was already a set of well-characterized properties that needed explaining. And explaining those properties was challenging, because networks exhibited those properties only if properly regularized. In the present circumstance it is much easier to make predictions because all networks (or more precisely, all networks of our ‘original’ type) adopted an essentially identical solution. This is now highlighted better:

"In principle, networks did not have to find this unified solution, but in practice training on eight speeds was sufficient to always produce it. This is not necessarily expected; e.g., in (Sussillo et al. 2015), solutions were realistic only when multiple regularization terms encouraged dynamical smoothness. In contrast, for the present task, the stacked-elliptical structure consistently emerged regardless of whether we applied implicit regularization by training with noise."

It is also worth noting that Foster et al. (2014) actually found very minimal stacking during monkey locomotion at different speeds, and related findings exist in cats. This likely reflects where the relevant dynamics are most strongly reflected. The discussion of this has been expanded:

"Such considerations may explain why (Foster et al. 2014), studying cortical activity during locomotion at different speeds, observed stacked-elliptical structure with far less trajectory separation; the ‘stacking’ axis captured <1% of the population variance, which is unlikely to provide enough separation to minimize tangling. This agrees with the finding that speed-based modulation of locomotion is minimal (Armstrong and Drew 1984) or modest (Beloozerova and Sirota 1993) in motor cortex. The difference between cycling and locomotion may be due to cortex playing a less-central role in the latter. Cortex is very active during locomotion, but that likely reflects cortex being ‘informed’ of the spinally generated locomotor rhythm for the purpose of generating gait corrections if necessary (Drew and Marigold 2015; Beloozerova and Sirota 1993). If so, there would be no need for trajectories to be offset between speeds because they are input-driven, and need not display low tangling."

2 Technical constraints on conclusions: It would be nice for the authors to comment on whether the inherent differences in dimensionality between structures with single cell resolution (the brain) and structures with only summed population activity resolution (muscles) might contribute to the observed results of tangling in muscle state space and detangling in neural state spaces. Since whole muscle EMG activity is a readout of a higher dimensional control signals in the motor neurons, are results influenced by the lack of dimensional resolution at the muscle level compared to brain? Another way to put this might be, if the authors only had LFP data and motor neuron data, would the same effects be expected to be observed/ would they be observable? (Here I am assuming that dimensionality is approximately related to the number of recorded units * time unit and the nature of the recorded units and signals differs vastly as it does between neuronal populations (many neurons, spikes) and muscles (few muscles with compound electrical myogram signals). It would be impactful were the authors to address this potential confound by discussing it directly and speculating on whether detangling metrics in muscles might be higher if rather than whole muscle EMG, single motor unit recordings were made.

We have added the following to the text to address the broad issue of whether there is a link between dimensionality and tangling:

"Neural trajectory tangling was thus much lower than muscle trajectory tangling. This was true for every condition and both monkeys (paired, one-tailed t-test; p<0.001 for every comparison). This difference relates straightforwardly to the dominant structure visible in the top two PCs; the result is present when analyzing only those two PCs and remains similar when more PCs are considered (Figure 4 - figure supplement 1). We have previously shown that there is no straightforward relationship between high versus low trajectory tangling and high versus low dimensionality. Instead, whether tangling is low depends mostly on the structure of trajectories in the high-variance dimensions (the top PCs) as those account for most of the separation amongst neural states."

As the reviewer notes, the data in the present study can’t yet address the more specific question of whether EMG tangling might be different at the level of single motor units. However, we have made extensive motor unit recordings in a different task (the pacman task). It remains true that neural trajectory tangling is much lower than muscle trajectory tangling. This is true even though the comparison is fully apples-to-apples (in both cases one is analyzing a population of spiking neurons). A manuscript is being prepared on this topic.

3 Terminology and implications: A: what do the authors mean by a "muscle-like command". What would it look like and not look like? A rubric is necessary given the centrality of the idea to the study.

We have completely removed this term from the manuscript (see above).

B: if the network dynamics represent the controlled variables, why is it considered categorically different to think about control of dynamics vs control of the variables they control? That the dynamical systems perspective better accounts for the wide array of single neuronal activity patterns is supportive of the hypothesis that dynamics are controlling the variables but not that they are unrelated. These ideas are raised in the introduction, around lines 39-43, taking on 'representational perspective' which could be more egalitarian to different levels of representational codes (populations vs single neurons), and related to conclusions mentioned later on: It is therefore interesting that the authors arrive at a conclusion line 457: 'discriminating amongst models may require examining less-dominant features that are harder to visualize and quantify'. I would be curious to hear the authors expand a bit on this point to whether looping back to 'tuning' of neural trajectories (rather than single neurons) might usher a way out of the conundrum they describe. Clearly using population activity and dynamical systems as a lens through which to understand cortical activity has been transformative, but I fail to see how the low dimensional structure rules out representational (population trajectory) codes in higher dimensions.

We agree. As Paul Cisek once wrote: the job of the motor system is to produce movement, not describe it. Yet to produce it, there must of course be signals within the network that represent the output. We have lightly rephrased a number of sentences in the Introduction to respect this point. We have also added the following text:

"This ‘network-dynamics’ perspective seeks to explain activity in terms of the underlying computational mechanisms that generate outgoing commands. Based on observations in simulated networks, it is hypothesized that the dominant aspects of neural activity are shaped largely by the needs of the computation, with representational signals (e.g., outgoing commands) typically being small enough that few neurons show activity that mirrors network outputs. The network-dynamics perspective explains multiple response features that are difficult to account for from a purely representational perspective (Churchland et al. 2012; Sussillo et al. 2015; Russo et al. 2018; Michaels, Dann, and Scherberger 2016)."

As requested, we have also expanded upon the point about it being fair to consider there to be representational codes in higher dimensions:

"In our networks, each muscle has a corresponding network dimension where activity closely matches that muscle’s activity. These small output-encoding signals are ‘representational’ in the sense that they have a consistent relationship with a concrete decodable quantity. In contrast, the dominant stacked-elliptical structure exists to ensure a low-tangled scaffold and has no straightforward representational interpretation."

4 Is there a deeper observation to be made about how the dynamics constrain behavior? The authors posit that the stacked elliptical neural trajectories may confer the ability to change speed fluidly, but this is not a scenario analyzed in the behavioral data. Given that the authors do not consider multi-paced single movements it would be nice to include speculation on what would happen if a movement changes cadence mid cycle, aside from just sliding up the spiral. Do initial conditions lead to predictions from the geometry about where within cycles speed may change the most fluidly or are there any constraints on behavior implied by the neural trajectories?

These are good questions but we don’t yet feel comfortable speculating too much. We have only lightly explored how our networks handle smoothly changing speeds. They do seem to mostly just ‘slide up the spiral’ as the reviewer says. However, we would also not be surprised if some moments within the cycle are more natural places to change cadence. We do have a bit of data that speaks to this: one of the monkeys in a different study (with a somewhat different task) did naturally speed up over the course of a seven cycle point-to-point cycling bout. The speeding-up appears continuous at the neural level – e.g., the trajectory was a spiral, just as one would predict. This is now briefly mentioned in the Discussion in the context of a comparison with SMA (as suggested by this reviewer, see below). However, we can’t really say much more than this, and we would definitely not want to rule out the hypothesis that speed might be more fluidly adjusted at certain points in the cycle.

5 Could the authors comment more clearly if they think that state space trajectories are representational and if so, whether the conceptual distinction between the single-neuron view of motor representation/control and the population view are diametrically opposed?

See response to comment 3B above. In most situations the dynamical network perspective makes very different predictions from the traditional pure representational perspective. So in some ways the perspectives are opposed. Yet we agree that networks do contain representations – it is just that they usually aren’t the dominant signals. The text has been revised to make this point.

Author Response:

Reviewer #3 (Public Review):

The Schepartz lab have previously shown that the binding of growth factors results in the formation of two distinct coiled coil dimers within the juxtamembrane (JM) segment. These two isomeric coiled coil structures are also allosterically preferred by point mutations within transmembrane (TM) helix. In this manuscript, authors demonstrate that the JM coiled coil is a binary switch, governing the trafficking status of EGFR, either towards degradative or recycling pathway.

They design novel variants of EGFR (E661R and KRAA) that mimic the two distinct coiled coil types, EGF-type and TGF-α-type. These variants are further validated using bipartite tetracysteine- ReAsH system. In order to assess the trafficking of these variants, authors use confocal imaging to measure colocalization with respective organelle markers. In addition, authors also use variants with point mutations at TM segment that controls the JM coiled coil state to demonstrate that the trafficking is dependent on JM segment and not growth factor identity. EGFR signaling is of prime importance in cancer biology and trafficking plays a major role, where the degradative pathway decreases the signaling, in contrast to recycling pathway that sustains the signaling. The authors clearly demonstrate this switch in EGFR lifetime using relevant variants and show how well-known tyrosine kinase inhibitors regulate this in a drug resistant non-small cell lung cancer model.

The model proposed by the authors is mostly well supported by data, but few points require clarification.

i) The authors need to address why the switch is incomplete when JM mutants are used but appears complete with TM mutants. A) Does this mean recycling requires other criteria in addition to JM segment? B) Is it possible that TM mutants cause other changes in addition to controlling JM segment? C) Would it be better if organelle transmembrane markers were used (Tf, Lamp1, NPC1 etc.).

