Author response:

(1) General Statements

We thank all three reviewers for their constructive comments and suggestions. We also thank reviewers #2 and #3 for considering our work to be timely and of interest to the field, not only for basic researchers, but also for translational scientists and industry. We are now providing additional results to further support our hypothesis and hope that all reviewers will find that our manuscript is now ready for publication. 

(2) Point-by-point description of the revisions

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

The manuscript by Coquel et al. investigates the effects of BKC and IBC, two compounds found in Psoralea corylifolia in DNA replication and the response to DNA damage, and explores their potential use in cancer treatment. These compounds have been previously shown to affect different cellular pathways and the authors use transformed cancer cells of different origins and a non-transformed cell line to question if their combination is toxic in cancer versus non-cancer cells. They propose that BKC inhibits DNA polymerases while IBC targets CHK2. Their results show that both compounds do affect DNA replication, inducing replication stress and affecting double strand break repair. They also show that their combined use increases their toxicity in a synergistic manner. 

However, there are some major conclusions that are still not very well supported by the data: first, the differential effect on cancer and non-transformed cells; second, the direct link of BKC to the inhibition of DNA polymerases; and third, it is unclear if CHK2 is the relevant target for IBC in this context. 

Regarding these points the authors should address the following issues: 

(1) Most of the experiments use BJ fibroblasts as a control cell line. In order to evaluate if these compounds are preferentially toxic for cancer cells, the use of more than one non-transformed cell line is necessary. In addition, BJ cells are fibroblasts while most of the cancer cell lines employed are of epithelial origin. The authors could use MCF10 and RPE cells (both of epithelial origin) as control cell lines to complement the results and better support this claim. 

We have now monitored the effect of IBC and BKC on the proliferation of MCF-7, MCF-10A and RPE-1 cells using the WST-1 assay and obtained similar results as for BJ and MCF-7 cells. These results are now included in the revised manuscript as Fig. S1A and S1B.

(2) In order to explore what are the targets of BKC and IBC Cellular Thermal Shift Assays (CETSA) could be used. Either by doing an unbiased mass spectrometry analysis of proteins stabilized by these compounds or by a direct analysis of candidate proteins by western blot (a similar approach has been used for IBC to show that it inhibits SIRT2 in Ren et al., 2024 Phytotherapy Res).

We thank this Reviewer for suggesting the use of the CETSA assay. We have now performed  CETSA on MCF-7 cells and found that IBC stabilizes CHK2 but not CHK1, to the same extent as the commercial CHK2 inhibitor BML-277 used here as a positive control. These results are now shown in new Fig. 4G and 4H.

(3) For BKC in vitro polymerase assays could be carried out to show the direct inhibition of the DNA polymerase delta, for instance. 

We have used high-speed Xenopus egg extracts to replicate ssDNA in vitro (Fig. S2C). This assay differs from the in vitro replication assay using low-speed Xenopus egg extracts (Fig. 2H) in that it only monitors elongation by replicative DNA polymerases (Pol δ and ε) and not earlier steps such as origin licensing and activation. The combined use of both low-speed and highspeed extracts strongly supports the view that BKC inhibits replicative DNA polymerases. 

To confirm this result, we have also used CETSA to monitor BKC binding to different subunits of DNA Polδ and Polε in MCF-7 cells and in Xenopus egg extracts (Fig. 3C-D Fig. S3). We found that BKC binds POLD1 and POLE, the catalytic subunits of Pol δ and ε respectively, but not the accessory subunit POLD3 nor PCNA. Together with our docking results and DNA fiber experiments, these data strongly support the view that BKC is a potent inhibitor of DNA Pol and Pol. 

(4) In addition, the authors could analyze the integrity of replication forks by PCNA immunofluorescence analysis. The colocalization of PCNA and POLD or POLE subunits could also support the role of DNA polymerases as targets of BKC. 

Our molecular docking results also show that BKC occupies the catalytic sites of DNA Pol δ and ε, which may not affect their subcellular localization and/or PCNA binding. Since our DNA replication assays, CETSA and DNA fiber analyses strongly support the view that BKC inhibits replicative DNA polymerases, we have not performed this additional experiment.

(5) In the case of IBC and the inhibition of CHK2, the authors should check the effect of IBC on the phosphorylation of BRCA1 on S988. The changes in CHK2 phosphorylation in Figure 3B are not convincing. The experiment should be repeated and the average of at least three experiments needs to be quantified. 

We now provide evidence that IBC inhibits BRCA1 phosphorylation on S988. Western blots and quantification for three biological replicates are shown in Fig. 4C and Fig. S4H. Densitometric quantification of CHK2 phosphorylation on S516 from 3 biological replicates, along with statistical analysis, is now shown in Fig. S4G.