The revised manuscript now includes a discussion of why the localization switch is less complete for the JM mutants than for the TM mutants. Whether these differences mean that the direction of trafficking requires direct interactions with the JM segment, or alternatively that the TM mutants cause other relevant changes in EGFR is currently under investigation.

ii) It would be helpful to represent data as a distribution or scatter points instead of bar plot. Did authors observe any expression level dependence on their colocalization and lifetime assays?

Figures 2 and 3 have been changed to illustrate both bars and individual points. We did not evaluate the effect of expression level on the extent of colocalization or EGFR lifetime.

iii) Did authors investigate the lifetime of JM variants? Like it was shown with TM variants in Fig 4.

Author Response

Reviewer #1 (Public Review):

Dosil et al. have extensively analyzed NK cell-derived extracellular vesicles containing miRNAs. They analyzed the miRNAs in NK cell-derived EVs and found that specific types of miRNAs are contained in NK cell-derived EVs. Furthermore, they found that NK cell-derived EVs have immunomodulatory functions for T-cell response as well as for monocytes and moDCs. This paper is well designed and provides important information on NK cell-derived EVs. However, it is unclear whether NK cell-derived EVs are different from EVs derived from other immune cells such as T cells and B cells.

We thank the reviewer for his/her comments and for pointing out this key point.

1) The authors analyzed human NK cell-derived EVs. The repertoire of miRNAs in NK-EVs may differ among individuals. It would be better to show the degree of individual differences.

We thank the reviewer for highlighting this point and agree that miRNA content in NK-EVs differs among individuals. We have now included a separate table where we show the relative abundance of EV-miRNAs in secreting activated NK cells and their secreted EVs from small RNA sequencing data, and the corresponding plots, including statistics (new Figure 1-figure supplement 2B,C). However, it is important to highlight that the enrichment of these miRNAs in NK-EVs compared to their parental cells is consistent within individuals, as shown in Figure 1- figure supplement 2 and Supplementary Table S1 where all individual data are shown.

Furthermore, to address the reviewer concern of whether NK-EV content differs from that of other EVs from different cell types we have further analyzed the average ratio of EVs vs secreting cells from a recent article (11) and found that the enrichment of specific miRNAs in NK-EVs is rather cell specific and differs from other unrelated cells such as white fat and hepatic cells, as shown in Figure Review 1 below.

Figure Review 1. Parental cell and EV expression of NK-EV enriched miRNAs

2) The authors analyzed the effect of NK-EVs on T cell response in Fig. 4. However, it is possible that EVs affect T cell responses in a nonspecific manner. It may be necessary to include control EVs.

To address this key point raised by the reviewer, several new experiments were performed.

First, small EVs from two distinct human cell lines (namely the HEK-293, human epithelial kidney cells and the Raji B lymphoblast cells) were isolated, following the differential ultracentrifugation protocol, as described in the methods section. Their effects in primary T cells isolated from human healthy donors showed no impact, neither in IFN-γ secretion (new Figure 3-figure supplement 3), nor in activation, measured by CD25 expression (Figure 4-figure supplement 2E,F), that even decreased upon Raji B cell EV-treatment under Th1-polarizing conditions.

Also, three microRNAs that are preferentially excluded from the NK-EV fraction were selected, namely hsa-miR-124, hsa-miR-3667 and hsa-miR-4158 and loaded onto gold-nanoparticles (new Figure 6-figure supplement 2), and their effects were evaluated in immunocompetent C57/BL6 mice after footpad injection. These experiments showed no effects of these nanoparticles, as observed for NK-EV enriched microRNAs, neither in activation, nor in IFN-γ secretion (new Figure 6H).

Author Response:

Reviewer #1:

Lee et al. identify miR-20b as a molecular regulator of hepatic lipid metabolism through the post-transcriptional regulation of the nuclear receptor PPAR alpha. Through mechanistic studies the authors identified the 3'UTR of PPARa as a direct target for miR-20b regulation of expression. The experiments are well controlled and the study provides deep mechanistic insight into the miR-20b/PPARa circuit in modulating hepatic lipid metabolism. Furthermore, the authors provide evidence that targeting the miR-20b pathway to enhance PPARa activation via synthetic ligand fenofibrate. The studies provide much needed mechanistic insight into molecular regulators of hepatic lipid metabolism in response to nutrient stress such as high fat diet. While this is a detailed and thorough assessment of this pathway, there are several issues that were identified in the review of this article outlined below:

1) The authors state there is no off target expression of miR-20b in adipose tissue in their over expression experiments. However, per figure 4 supplement 1, EpiWAT has increased expression over controls in HFD fed conditions. Furthermore, figure 4 supplement 2 shows a functional difference in EpiWAT weight in HFD where miR-20b treated mice have higher fat weight. The authors need at the least to discuss the potential role of adipose tissue in promoting their observed phenotype.

This is a good point. We increased the number of samples and carefully analyzed the changes of both the expression of Mir20b and the weight of epididymal adipose tissue. We observed that slight increase of Mir20b expression in epididymal adipose tissue of AAV- miR20b HFD-fed mice compared to AAV-control NCD-fed mice, not HFD-fed mice. The expression of Mir20b in adipose tissue of between AAV-control HFD and AAV-Mir20b HFD mice was not significantly changed (Figure 5-figure supplement 1).

We have revised the text and added the discussion about the potential role of adipose tissue (page 25-26, line 582-594). Hepatic steatosis could be affected by adipose tissue through free fatty acid (FFA) release and hepatic uptake of circulating FFAs (Rasineni et al., 2021). Our results showed that the epididymal adipose tissue of HFD-fed mice was enlarged upon AAV-Mir20b treatment; however, the serum FFA levels in these mice were comparable to those in mice treated with the AAV-Control (Figure 5-figure supplement 4B)). Of note, the expression of genes related to lipolysis did not change in adipose tissues, and that of hepatic FA transporter, CD36, was decreased by AAV-Mir20b treatment (Figure 5Q and Figure 5-figure supplement 4A). In addition, excess hepatic triglycerides (TGs) are secreted as very low density lipoproteins (VLDLs), and the secretion rate increases with the TG level (Fabbrini et al., 2008). VLDLs deliver TGs from the liver to adipose tissue and contributes expansion of adipose tissue (Chiba et al., 2003). Together, these reports suggest that adipose tissue is also remodeled by the liver in HFD-fed mice and non-alcoholic fatty liver disease (NAFLD) patients. Therefore, the levels of hepatic TGs are unlikely affected by epididymal adipose tissue, and the increase in fat content (Figure 5-figure supplement 3) may be a consequence of increased hepatic TG levels.

2) Figure 5 shows anti-miR-20b essentially restores PPARa expression. However, the rescue effects in terms of body weight, liver triglycerides and liver damage are only modestly improved. The authors need to discuss this modest effect and potentially offer alternative mechanisms aside from PPARa as the physiological target.

Previously, we introduced AAV treatment after four weeks of high fat diet (HFD) feeding. Anti-Mir20b treatment significantly changed the expression of PPARA; however, the effect on the pathophysiological properties of the liver was significant but modest. We thought that this was because there was not enough time to make a proper impact on the liver. Thus, to maximize the effect of ani-Mir20b, the AAV was administered when the HFD was started. The new results showed more significant effects of anti-Mir20b (Figure 6).

We also observed that other nuclear receptors, such as RORA, RORC, and THRB, could be potential targets of MIR20B (Figure 2H and Figure 2-figure supplement 3). However, in the patient data, there was no significant correlation between the expression of those nuclear receptors and that of MIR20B. In addition, among the candidate targets, only PPARA was selected as an overlapped predicted target of MIR20B by various miRNA target prediction programs, including miRDB, picTAR, TargetSCAN, and miRmap (Figure 2J, Figure 2-figure supplement 2). Consistent with these results, we observed that Ppara, not other nuclear receptors, is the target gene of MiR20b in both AAV-Mir20b and AAV-anti- Mir20b mice (Figure 5-figure supplement 2, Figure 6-figure supplement 2). Thus, we focused on PPARA as a MIR20B target in NAFLD.

3) The authors performed experiments with mutated 3'UTR of PPARa and show mutated PPARa is refractory to regulation by miR-20b. However, the authors provide no functional evidence that mutating the 3'UTR of PPARa elicits changes in hepatic lipid metabolism. Discussion of this point is needed at the minimal.

Thank you for your comment. To provide functional evidence, we tried to establish the PPARA 3’UTR mutation knock-in (KI) system in cells. However, we could not succeed because of technical difficulties and time constraints. Alternatively, we introduced the wild type PPARA open reading frame (ORF) followed by either the wild type (WT) or mutant (Mut) 3’UTR of PPARA in HepG2 cells, and analyzed the importance of the 3’UTR of PPARA. As shown in Figure 2-figure supplement 5C, MIR20B significantly suppressed the expression of PPARA and its target genes in PPARA-3’UTR WT expressing cells. Furthermore, Oil Red O staining showed that MIR20B expression increased the intracellular lipid content in these cells (Figure 2-figure supplement 5B). However, MIR20B did not have an effect on either the expression of PPARA and its target genes or intracellular lipid content in PPARA-3’UTR Mut expressing cells (Figure 2-figure supplement 5C, D). We have added the new results in page 17-18, line 350-359 and Figure 2-figure supplement 5.

Reviewer #2:

1) In the experiments depicted in Figures 1D and E, did OA treatment of HepG2 and/or Huh-7 cells produce a reduction in the levels of mRNA encoding PPARalpha (or PPARalpha protein levels) in concordance with the shown rise in mRNA for miR-20b?