(6) To prove that CHK2 is the relevant target for IBC the authors could test if ATM and CHK2 knockout cells are more resistant to this compound, since it would prevent the phosphorylation of CHK2. 

We have performed siRNA transfection targeting CHK2. The transfected cells died after 72 hours in culture, so we have been unable to determine whether CHK2-KD cells have increased resistance to IBC.  

In addition to these experiments, I would suggest some other major improvements in the manuscript: 

(1) The concentration of both compounds should be provided in molar units throughout the paper.

Thanks for pointing this out, we now use molar units throughout the paper.

(2) The authors do not clearly indicate the concentration that is employed in the different experiments, making it difficult to assess the results. For instance, Figure 2 does not include the concentration in the legend or in the text. Time and concentration need to be clearly shown for each experiment. 

The experimental conditions and inhibitor concentrations are now clearly indicated for each experiment.

(3) Some experiments are only repeated once (fiber assays) or twice (cell cycle analysis by flow cytometry). These experiments need to be repeated 3 times and the proper statistical analysis performed (comparison of the medians). 

Superplots with biological replicates for all DNA fiber assays are now displayed. The number of biological replicates is now indicated in the legends and appropriate statistical analyses are used.

Other minor points or suggestions: 

(1) Analyzing fork asymmetry would further support the direct effect of BKC on DNA polymerases. 

The effect of BKC on fork asymmetry is now shown in Fig. 2F. 

(2) A dose dependent analysis of BKC on the speed of DNA replication would also support this point. 

Superplots of DNA fiber assays showing the effect of different concentrations of BKC on fork speed from three biological replicates are now included in Fig. 2E.

(3) Page 7: BKC reduces fork speed ...two-fold. This sentence is not very clear, it would be better to say that speed is half of the control. 

This sentence was changed to “BKC reduced fork speed by a factor of two relative to untreated cells”.

(4) Figure 4G and S4D show contradictory results regarding the induction of Rad51 foci by IBC treatment. This needs to be clarified. 

Figure 4G and S4D (now Fig. 5G and S5D) do not show contradictory results. In both cases, IBC treatment impaired the induction of RAD51 foci by IR or bleomycin.  

(5) Page 12, Figure S5C is called for but it does not exist (probably meaning Figure S5B). 

We apologize for this error, which has now been corrected.  

Reviewer #1 (Significance): 

The work by Coquel et al. aims at elucidating the use of BKC and IBC as a combined therapy to induce cell death in cancer cells by targeting DNA replication and CHK2. Both BKC and IBC have been previously shown to affect the proliferation of cancer cells. BKC has been shown to induce S phase arrest in an ATR dependent manner in MCF7 cells (Li et al., 2016 Front Pharm), while IBC induces cell death in MDA-MB-231 cells (Wu et al., 2022 Molecules). In this regard, the more interesting contribution of the manuscript is the potential identification of the targets of these compounds in cancer cells. The inhibition of CHK2 by IBC is quite compelling although it needs to be further proven. In contrast, the hypothesis that BKC inhibits DNA polymerases remains highly speculative. The results offer a limited advance in the knowledge of the mechanism of action of these two compounds. Focusing on the action of IBC on CHK2 would increase the impact of the results. In this sense a very recent report has been published showing that IBC inhibits SIRT2 (Ren et al., 2024 Phyto Res), showing that IBC can affect multiple enzymes and processes. This should be taken into account for a further analysis of its mechanism of action. 

In addition to the identification of the targets of BKC and IBC, the authors also focus on their combination for cancer treatment. This is based on the idea that blocking the DSB repair and inducing replication stress at the same time is an efficient approach to induce cancer cell death. This is not a new concept, since the loss of ATM sensitizes cancer cells to the inhibition of the replication stress response and several combination therapies have been put forward with the idea of generating replication stress and preventing the subsequent repair of the double strand breaks induced in these cells. Thus, the novelty here is limited, especially considering that the effect of BKC on DNA replication has already been described. Further, since its mechanism of action is unclear, it is difficult to ascribe the observed synergy to the speculated hypothesis. A deeper analysis of IBC as a CHK2 inhibitor would be more interesting, and the potential combination with other chemotherapy agents such as replication stress inhibitors, HU or DNA damaging agents. Also, the lack of a good control of non-transformed cells also reduces the relevance of the work. 

In its current state, the interest of the manuscript is limited. The mechanistical advance is not strong enough and is not completely supported by the data, and the use of these compounds as a combination therapy does not provide new insights in cancer treatment. In my opinion, focusing on the inhibition of CHK2 by IBC and its potential use would broaden the impact of the results beyond the mere analysis of the action of these compounds. 

We thank this reviewer for his/her constructive and insightful comments. We have followed his/her advice and focused our analysis on the action of IBC on CHK2. Using CETSA, we confirmed that IBC binds CHK2 to the same extent as BML-277 inhibitor, but does not bind CHK1. We also show that IBC inhibits BRCA1 phosphorylation on S988 and CHK2 phosphorylation on S516. Together with the results presented in the initial version of the manuscript, these data support the view that CHK2 is a key IBC target. We have also applied CETSA to DNA polymerases and confirmed that BKC directly targets DNA Polδ and ε. Although it is unlikely that IBC and BKC will ever be used in combination therapies, the synergistic effect that we measured on cancer cells in vivo and in vitro indicates that IBC sensitizes cancer cells to endogenous replication stress and to exogenous sources of DNA damage, which could be used to replace BKC in combination therapies. For instance, our data indicate that IBC can be used in combination with drugs such as etoposide, doxorubicin or cyclophosphamide to potentiate their effect on drug-resistant lymphoma cell lines (DLBCL). As requested by this Reviewer, we have modified the discussion section to put more emphasis on IBC and CHK2 inhibitors and we hope that he/she will now find this revised version suitable for publication.

Reviewer #2 (Evidence, reproducibility and clarity): 

In the manuscript by Coquel et al., the authors report their findings on the effect of 2 natural compounds from Psoralea corylofolia plant extracts on cancer cells. They show that these compounds, bakuchiol (BKC) and isobavachalcone (IBC), inhibit proliferation of cancer cells and tumor development in xenografted mice, particularly when used in combination. They further show that BKC inhibited DNA polymerases and induced replication stress, and show evidence that IBC inhibits Chk2 kinase activity and downstream double-strand break repair. Based on their findings, the authors conclude that Chk2 inhibition and DNA replication inhibition represent a potential synergistic strategy to selecting target cancer cells. 

Major: 

(1) The data showing IBC is a Chk2 inhibitor is weak and more rigorous investigation is needed to establish this compound as a Chk2 inhibitor. 

As indicate in our response to Reviewer #1, we have now analyzed the binding of IBC to CHK2 using the Cellular Thermal Shift Assay (CETSA) in MCF-7 cells. Our data clearly show that IBC binds to CHK2 but not CHK1. These results are now shown in Fig. 4G and 4H.

For one, the authors mention they screened 43 cell cycle-related kinases in vitro, but only show data for 8 kinases in their kinase activity screens. Of these 8 kinases, Chk2 is the most strongly inhibited, but there are no data shown for the other 35 kinases. 

Data for all the protein kinases tested in the in vitro assay are now presented in Fig. S4D and S4E.  

Additionally, the purpose of the CHK2 mutants should be discussed in the text. 

The CHK2(I157T) mutation is linked to an increased risk of breast and colorectal cancers. CHK2(R145W) is associated with Li-Fraumeni Syndrome. Both mutations do not affect the basal kinase activity of CHK2. This information is now indicated in the legend of Fig. S4D. 

Secondly, the western blot in Fig 3B, appears to show a very modest effect of IBC on Chk2 autophosphorylation and not that different from the effect of IBC on Akt phosphorylation in Fig S3a. Yet, the authors claim that IBC inhibits Chk2 but not Akt. To strengthen these blots, a known Chk2 inhibitor, such as the one shown in Fig 4 (BML-277) should be included as a positive control for pChk2 similarly to what was shown for Akt with MK-2206. 

We have now replaced the western blot in Fig. 3B (now Fig. 4B) with another biological replicate. Quantifications and statistical analyses of biological replicates are shown in Fig. S4G. Overall, we observed a 50% reduction of CHK2 auto-phosphorylation in MCF7 cells treated with IBC, and a 20% reduction in AKT phosphorylation (Fig. S4A). There was no additional reduction in AKT phosphorylation when cells were treated with IBC in combination with MK-2206, compared to cells treated with MK-2206 alone. We now include the CHK2 inhibitor BML-277 as a positive control alongside with IBC to monitor CHK2 and CHK1 auto-phosphorylation in Fig. 4B, S4G, 4D and S4I, respectively.

Western blots showing a loss of phosphorylation of additional Chk2 targets is also needed. The manuscript mentions Brca1 S988 as a Chk2 substrate important for DSB repair. Showing the effect of IBC on this phosphorylation site would strengthen the conclusions. 

We now provide evidence that IBC inhibits BRCA1 phosphorylation at S988. Western blots and quantification for three biological replicates are shown in Fig. 4C and S4H. 

(2) The authors claim that the combination of IBC and BKC inhibit cell growth in a synergistic manner and that the "effect is more pronounce on cancer cells than on non-cancer cells." However, only 1 non-malignant cell line was used, and it was a fibroblast line. To make this claim, the authors need to show the effect in additional non-malignant cells, preferably with epithelial cell types. 