Thank you for your question. The samples used in Figure 1C–E were also analyzed to observe the changes in the expression of PPARA (Figure 2-figure supplement 4A–C). In each sample, the increase in MIR20B expression resulting from oleic acid (OA) treatment and HFD was accompanied by a reduction in the levels of PPARA mRNA.

2) Moreover, Figure 1 shows a fuller landscape of the transcriptional impact of microRNAs in context of obese livers in mice and human. Given this, what made miR20-b more interesting than, for example, miR106a, miR-17, or others that also appear to be robustly regulated? Why focus on miR20b?

This is a very good point. In the analysis of the regulatory network, other miRNAs including MIR129 and MIR106A appeared to possibly regulate nuclear receptors in NAFLD. We further confirmed the relationship between candidate miRNAs and NAFLD progression in patient samples. As shown in the revised Figure 1B, we observed that the expression of MIR20B was more robustly and significantly changed with NAFLD progression than that of MIR129 and MIR106a. This tendency was also confirmed in other experiments using OA- treated HepG2 and Huh7 cells or HFD-fed mice (Figure 1-figure supplement 4). Thus, we focused on the role of MIR20B in NAFLD. Nevertheless, we do not rule out the possibility that other miRNAs may be involved in NAFLD progression. Subsequent studies may uncover the roles of other miRNAs in liver physiology.

3) What does the rank and p-value exactly represent in tabular part of Figure 1A? This is very unclear as shown, including the figure legend.

The p-values in the table of Figure 1A were obtained from the hypergeometric distribution used for testing the enrichment of downregulated nuclear receptors among the targets of a miRNA. In other words, they indicate the probability of having downregulated nuclear receptors among the miRNA targets. They were calculated by the following equation:

where N is the total number of genes analyzed, M is the number of candidate target genes of the miRNA, D is the downregulated NR genes, and O is the observed overlap between miRNA targets and the downregulated NR genes as described in the Materials and Methods (page 9, line 155-157). The ranks in the table were determined according to the p-value. The legend of Figure 1A has been modified as follows:

“Figure 1. MIR20B expression is significantly increased in the livers of dietary and genetic obese mice and humans. (A) The miRNA regulatory networks for NR genes downregulated in the transcriptome of NAFLD patients. The adjusted p-values in the table represent the enrichment of miRNA targets in the downregulated NR genes (hypergeometric distribution).”

4) Figure 1, supplement 1 shows characteristics of patients involved in data for Figure 1, etc. This shows that the normal patients are younger than the other two groups, the M-F ratio is not identical (more female in the normal group), and the total cholesterol levels are not well matched either. What other parameters are available? Hemoglobin A1c? Fasting glucose? In the end, we need to know that the groups, apart from the severity of NAFLD and NASH, were well matched. Given the small size of each group (n = only 4-5, this matching is critical to avoid confounding of the relationship between miR-20b, PPARalpha, and NAFLD/NASH progression.

Thank you for your comment. Accordingly, we have included the patient information in a table (Figure 1-figure supplement 1A, B). To increase the statistical power and prevent confounding effects, we increased the number of samples and tried to match them to compare age, weight, and male/female ratio between the groups. Due to the limited number of patient samples, the cohorts could not be perfectly matched. Nevertheless, there were no significant differences in age and male/female ratio among the three groups. Specifically, serum AST, ALT, and fasting glucose levels were significantly increased with progression from normal to non-alcoholic steatohepatitis (NASH), but total cholesterol was comparable as previously reported (Chung et al., 2020). We have revised the text in page 7-8, line 118- 130.

5) The title of Figure 2 relates to PPARalpha. However, in Figure 2G, it is clear that several NRs are downregulated by miR20b overexpression in cells. Although the paper focuses on PPARalpha, should the authors not explore at least some of the other hits to ensure that the impact of PPARalpha is of particular importance vs. others?

This is a good point. We also observed that other nuclear receptors, such as RORA, RORC, and THRB, could be potential targets of MIR20B (Figure 2H and Figure 2-figure supplement 3). However, in the patient data, there was no significant correlation between the expression of those nuclear receptors and that of MIR20B. In addition, among the candidate targets, only PPARA was selected as an overlapped predicted target of MIR20B by various miRNA target prediction programs, including miRDB, picTAR, TargetSCAN, and miRmap (Figure 2J, Figure 2-figure supplement 2). Consistent with these results, we observed that PPARA, not other nuclear receptors is the target gene of MIR20B in both AAV-Mir20b and AAV-anti-Mir20b mice (Figure 5-figure supplement 2, Figure 6-figure supplement 2). Thus, we focused on PPARA as a MIR20B target in NAFLD.

6) In Figure 3, the data show, presumably, that OA induces miR20b, which then represses PPARalpha and, in turn, CD36 downstream of PPARalpha. If this is the case, then how does OA continue to get into the cells? Once CD36 expression falls dramatically, doesn't the key OA uptake mechanism fall with it? Then, does the induction of miR20b abate? Or, does FATP6 or another uptake mechanism account for OA entry into these cells?

This is a good point. FA uptake was decreased by overexpression of MIR20B, and was accompanied by a considerable decrease in CD36 expression (Figure 4B, J). However, other lipid transporters such as FATPs were not significantly altered (Figure 4-figure supplement 5), suggesting that FA uptake is continued by these transporters. The expression of CD36 is relatively low in normal hepatocytes, and the molecule may not be the primary fatty acid transporter in these cells (Wilson et al., 2016). Furthermore, the decrease in FA uptake upon CD36 KO is modest even during a HFD (Wilson et al., 2016). In addition, we observed that the expression of MIR20B is induced and increased for up to 24 h by OA treatment. This is followed by a slight decrease, remaining at a constant elevated level (Figure 4-figure supplement 6). Together, the findings indicated that other fatty acid transporters contributing to FA uptake account for the entry of OA into cells. We have added these discussion in page 25, line 571-581.

7) Similarly, what happens to AGPAT, GPAT, and DGAT expression in context of OA treatment and modulation of miR20b? Does the capacity of the cell to store OA in the form of triglyceride inside of lipid droplets change, so that the amount of free OA or oleyl-CoA inside the cell rises? Could this impact the transcriptional phenotype?

This is a very good point. Accordingly, we analyzed the transcriptional phenotype in the context of OA treatment and modulation of MIR20B. The expression of glycerolipid synthetic genes, including AGPATs, GPATs, and DGATs, was increased by OA treatment, but MIR20B overexpression did not influence the expression of lipogenic genes except for that of DGAT1. However, treatment with anti-MIR20B significantly reduced the expression of glycerolipid synthetic genes, including GPATs and DGATs, under OA treatment (Figure 4C, N). These results suggested that MIR20B is necessary but not sufficient to induce the expression of glycerolipid synthetic genes under OA treatment. We have shown that OA induces the expression of MIR20B (Figure 1C), which can explain why MIR20B overexpression did not show an additional enhancement under OA treatment. The increase in DGAT1 expression induced by MIR20B might contribute to the increase in TG formation and capacity to store OA. This could change the flux of oleyl-CoA to TG synthesis, not β-oxidation with reduced expression of lipid oxidation-associated genes (Figure 4B). Thus, we can expect that the decrease in OA uptake and increase in TG formation induced by MIR20B resulted in reduced amounts of OA or oleyl-CoA inside the cell. However, as lipid consumption through FA oxidation is decreased by MIR20B, free OA or oleyl-CoA might be maintained at a stably increased level compared to that of OA-untreated MIR NC or MIR20B condition, and the impact of the changes in OA or oleyl-CoA levels on the transcriptional phenotype might not be significant as found in a constant elevated level of MIR20B by OA (Figure 4-figure supplement 6). We have added these results in Figure 4C and the Discussion (page 26, line 595-610). Due to technical constraints, we could not measure the amounts of free OA and oleyl-CoA.

8) In Figure 3P, would the impact of anti-miR on the effect of OA on FASN be lost in PPARalpha KO cells? This would really test the functional relevance of the purported transcriptional hierarchy.

Thank you for your valuable comment. We tested the impact of anti-MIR20B treatment on OA-treated PPARA knock-down (KD) cells, not KO cells, due to technical constraints. PPARA KD cells showed a significant decrease in PPARA expression. As shown in Figure 4- figure supplement 4I, anti-MIR20B treatment enhanced the expression of PPARA but did not have a significant effect on fatty acid synthase (FASN) expression in both control and PPARA KD cells. In addition, PPARA KD did not affect FASN expression. The expression patterns of PPARα target genes differ between mice and humans. FASN is regulated by PPARα in mice, but this is unclear in humans (Rakhshandehroo, Hooiveld, Muller, & Kersten, 2009; Rakhshandehroo, Knoch, Muller, & Kersten, 2010). Moreover, fenofibrate, a PPARα agonist, reduces the expression of FASN in methionine choline-deficient (MCD)-fed mice (Cui et al., 2021). Here, we used human HepG2 cells to investigate the effect of OA and MIR20B. It is plausible that FASN might not be regulated by PPARα in our system. We have added these results in Figure 4-figure supplement 4I.

9) The authors should really at least perform a bulk RNAseq analysis to confirm the similarity of the effect of miR20b or anti-miR seen in cells, at the mouse or human liver tissue level. As it is, they only look at 3 FAOX genes, 2 FA uptake associated genes, and 2 FA synthesis genes. This is not very comprehensive as a validation of the in vitro data, although it is intriguing. Or, at the very least, look at a large validated set of PPARalpha target genes in vivo.

Thank you for your comment. Accordingly, we selected PPARα target genes altered by MIR20B in OA-treated cells (Figure 4-figure supplement 1A, B), and then examined the hepatic expression of PPARα target genes in HFD-fed mice treated with MIR20B or anti- MIR20B (Figure 5R and 6R). The expression of most PPARα target genes was decreased by OA treatment and the HFD, and MIR20B treatment further reduced their expression. In contrast, anti-MIR20B treatment rescued the reduced expression of PPARα target genes under OA treatment and the HFD. These results suggested that MIR20B suppresses PPARA in vivo, which is consistent with the results from cells. We have added these results in Figure 4-figure supplement 1A, B, Figure 5R, and Figure 6R.

10) Notably, the figures in general do NOT show individual data points. This is the standard for visual display, rather than bar graphs with simple SEM bars.

Thank you for your comment. We have revised the graphs to include individual data points.

11) The in vivo data (e.g. Figure 4) are very low n values. Augmenting this would add confidence to the data. As an example, of inconsistencies potentially stemming from very low n, the liver weights (Figure 4F) are not very different across groups, although the triglyceride levels in the livers (Figure 4H) are more than twice as high. The images of liver specimens shown as examples (Figure 4F) are also more dramatic than the weights would indicate. Note also that the body weights of the mice (Figure 4C) are different as well, and this alone could explain the livers being modestly heavier. Indeed, the extent of body weight excess mirrors the extent of liver weight excess, suggesting that the entire animal may be larger across multiple metabolic tissues including adipose. This is proven in Figure 4D, where the fat mass looks to be larger as well. To this end, Figure 4 supplement 2 shows multiple tissue weights to be increased in this model, suggesting that specificity for hepatic steatosis may be low.

Thank you for your comment. Accordingly, we conducted additional in vivo experiments with larger n values (n = 10). Then, we replaced the liver images with more representative ones. AAV-Mir20b robustly induced the hepatic expression of Mir20b and significantly increased the liver weight and hepatic TG levels (Figure 5F, 5I). In the liver of normal human, intrahepatic TGs do not exceed 5 % of the liver weight (Fabbrini & Magkos, 2015). In our results, TG levels were increased more than three times by the HFD, but the impact on liver weight was limited, as TGs did not account for more than 10 % of the liver weight (Figure 5I). Excess hepatic TGs are secreted as very low density lipoproteins (VLDLs), and the secretion rate increases with the TG level (Fabbrini et al., 2008). VLDLs deliver TGs from the liver to adipose tissue and other metabolic tissues (Heeren & Scheja, 2021). The excess hepatic TGs induced by MiR20b were presumably transferred to epididymal adipose tissue, contributing to the increase in adipose tissue weight, while inguinal and brown adipose tissues were not significantly affected by MiR20b (Figure 5-figure supplement 3). Together, the fat mass measured by EchoMRI included intrahepatic and adipose TGs, and mirrored the increases shown in Figure 5D. In addition, MiR20b induced the expression of hepatic DGAT1, which could explain increased TG secretion through VLDLs (Figure 4C) (Alves- Bezerra & Cohen, 2017; Liang et al., 2004).

Conversely, the supply of FFAs from adipose tissue might have contributed to hepatic steatosis. However, we observed that there were no significant changes in the expression of Mir20b and lipolytic genes in adipose tissue (Figure 5-figure supplement 4A). Furthermore, the serum FFA levels in the AAV-Control and AAV-Mir20b groups under the HFD were comparable (Figure 5-figure supplement 4B). These findings suggested that increased intrahepatic TG levels constituted the specific and primary effect of AAV-Mir20b.

12) In figure 5 S1, the anti-miR20b substantially reduces the weights of multiple tissues in mice fed a HFD, given this, why does overall body weight (figure 5c) show such a modest difference. Figure 5 E and F also suggest that the overall weights would have been lower than shown in Figure 5C. In the end, instead of bar graphs of the final weights, the entire weight curve for the mice fed the HFD should have been shown.

Thank you for your comment. To make our results more robust, we increased the sample size (n = 10). Moreover, we provided the entire weight curve and revised the results (Figure 6C). AAV-anti-Mir20b treatment significantly reduced the liver weight (Figure 6F). The weight of adipose tissue, including epididymal white adipose tissue (EpiWAT), tended to decrease; however, the difference was not significant (Figure 6-figure supplement 3). As indicated in a previous question (#11), the change in hepatic TG levels could affect the weight of other tissues. In our revised Figure 6C, we show that the overall weight change might be higher than the sum of weight change of specific metabolic tissues, such as the liver and adipose tissues.

13) How well were the NAFLD vs. normal GSE individuals matched? This is very important, since PPARalpha emerges from comparing these data sets. Matching is very important to make sure that the differences in NR expression does not stem from a confound that went along win parallel with the NAFLD cohort vs. the normal GSE cohort.

This is a very good point. PPARA emerged from regulatory network analysis (Figure 1A) and was selected as target of MIR20B through the analysis of RNA-seq data from MIR20B- overexpressing HepG2 cells (Figure 2). By constructing a regulatory network in NAFLD patients, we determined that MIR20B is responsible for NR regulation in NAFLD. As shown in Figure 1A, we analyzed the differential expression of NR in NAFLD using public GSE data (GSE130970) consisting of patients with NAFLD and age- and weight-matched normal controls (Hoang et al., 2019). To verify the expression of MIR20B, we assessed the miRNA levels in another non-coding RNA GSE dataset (GSE40744) in the original manuscript (previous Figure 1B). However, in the process of reviewing GSE40744 patients’ information with physicians, we found that some of the patients were virus-infected. Thus, we removed the data from GSE40744 and truly apologize for the confusion.

In the revised manuscript (page 16 line 303-304), we examined the expression of MIR20B and other candidate miRNAs such as MIR129 and MIR219A in patient samples from the Asan Medical Center (Seoul, Republic of Korea), who were diagnosed by pathologists and age- and weight-matched. As shown in Figure 1B, MIR20B is one of the main miRNAs involved in NAFLD progression. In addition, the expression of PPARA was significantly negatively correlated with that of MIR20B (Figure 2-figure supplement 3).

Reviewer #3:

In this manuscript, Le et al. use an elegant combination of cultured cells, patient samples, and mouse models to show that miR-20b promotes non-alcoholic fatty liver disease (NAFLD) by suppressing PPAR-alpha. The authors show that miR-20b inhibits PPAR-gamma expression, resulting in reduced fatty acid oxidation, decreased mitochondrial biogenesis, and increased hepatocyte lipid accumulation both in vitro and in vivo. Inhibition of miR-20b in mouse NAFLD models leads to increased PPAR-gamma, reduced hepatic lipid accumulation, decreased inflammation, and improved glucose tolerance. Overall, the data are well-controlled and support the authors' conclusions.

Strengths:

1) In Figure 1, the authors show miR-20b is increased in NAFLD patients, mouse obesity/NAFLD models, and cultured liver cancer cells treated with oleic acid (OA). The use of multiple complementary approaches is very powerful, although more information regarding the diagnoses in the 13 patient samples would be helpful (see below).

Thank you for your comment. Accordingly, we have included the patient information in a table (Figure 1-figure supplement 1A, B). To increase the statistical power and prevent confounding effects, we increased the number of samples and tried to match them to compare age, weight, and male/female ratio between the groups. Due to the limited number of patient samples, the cohorts could not be perfectly matched. Nevertheless, there were no significant differences in age and male/female ratio among the three groups. Specifically, serum AST, ALT, and fasting glucose levels were significantly increased with progression from normal to non-alcoholic steatohepatitis (NASH), but total cholesterol was comparable as previously reported (Chung et al., 2020). We have revised the text in page 7-8, line 118- 130.

2) In Figure 2, the authors show that PPAR-alpha is a direct target of miR-20b. These data include a luciferase reporter assay regulated by the 3'UTR of PPAR-alpha. Importantly, when the 3'UTR is mutated, suppression of luciferase expression by miR-20b is no longer observed. The authors use multiple different algorithms to predict miR-20b targets, look for overlap, and then confirm PPAR-alpha as the most important "hit" in vitro.

3) Figure 3 highlights changes in fatty acid metabolism in HepG2 cells transfected with miR-20b, miR-NC, or anti-miR-20b and treated with oleic acid. Figure 3, supplement 4 shows that anti-miR-20b can alleviate OA-induced hepatic steatosis in both HepG2 cells and primary hepatocytes. The use of another (primary) cell line here is important, because HepG2 is a liver cancer cell line, and metabolic changes in HepG2 cells might not be representative of non-neoplastic hepatocytes.

4) In Figure 4, the authors show that miR-20b promotes hepatic steatosis, increases liver weight, increases liver injury markers, and impairs glucose tolerance and insulin sensitivity in HFD-fed mice. Conversely, anti-miR-20b inhibits hepatic steatosis, decreases liver weight and liver injury markers, and improves glucose tolerance and insulin sensitivity in HFD-fed mice (Figure 5). Anti-miR-20b also inhibits hepatic steatosis and fibrosis and decreases liver injury markers in MCD-fed mice (Figure 8). These in vivo studies provide excellent support for the authors' hypothesis regarding the role of miR-20b in promoting fatty liver disease. The liver readily takes up small nucleic acids, including miRs and anti-miRs. Thus, the possibility of using anti-miR-20b as a therapeutic for fatty liver disease is intriguing, and supported by these experiments.

5) In Figure 6, in HepG2 cells, the authors demonstrate that PPAR-alpha overexpression (or to a lesser extent fenofibrate treatment) is able to rescue the transcriptional effects of miR-20b overexpression. Conversely, siPPAR-alpha can rescue the transcriptional effects of anti-miR-20b. Similar results are shown in Figure 7-fenofibrate is able to at least partially suppress some of the metabolic phenotypes that are exacerbated by miR-20b overexpression in HFD-fed mice (the decreased lean/BW ratio, elevated fasting glucose, some transcriptional changes). Again, it is nice to see that the in vitro data is supported by in vivo results.

Thank you for your comments.

Weaknesses:

1) In Figure 3, figure supplement 2, it seems the effects of miR-20b overexpression in primary hepatocytes may be a bit overstated. While it does seem that miR-20b enhances the accumulation of fat in primary hepatocytes upon OA treatment, miR-20b overexpression alone does not seem to have significant effects on steatosis (A), cholesterol (B), or triglycerides (C).

Thank you for your comment. We have revised the text; “Unlike in HepG2 cells (Figure 2A-C), MIR20B alone did not induce lipid accumulation in primary hepatocytes without OA treatment, but MIR20B significantly increased lipid accumulation in the presence of OA (Figure 4-figure supplement 2)” (page 19, line 383-385). “Figure 4-figure supplement 2. MIR20B enhances lipid accumulation in primary hepatocytes under OA-treatment” (the title of Figure 4-figure supplement 2)

2) Histologic analysis of mouse liver samples by a pathologist is lacking. In Figure 4, is there increased inflammation and/or fibrosis with miR-20b overexpression, or just increased steatosis? In Figure 4 and Figure 8, it would be helpful if steatosis, fibrosis, and inflammation were quantified/scored histologically.

Thank you for your comment. Accordingly, we have conducted histological analysis and measured the NAFLD activity score (NAS) and fibrosis score by a pathologist. We have added the scoring graphs in Figure 5H, 6H, 7H, 8I, 8J, 9G, and 9H. In Figure 5G and 5H, AAV-Mir20b significantly increased steatosis but the increase of inflammation was not significant under the HFD; However, AAV-anti-Mir20b significantly decreased steatosis and inflammation, fibrosis under the MCD (Figure 8H-J). In addition, the combination of AAV-anti- Mir20b with fenofibrate significantly alleviated steatosis, inflammation, and fibrosis compared to AAV-Control under the MCD (Figure 9F-H).

3) The effects of anti-miR-20b on hepatic triglycerides and inflammatory markers in vivo are modest (Figures 5 and 8). Perhaps an enhancement could be seen by combining anti-miR-20b with fenofibrate. While the authors show that fenofibrate's effects are suppressed with miR-20b overexpression, they don't examine what happens when fenofibrate is combined with anti-miR-20b. To me, this experiment is critical to determine if PPAR-alpha activity could be further maximized to combat NAFLD (beyond what is seen with fenofibrate alone).

This is a very good point. Accordingly, we performed a new experiment in which fenofibrate was combined with anti-Mir20b to treat MCD-fed mice. The combination showed further improvements compared with those obtained by fenofibrate treatment alone. The results have been described in page 23-24, line 518-536.

“Recently, drug development strategies for NAFLD/NASH are moving toward combination therapies (Dufour, Caussy, & Loomba, 2020). However, the efficacy of developing drugs, including fenofibrate, against NAFLD/NASH is limited (Fernandez-Miranda et al., 2008). Thus, we tested whether the combination of anti-Mir20b and fenofibrate would improve NAFLD in MCD-fed mice. The levels of hepatic Mir20b were reduced after administration of AAV-anti-Mir20b in MCD-fed mice compared to those in mice administered with AAV-Control, and this reduction was also observed after fenofibrate treatment (Figure 9A). Interestingly, the combination of AAV-anti-Mir20b and fenofibrate increased the levels of PPARα to a greater extent than AAV-Mir20b alone (Figure 9B, C). AAV-anti-Mir20b or fenofibrate administration significantly reduced the liver weight and hepatic TG levels, and co- administration further reduced hepatic steatosis (Figure 9D, E). Histological sections showed that the combination of AAV-anti-Mir20b and fenofibrate improved NAFLD, as evidenced by the effects on both lipid accumulation and fibrosis in the liver (Figure 9F-H). Consistently, the levels of AST and ALT were significantly lower after combined treatment with AAV-anti- Mir20b and fenofibrate than after a single treatment (Figure 9I, J). In addition, the expression of genes related to hepatic inflammation, such as Tnf and Il6 (Figure 9K), and fibrosis, such as Acta2, Col1a1, Fn, and Timp1, (Figure 9L), was further decreased by the combination of AAV-anti-Mir20b and fenofibrate. These results suggest that AAV-anti-Mir20b may increase the efficacy of fenofibrate, especially its effect on fibrosis, and provide a more effective option for improving NAFLD/NASH."

Author Response

Reviewer #1 (Public Review):

This work introduces a novel framework for evaluating the performance of statistical methods that identify replay events. This is challenging because hippocampal replay is a latent cognitive process, where the ground truth is inaccessible, so methods cannot be evaluated against a known answer. The framework consists of two elements:

1) A replay sequence p-value, evaluated against shuffled permutations of the data, such as radon line fitting, rank-order correlation, or weighted correlation. This element determines how trajectory-like the spiking representation is. The p-value threshold for all accepted replay events is adjusted based on an empirical shuffled distribution to control for the false discovery rate.

2) A trajectory discriminability score, also evaluated against shuffled permutations of the data. In this case, there are two different possible spatial environments that can be replayed, so the method compares the log odds of track 1 vs. track 2.

The authors then use this framework (accepted number of replay events and trajectory discriminability) to study the performance of replay identification methods. They conclude that sharp wave ripple power is not a necessary criterion for identifying replay event candidates during awake run behavior if you have high multiunit activity, a higher number of permutations is better for identifying replay events, linear Bayesian decoding methods outperform rank-order correlation, and there is no evidence for pre-play.

The authors tackle a difficult and important problem for those studying hippocampal replay (and indeed all latent cognitive processes in the brain) with spiking data: how do we understand how well our methods are doing when the ground truth is inaccessible? Additionally, systematically studying how the variety of methods for identifying replay perform, is important for understanding the sometimes contradictory conclusions from replay papers. It helps consolidate the field around particular methods, leading to better reproducibility in the future. The authors' framework is also simple to implement and understand and the code has been provided, making it accessible to other neuroscientists. Testing for track discriminability, as well as the sequentiality of the replay event, is a sensible additional data point to eliminate "spurious" replay events.

However, there are some concerns with the framework as well. The novelty of the framework is questionable as it consists of a log odds measure previously used in two prior papers (Carey et al. 2019 and the authors' own Tirole & Huelin Gorriz, et al., 2022) and a multiple comparisons correction, albeit a unique empirical multiple comparisons correction based on shuffled data.

With respect to the log odds measure itself, as presented, it is reliant on having only two options to test between, limiting its general applicability. Even in the data used for the paper, there are sometimes three tracks, which could influence the conclusions of the paper about the validity of replay methods. This also highlights a weakness of the method in that it assumes that the true model (spatial track environment) is present in the set of options being tested. Furthermore, the log odds measure itself is sensitive to the defined ripple or multiunit start and end times, because it marginalizes over both position and time, so any inclusion of place cells that fire for the animal's stationary position could influence the discriminability of the track. Multiple track representations during a candidate replay event would also limit track discriminability. Finally, the authors call this measure "trajectory discriminability", which seems a misnomer as the time and position information are integrated out, so there is no notion of trajectory.

The authors also fail to make the connection with the control of the false discovery rate via false positives on empirical shuffles with existing multiple comparison corrections that control for false discovery rates (such as the Benjamini and Hochberg procedure or Storey's q-value). Additionally, the particular type of shuffle used will influence the empirically determined p-value, making the procedure dependent on the defined null distribution. Shuffling the data is also considerably more computationally intensive than the existing multiple comparison corrections.

Overall, the authors make interesting conclusions with respect to hippocampal replay methods, but the utility of the method is limited in scope because of its reliance on having exactly two comparisons and having to specify the null distribution to control for the false discovery rate. This work will be of interest to electrophysiologists studying hippocampal replay in spiking data.

We would like to thank the reviewer for the feedback.

Firstly, we would like to clarify that it is not our intention to present this tool as a novel replay detection approach. It is indeed merely a novel tool for evaluating different replay detection methods. Also, while we previously used log odds metrics to quantify contextual discriminability within replay events (Tirole et al., 2021), this framework is novel in how it is used (to compare replay detection methods), and the use of empirically determined FPR-matched alpha levels. We have now modified the manuscript to make this point more explicit.

Our use of the term trajectory-discriminability is now changed to track-discriminability in the revised manuscript, given we are summing over time and space, as correctly pointed out by the reviewer.

While this approach requires two tracks in its current implementation, we have also been able to apply this approach to three tracks, with a minor variation in the method, however this is beyond the scope of our current manuscript. Prior experience on other tracks not analysed in the log odds calculation should not pose any issue, given that the animal likely replays many experiences of the day (e.g. the homecage). These “other” replay events likely contribute to candidate replay events that fail to have a statistically significant replay score on either track.

With regard to using a cell-id randomized dataset to empirically estimate false-positive rates, we have provided a detailed explanation behind our choice of using an alpha level correction in our response to the essential revisions above. This approach is not used to examine the effect of multiple comparisons, but rather to measure the replay detection error due to non-independence and a non-uniform p value distribution. Therefore we do not believe that existing multiple comparison corrections such as Benjamini and Hochberg procedure are applicable here (Author response image 1-3). Given the potential issues raised with a session-based cell-id randomization, we demonstrate above that the null distribution is sufficiently independent from the four shuffle-types used for replay detection (the same was not true for a place field randomized dataset) (Author response image 4).

Author response image 1.

Distribution of Spearman’s rank order correlation score and p value for false events with random sequence where each neuron fires one (left), two (middle) or three (right) spikes.

Author response image 2.

Distribution of Spearman’s rank order correlation score and p value for mixture of 20% true events and 80% false events where each neuron fires one (left), two (middle) or three (right) spikes.

Author response image 3.

Number of true events (blue) and false events (yellow) detected based on alpha level 0.05 (upper left), empirical false positive rate 5% (upper right) and false discovery rate 5% (lower left, based on BH method)

Author response image 4.

Proportion of false events detected when using dataset with within and cross experiment cell-id randomization and place field randomization. The detection was based on single shuffle including time bin permutation shuffle, spike train circular shift shuffle, place field circular shift shuffle, and place bin circular shift shuffle.

Reviewer #2 (Public Review):

This study proposes to evaluate and compare different replay methods in the absence of "ground truth" using data from hippocampal recordings of rodents that were exposed to two different tracks on the same day. The study proposes to leverage the potential of Bayesian methods to decode replay and reactivation in the same events. They find that events that pass a higher threshold for replay typically yield a higher measure of reactivation. On the other hand, events from the shuffled data that pass thresholds for replay typically don't show any reactivation. While well-intentioned, I think the result is highly problematic and poorly conceived.

The work presents a lot of confusion about the nature of null hypothesis testing and the meaning of p-values. The prescription arrived at, to correct p-values by putting animals on two separate tracks and calculating a "sequence-less" measure of reactivation are impractical from an experimental point of view, and unsupportable from a statistical point of view. Much of the observations are presented as solutions for the field, but are in fact highly dependent on distinct features of the dataset at hand. The most interesting observation is that despite the existence of apparent sequences in the PRE-RUN data, no reactivation is detectable in those events, suggesting that in fact they represent spurious events. I would recommend the authors focus on this important observation and abandon the rest of the work, as it has the potential to further befuddle and promote poor statistical practices in the field.

The major issue is that the manuscript conveys much confusion about the nature of hypothesis testing and the meaning of p-values. It's worth stating here the definition of a p-value: the conditional probability of rejecting the null hypothesis given that the null hypothesis is true. Unfortunately, in places, this study appears to confound the meaning of the p-value with the probability of rejecting the null hypothesis given that the null hypothesis is NOT true-i.e. in their recordings from awake replay on different mazes. Most of their analysis is based on the observation that events that have higher reactivation scores, as reflected in the mean log odds differences, have lower p-values resulting from their replay analyses. Shuffled data, in contrast, does not show any reactivation but can still show spurious replays depending on the shuffle procedure used to create the surrogate dataset. The authors suggest using this to test different practices in replay detection. However, another important point that seems lost in this study is that the surrogate dataset that is contrasted with the actual data depends very specifically on the null hypothesis that is being tested. That is to say, each different shuffle procedure is in fact testing a different null hypothesis. Unfortunately, most studies, including this one, are not very explicit about which null hypothesis is being tested with a given resampling method, but the p-value obtained is only meaningful insofar as the null that is being tested and related assumptions are clearly understood. From a statistical point of view, it makes no sense to adjust the p-value obtained by one shuffle procedure according to the p-value obtained by a different shuffle procedure, which is what this study inappropriately proposes. Other prescriptions offered by the study are highly dataset and method dependent and discuss minutiae of event detection, such as whether or not to require power in the ripple frequency band.

We would like to thank the reviewer for their feedback. The purpose of this paper is to present a novel tool for evaluating replay sequence detection using an independent measure that does not depend on the sequence score. As the reviewer stated, in this study, we are detecting replay events based on a set alpha threshold (0.05), based on the conditional probability of rejecting the null hypothesis given that the null hypothesis is true. For all replay events detected during PRE, RUN or POST, they are classified as track 1 or track 2 replay events by comparing each event’s sequence score relative to the shuffled distribution. Then, the log odds measure was only applied to track 1 and track 2 replay events selected using sequence-based detection. Its important to clarify that we never use log odds to select events to examine their sequenceness p value. Therefore, we disagree with the reviewer’s claim that for awake replay events detected on different tracks, we are quantifying the probability of rejecting the null hypothesis given that the null hypothesis is not true.

However, we fully understand the reviewer’s concerns with a cell-id randomization, and the potential caveats associated with using this approach for quantifying the false positive rate. First of all, we would like to clarify that the purpose of alpha level adjustment was to facilitate comparison across methods by finding the alpha level with matching false-positive rates determined empirically. Without doing this, it is impossible to compare two methods that differ in strictness (e.g. is using two different shuffles needed compared to using a single shuffle procedure). This means we are interested in comparing the performance of different methods at the equivalent alpha level where each method detects 5% spurious events per track rather than an arbitrary alpha level of 0.05 (which is difficult to interpret if statistical tests are run on non-independent samples). Once the false positive rate is matched, it is possible to compare two methods to see which one yields more events and/or has better track discriminability.

We agree with the reviewer that the choice of data randomization is crucial. When a null distribution of a randomized dataset is very similar to the null distribution used for detection, this should lead to a 5% false positive rate (as a consequence of circular reasoning). In our response to the essential revisions, we have discussed about the effect of data randomization on replay detection. We observed that while place field circularly shifted dataset and cell-id randomized dataset led to similar false-positive rates when shuffles that disrupt temporal information were used for detection, a place field circularly shifted dataset but not a cell-id randomized dataset was sensitive to shuffle methods that disrupted place information (Author response image 4). We would also like to highlight one of our findings from the manuscript that the discrepancy between different methods can be substantially reduced when alpha level was adjusted to match false-positive rates (Figure 6B). This result directly supports the utility of a cell-id randomized dataset in finding the alpha level with equivalent false positive rates across methods. Hence, while imperfect, we argue cell-id randomization remains an acceptable method as it is sufficiently different from the four shuffles we used for replay detection compared to place field randomized dataset (Author response image 4).

While the use of two linear tracks was crucial for our current framework to calculate log odds for evaluating replay detection, we acknowledge that it limits the applicability of this framework. At the same time, the conclusions of the manuscript with regard to ripples, replay methods, and preplay should remain valid on a single track. A second track just provides a useful control for how place cells can realistically remap within another environment. However, with modification, it may be applied to a maze with different arms or subregions, although this is beyond the scope of our current study.

Last of not least, we partly agree with the reviewer that the result can be dataset-specific such that the result may vary depending on animal’s behavioural state and experimental design. However, our results highlight the fact that there is a very wide distribution of both the track discriminability and the proportion of significant events detected across methods that are currently used in the field. And while we see several methods that appear comparable in their effectiveness in replay detection, there are also other methods that are deeply flawed (that have been previously been used in peer-reviewed publications) if the alpha level is not sufficiently strict. Regardless of the method used, most methods can be corrected with an appropriate alpha level (e.g. using all spikes for a rank order correlation). Therefore, while the exact result may be dataset-specific, we feel that this is most likely due to the number of cells and properties of the track more than the use of two tracks. Reporting of the empirically determined false-positive rate and use of alpha level with matching false-positive rate (such as 0.05) for detection does not require a second track, and the adoption of this approach by other labs would help to improve the interpretability and generalizability of their replay data.

Reviewer #3 (Public Review):

This study tackles a major problem with replay detection, which is that different methods can produce vastly different results. It provides compelling evidence that the source of this inconsistency is that biological data often violates assumptions of independent samples. This results in false positive rates that can vary greatly with the precise statistical assumptions of the chosen replay measure, the detection parameters, and the dataset itself. To address this issue, the authors propose to empirically estimate the false positive rate and control for it by adjusting the significance threshold. Remarkably, this reconciles the differences in replay detection methods, as the results of all the replay methods tested converge quite well (see Figure 6B). This suggests that by controlling for the false positive rate, one can get an accurate estimate of replay with any of the standard methods.

When comparing different replay detection methods, the authors use a sequence-independent log-odds difference score as a validation tool and an indirect measure of replay quality. This takes advantage of the two-track design of the experimental data, and its use here relies on the assumption that a true replay event would be associated with good (discriminable) reactivation of the environment that is being replayed. The other way replay "quality" is estimated is by the number of replay events detected once the false positive rate is taken into account. In this scheme, "better" replay is in the top right corner of Figure 6B: many detected events associated with congruent reactivation.

There are two possible ways the results from this study can be integrated into future replay research. The first, simpler, way is to take note of the empirically estimated false positive rates reported here and simply avoid the methods that result in high false positive rates (weighted correlation with a place bin shuffle or all-spike Spearman correlation with a spike-id shuffle). The second, perhaps more desirable, way is to integrate the practice of estimating the false positive rate when scoring replay and to take it into account. This is very powerful as it can be applied to any replay method with any choice of parameters and get an accurate estimate of replay.

How does one estimate the false positive rate in their dataset? The authors propose to use a cell-ID shuffle, which preserves all the firing statistics of replay events (bursts of spikes by the same cell, multi-unit fluctuations, etc.) but randomly swaps the cells' place fields, and to repeat the replay detection on this surrogate randomized dataset. Of course, there is no perfect shuffle, and it is possible that a surrogate dataset based on this particular shuffle may result in one underestimating the true false positive rate if different cell types are present (e.g. place field statistics may differ between CA1 and CA3 cells, or deep vs. superficial CA1 cells, or place cells vs. non-place cells if inclusion criteria are not strict). Moreover, it is crucial that this validation shuffle be independent of any shuffling procedure used to determine replay itself (which may not always be the case, particularly for the pre-decoding place field circular shuffle used by some of the methods here) lest the true false-positive rate be underestimated. Once the false positive rate is estimated, there are different ways one may choose to control for it: adjusting the significance threshold as the current study proposes, or directly comparing the number of events detected in the original vs surrogate data. Either way, with these caveats in mind, controlling for the false positive rate to the best of our ability is a powerful approach that the field should integrate.

Which replay detection method performed the best? If one does not control for varying false positive rates, there are two methods that resulted in strikingly high (>15%) false positive rates: these were weighted correlation with a place bin shuffle and Spearman correlation (using all spikes) with a spike-id shuffle. However, after controlling for the false positive rate (Figure 6B) all methods largely agree, including those with initially high false positive rates. There is no clear "winner" method, because there is a lot of overlap in the confidence intervals, and there also are some additional reasons for not overly interpreting small differences in the observed results between methods. The confidence intervals are likely to underestimate the true variance in the data because the resampling procedure does not involve hierarchical statistics and thus fails to account for statistical dependencies on the session and animal level. Moreover, it is possible that methods that involve shuffles similar to the cross-validation shuffle ("wcorr 2 shuffles", "wcorr 3 shuffles" both use a pre-decoding place field circular shuffle, which is very similar to the pre-decoding place field swap used in the cross-validation procedure to estimate the false positive rate) may underestimate the false positive rate and therefore inflate adjusted p-value and the proportion of significant events. We should therefore not interpret small differences in the measured values between methods, and the only clear winner and the best way to score replay is using any method after taking the empirically estimated false positive rate into account.

The authors recommend excluding low-ripple power events in sleep, because no replay was observed in events with low (0-3 z-units) ripple power specifically in sleep, but that no ripple restriction is necessary for awake events. There are problems with this conclusion. First, ripple power is not the only way to detect sharp-wave ripples (the sharp wave is very informative in detecting awake events). Second, when talking about sequence quality in awake non-ripple data, it is imperative for one to exclude theta sequences. The authors' speed threshold of 5 cm/s is not sufficient to guarantee that no theta cycles contaminate the awake replay events. Third, a direct comparison of the results with and without exclusion is lacking (selecting for the lower ripple power events is not the same as not having a threshold), so it is unclear how crucial it is to exclude the minority of the sleep events outside of ripples. The decision of whether or not to select for ripples should depend on the particular study and experimental conditions that can affect this measure (electrode placement, brain state prevalence, noise levels, etc.).

Finally, the authors address a controversial topic of de-novo preplay. With replay detection corrected for the false positive rate, none of the detection methods produce evidence of preplay sequences nor sequenceless reactivation in the tested dataset. This presents compelling evidence in favour of the view that the sequence of place fields formed on a novel track cannot be predicted by the sequential structure found in pre-task sleep.

We would like to thank the reviewer for the positive and constructive feedback.

We agree with the reviewer that the conclusion about the effect of ripple power is dataset-specific and is not intended to be a one-size-fit-all recommendation for wider application. But it does raise a concern that individual studies should address. The criteria used for selecting candidate events will impact the overall fraction of detected events, and makes the comparison between studies using different methods more difficult. We have updated the manuscript to emphasize this point.

“These results emphasize that a ripple power threshold is not necessary for RUN replay events in our dataset but may still be beneficial, as long as it does not excessively eliminate too many good replay events with low ripple power. In other words, depending on the experimental design, it is possible that a stricter p-value with no ripple threshold can be used to detect more replay events than using a less strict p-value combined with a strict ripple power threshold. However, for POST replay events, a threshold at least in the range of a z-score of 3-5 is recommended based on our dataset, to reduce inclusion of false-positives within the pool of detected replay events.”

“We make six key observations: 1) A ripple power threshold may be more important for replay events during POST compared to RUN. For our dataset, the POST replay events with ripple power below a z-score of 3-5 were indistinguishable from spurious events. While the exact ripple z-score threshold to implement may differ depending on the experimental condition (e.g. electrode placement, behavioural paradigm, noise level and etc) and experimental aim, our findings highlight the benefit of using ripple power threshold for detecting replay during POST. 2) ”

Author Response:

Evaluation Summary:

This manuscript addresses a phenomenon of great interest to researchers in cell metabolism and cancer biology: namely, why do cancer cells often secrete high levels of lactate, despite the presence of abundant oxygen to power nutrient oxidation (Warburg effect). The authors propose that lactate export and subsequent extracellular acidification provides a selective advantage and the concomitant rise in intracellular pH is sufficient to drive flux through glycolysis, thereby sustaining the Warburg effect. This is an intriguing hypothesis that ties together many published observations, but it would require further support both from the technical and conceptual side.

The concept proposed in the evaluation summary is not quite correct, in this paper we have tried to show that it is not lactate export that drives extracellular acidification, but that cells which can increase proton export, via over-expression or increased activity of proton exporting proteins, can subsequently drive upregulation of glycolysis and increased lactate production, likely due to increased intracellular pH (pHi) and the ability of glycolytic enzymes to have enhanced activity under slightly higher pHi. As mentioned in the summary, although some of these observations are known, the novelty lies in that they have not been directly proven by inducing acid export prior to a glycolytic phenotype, we believe showing the casual nature of proton export on glycolysis is the novelty of this research.

Reviewer #1 (Public Review):

In this manuscript, the authors tackle an interesting puzzle: why do cancer cells secrete most of their glucose as lactate? The authors propose that acid export is sufficient to enhance glycolysis and provide a selective advantage to cancer cells growing in vivo. To this end, the authors show that clonal lines expressing CA-IX or PMA1, each of which will facilitate proton export, have elevated capacity to acidify extracellular medium and can drive increased migration/invasion and tumor growth or metastases. In support of the model that extracellular pH is a key driver of metastases, the effect of CA-IX expression on lung metastases is reversed following bicarbonate treatment. While many of the individual conclusions of the manuscript are not novel-for example, pH has been reported to control glycolysis and it is established that CA-IX expression modulates migration/metastases-providing a comprehensive assessment of the ability of proton export to drive the Warburg effect, and assessing the significance of metabolic rewiring driven by acid export on tumor growth, would represent an important resource for researchers intrigued by the pervasive observation that cancer cells secrete lactate despite potential bioenergetic disadvantages of discarding biomass.

The strength of the manuscript lies therefore in tying these disparate observations together in a coherent model and testing the role of acid export per se on glycolytic flux. The technical weaknesses of the paper prevent such coherent model building. A major concern is that all cell lines appear to be generated by transient transfection followed by clonal selection, giving rise to cells with notable variability and inconsistent phenotypes. More traditional approaches to manipulate enzyme expression will provide more robust model systems to test the proposed model. Similarly, direct measures of glycolytic flux are required to make conclusions about the role of acid export in promoting glycolysis. Another strength is the use of heterologous enzyme systems to alter proton export in cancer cells, but alternative explanations for these results are not fully considered. Ultimately, to what extent acid export per se, as opposed to altered metabolism driven by acid export, drives enhanced tumor metastases is not addressed.

We agree wholly with Reviewer 1 that although individual components of this manuscript have previously been implicated in cancer research, the novelty lies in directly assessing metabolic changes, specifically the Warburg effect, as a result of proton production to determine causality rather than correlation as previous studies have shown. The reviewer makes a valid point about our use of clones and this is something we considered at length. When originally designing these experiments, we had many conversations within our lab and with collaborators and colleagues, and the overall consensus was that bulk populations are more likely to have heterogeneous expression levels unrelated to transfection, which could result in the phenotype generated being noisy and not indicative of what occurs when proton exporters are over-expressed. We chose to isolate single clones, maintaining these in antibiotic selection media, to ensure stable over-expression. After confirming over-expression, cells were grown without antibiotics and screened regularly for maintenance of protein expression. This was also one of the reasons why we utilized over-expression of two different proton exporters in multiple different cell lines to be confident that proton export was changing the metabolic phenotype and not just due to changes in an individual isolated clonal line. We utilized bulk population for the MOCK clones, to ensure we weren’t selecting for a clone which had inherently different metabolic traits from the parental population. As described in the paper, while some of the behaviors of the different clones are indeed divergent, the impact of expression on increased glucose uptake and lactate production is wholly consistent and highly correlated to expression of PMA1 or CA-IX. Although we utilized metabolic profiling, we do not claim to infer flux from these data. Flux was assessed via lactate production and glucose consumption rates. The metabolomic analyses showed that glycolytic intermediates upstream of Pyruvate Kinase (PK) were uniformly increased in transfectants. This was an unequivocal finding and, given the increased flux, we have concluded that transfection results in activating glycolytic enzymes upstream of PK. The pleiotropic nature of these effects have led us to propose that intracellular pH was increasing and likely enhancing glycolytic enzyme activity throughout the glycolytic pathway. We measured the intracellular pH and showed that it was generally elevated in the transfectants. Finally, the reviewer was concerned that we did not address the mechanism by which pH increases metastases. Such a study would be beyond the scope of this paper and, indeed, was the subject of a two-volume special issue of Cancer Mets. Rev. in 2019 (PMC6625888). Hence, in this paper, we were not trying to address the mechanism by which pH affects metastasis, but simply wanted to show additional biological relevance.

Reviewer #2 (Public Review):

The work by Xu et al proposes that the Warburg effect - the increase of glycolytic metabolism usually displayed by tumor cells, is driven by increased proton excretion rather than by oncogenic dysregulation of glycolytic enzyme levels. As a proof-of-principle, they engineered tumor cells to increase proton excretion. They observed an increase in glycolytic rate, pH, and malignancy in their engineered cells.

1. My main issue with this work is that I do not agree with the authors when they say that the "canonical view" is that oncolytic mutations are thought to drive the Warburg effect. What I understand the consensus to be, is that it is fast proliferating cells - rather than malignant cells - the ones who display this form of metabolism. The rationale is that glycolytic metabolism allows keeping biomass by redirecting lactate and from the phosphate pentose pathway. In contrast, the end product of oxidative phosphorylation is CO2 that cannot be further utilized in cell metabolism.

They claim that they Vander Heiden et al., 2009 shows that "fermentation under aerobic conditions is energetically unfavorable and does not confer any clear evolutionary benefits." This is incorrect. While that review states that the Warburg effect has little effect on the ATP/ADP ratio, they do show this form of metabolism has significant benefits for fast proliferating cells. In fact, the whole review is about how the Warburg effect is a necessary metabolic adaptation for fast proliferation rather than a unique feature of malignant cells.

1. Their main observation is not surprising. From a biochemical standpoint, protons are final product of glycolysis (from the production of lactic acid). Thus, by mass action, any mechanism to remove protons from the cell will result in accelerated glycolytic rate. Similarly, reducing intracellular pH will necessarily slow down LDHA's activity, which in turn will slow down pyruvate kinase and so on.

2. Their experiments are conducted on transformed cells - that by definition - have oncogenic driver mutations. They should test the effect of proton exporter using primary non-transformed cells (fresh MEFs, immune cells, etc). I would expect that they will still see the increase in glycolysis in this case. And yet, I would still have my concerns I expressed in my previous point.

3. The fact that they can accelerate the Warburg effect by increasing proton export does not mean is the mechanism used by tumor cells in patients or "the driver" of this effect. As I mentioned, their observation is expected by mass action but tumors that do not overexpress proton transporter may still drive their Warburg effect via oncogenic mutations. The biochemical need here is to increase the sources of biomass and redox potential and evolution will select for more glycolytic phenotypes.

Comment 1: We disagree with the reviewer that the energetic demands of a faster proliferating cell drive glycolysis in order to produce the biomass needed for generation of new cells. Available evidence does not support this hypothesis. As the reviewer mentioned, there is a correlation between proliferation and aerobic glycolysis (i.e. if cells are stimulated to grow they will consume more glucose), and the same can be said for motility (i.e. more motile cells have higher aerobic glycolysis). This is also true for normal cells and tissues that exhibit high levels of aerobic glycolysis. We agree that glycolytic ATP generation is more rapid than oxidative phosphorylation and that this may confer some selective advantage for transporters, as we described in PMC4060846. Nonetheless, it is clear that under conditions of similar proliferation and motility, more aggressive cancer cells ferment glucose at much higher rates. However, correlations between neither proliferation nor motility are the “Warburg Effect” which is a higher rate of aerobic glycolysis in cancers, regardless of proliferation or migration. As we described in PMID 18523064, the prevailing view in the cancer literature is that the Warburg effect is driven by oncogenes (ras, myc), transcription factors (HIF) and tumor suppressors (p53/TIGAR) through increased expression of glycolytic enzymes. This assumes that expression levels drive flux which has not been proved empirically. In biochemical pathways, it is canon that flux is regulated by demand (e.g. ATP) or through some post-transcriptional control (e.g. pH). In Vander Heiden’s paper the steady state levels are reported of ATP/ADP ratios, not flux. The first paragraph of the intro has been modified to accommodate this concern.

Comment 2: The fact that our results are not surprising is our major argument: i.e. that glycolytic flux can be enhanced by increasing the rate of H+ export. We saw an increase in intracellular pH (pHi), but our metabolomics data do not support a direct effect on LDHA or PK. Instead, we show that clones with higher pHi have a crossover point at PK, due to reduced inhibition of upstream enzymes which is not there in clones at lower pHi.

Comment 3: We agree it would be interesting to study the effects of proton export on immune cells especially given the increase in immunotherapy use in cancer treatment. We did utilize HEK 293 cells shown in supplemental figure S6, to show this was not a cancer cell line specific phenomenon, and we saw increased aerobic glycolysis with over-expression of CA-IX.

Comment 4: We agree that oncogenic mutations can alter glycolytic rate, but we observed that increased expression and activity of proton exporters is sufficient to drive a Warburg effect. Although the reviewer indicates that glycolysis is responsible for generating the biomass needed for these faster proliferating cells, we have shown that proton exporter driven aerobic glycolysis does not increase proliferation rates. The literature, see Vander Heiden’s paper below, suggests that amino acids, mainly glutamine, can support the majority of biomass needs of a proliferating cell. Hence, reliance on aerobic glycolysis remains energetically inefficient and inefficient in that most of the carbons are removed, and thus will not be selected by evolution.

Hosios, A.M., Hecht, V.C., Danai, L.V., Johnson, M.O., Rathmell, J.C., Steinhauser, M.L., Manalis, S.R., & Vander Heiden, M.G. (2016). Amino Acids Rather than Glucose Account for the Majority of Cell Mass in Proliferating Mammalian Cells. Developmental cell, 36 5, 540-9 .

Reviewer #3 (Public Review):

The authors claim that "proton export drives the Warburg effect". For this, they expressed proton-exporting proteins in cells and measured the intracellular proton concentration and the Warburg effect. Based on their data, however, I do not see elevated Warburg effect in these cells and thus conclude that the claim is not supported.

The authors concluded that the CA-IX or PMA1 expressing cells had increased Warburg effect. I don't think this conclusion can be made based on the data presented. For the MCF-7 cells, the glucose consumption is ~18 pmol/cell/24hr (Fig. 5E) and lactate production is ~0.6 pmol/cell/24hr (Fig. 5F), indicating that 0.6/18/2 = 1.7% of the glucose is excreted as lactate. This low percentage remains true for the PMA1 expressing cells. For example, for the PMA1-C5 cells, the percentage of glucose going to lactate is about 1.8/38/2 = 2.4% (Fig. 5EF). While indeed there was an increase of both the glucose and lactate fluxes in the PMA1 expressing cells, the vast majority of the glucose flux ends up elsewhere likely the TCA cycle. This is a very different phenotype from cancer cells that have Warburg effect. The same calculation can be done for the CA-IX cells but the data on the glucose and lactate concentration there are inconsistent and expressed in confusing units (which I will elaborate in the next paragraph). Nevertheless, as there were at most a few folds of increase in lactate production flux in the M1 and M6 cells, the glucose flux going to lactate production is likely also a few percent of the total glucose uptake flux. Again, these cells do not really have Warburg effect.

The glucose and lactate concentration data are key to the study. The data however appear to lack consistency. The lactate concentration data in Fig. 1F shows a ~5-fold increase in the M1 and M6 cells than the controls but the same data in S. Fig. 2 shows a mere ~50% increase. The meaning of the units on these figures is not clear. While "1 ng/ug protein" means 1ng of lactate is produced by 1 ug protein of cells over a 24 hour period, I do not understand what "ng/ul/ug protein" means (Fig. 1F). Also, "g/L/cell" must be a typo (S. Fig. 2). Furthermore, regarding the important glucose consumption flux, it is not clear why the authors did not directly measure it as they did for the PMA1 cells (Fig. 5E). Instead, they showed two indirect measurements which are not consistent with each other (Fig. 1E and S. Fig. 1).

The reviewer pointed out discrepancies in our data and, upon reviewing, we have identified a dilution error leading to miscalculation of glucose consumption in Fig 5E. We have also repeated these experiments which agree with our re-calculation. Originally, it appeared from the data we presented that there was very little lactate flux, we have re-calculated the glucose excreted as lactate (average % using data from Fig. 5E and 5F) and present in a table below. We do believe we observed a Warburg effect in our proton exporting cells consistently. The reviewer points out that we utilized multiple methods to measure glycolysis in these cells leading to inconsistency, however we felt using multiple methods/instruments/kits to assess glucose consumption, lactate production, and glucose induced proton production rates was a strength of our findings as we consistently saw increased glycolysis in our proton exporting clones, irrespective of proton exporter, cell line, or method utilized. We are also not suggesting that glucose is solely being metabolized through glycolysis and do agree that it can metabolized through other metabolic pathways too such as TCA cycle, as the reviewer stated. The units used for these graphs are described in the methods and figure legends, in some assays such as Fig. 1F lactate was graphed as the ng of lactate per ul of cell culture media and then normalized per ug protein, which was determined by calculating the protein concentration of cells per well of the assay. Supplementary figure 2 has been re plotted per 10K cells to match other normalization values in the paper. Fig 1E and Fig. S1 are two different time points, M6 acidified media faster than M1 and this is likely why at 1 hour we are not yet seeing substantial increase in glucose uptake of M1.

Author Response

Reviewer #1 (Public Review):

1) The authors present an interesting proposal for how the generative model operates when producing shapes in Fig 6, as well as some alternative strategies in Fig 7. It is not clear what evidence supports the idea that shapes are first broken down into parts, then modified and recombined. It is obvious from the data that distinctive features are preserved (in some cases), but some clarification on the rest would be useful. For instance, is it possible that conjunctions or combinations of features are processed in concert? What determines whether critical features are added or subtracted to the shape during generation? Some more justification for this proposed model is needed, as well as for how the exceptions and alternate strategies were determined.