We have now monitored cell proliferation using the WST-1 assay in two additional non-malignant cell lines, namely MCF-10A and RPE-1 cells. Cells were treated with IBC/BKC and their growth was compared to that of MCF-7 cells. These experiments yielded similar results to those obtained with BJ fibroblasts. These new data are now included in the revised version as Fig. S1A and S1B. 

Minor: 

(1) Densitometry data for all western blots should be shown with mean+/- stdev of independent western blots. 

Densitometry data for all western blots with biological replicates are now shown in supplementary figures.

(2) In Figure 1B the statistical test used to analyze cell number was not stated. 

The statistical test is now indicated in Fig. 1B.

(3) In Figure 2A, the DAPI image for BKC is the merged image and should be replaced with just DAPI. 

This error has now been corrected.

(4) In Figure 2B, the y-axis label says "yH2AX foci (MFI)". MFI and foci are not the same thing, and for yH2AX, the signal is often not focal. MFI of yH2AX is an appropriate measurement for replication stress, it's just not appropriate to equate MFI to foci. 

We apologize for this labeling error, which has now been corrected.

(5) For the 53BP1 MFI and Rad51 MFI shown in Fig 4 and Fig S4, it is more appropriate to show the number of foci/cell as these are better indicators of breaks and repair sites. MFI is influenced by expression levels of the proteins and not necessarily the break/repair. 

The numbers of 53BP1 and RAD51 foci are now shown.

(6) The data in Figures 5B and 5C are very difficult to read. Perhaps color-coat the lines/symbols. 

We have now colored the graph to increase its readability. 

Reviewer #2 (Significance): 

The findings reported in this manuscript are timely, of interest to the field, and are mostly wellsupported by the experimental data. However, there are a few concerns that need to be addressed. 

We are grateful to Reviewer #2 for his positive assessment of our manuscript. We hope that we have adequately addressed all of his/her specific concerns and that he/she will agree with the need to put more emphasis on IBC and CHK2 inhibition as requested by Reviewer #1.

Reviewer #3 (Evidence, reproducibility and clarity): 

The manuscript: "Synergistic effect of inhibiting CHK2 and DNA replication on cancer cell growth" successfully demonstrates that the compounds BKC and IBC found in Psoralea corylifolia act synergistically to inhibit cancer cell proliferation, using a wide range of well-chosen methodologies. Moreover, the authors characterized the mechanisms of action of both drugs, which result in inhibition of cell proliferation. The use of multiple cell lines and the mice models makes the study robust and complete. The manuscript presents a well written study that offers new insights and contributions to the field. 

A few suggestions to improve the study: 

(1) Given that both compounds BKC and IBC have already been previously described in the literature, it would be helpful for the reader to have them described better at the beginning of the study. 

Thanks for pointing this out. We have now better described BKC and IBC at the beginning of the results section, as well as in the discussion. We agree that this could be helpful to readers.

(2) Addition of western blot quantifications over the number of experimental repeats is important specifically for Fig. 2C and Fig. 3C where partial effect of treatment on a signal level is reported. 

The densitometry analysis of data shown in Fig. 2C and biological replicates are now shown in Fig. S2B. Quantification for Fig. 3C (now Fig. 4D) is shown in Fig. S4I.

(3) The quantification of mean intensity for 53BP1 and RAD51 foci should be exchanged with the quantification of number of foci per cell. While the quantification of gH2AX signal intensity is a correct representation of induction of this signal upon damage, foci formed by protein recruitment to DNA damage sites should be quantified by counting the number of foci, rather than signal in the whole cell/nucleus. These proteins exist before damage and are re-located in response to the damage. 

Quantification of 53BP1 and RAD51 foci is now expressed as the number of foci per cell. 

(4) Materials & Methods section is missing the methods for the experiment described in Fig. 1B. In summary, after addressing our few concerns, we believe the manuscript should be accepted for publication. 

The WST-1 assay used for cell number quantification is included in “Reagents” in Material & Methods section.

Reviewer #3 (Significance):

The manuscript presents a well written study that offers new insights and contributions to the field. Although the inhibitors described have been known in science, the authors present convincingly their mode of action, which is either better characterized (for BKC) or inhibiting a different than previously suggested enzyme (for IBC). Authors also nicely pinpoint and explain the narrow window of concentrations when these two compounds act synergistically rather than additively. The analyses in multiple cell lines, mouse models and in combination with other cancer treatments, makes this study of interest not only for fundamental researchers but also for translational scientists and industry.

My field of expertise: DNA replication and replication stress across model systems. 

We are grateful to Reviewer #3 for his/her very positive assessment of our work and we hope that he/she will find this revised version suitable for publication.

Author response:

Reviewer #1: 

Summary:

Ngo et. al use several computational methods to determine and characterize structures defining the three major states sampled by the human voltage-gated potassium channel hERG: the open, closed, and inactivated state. Specifically, they use AlphaFold and Rosetta to generate conformations that likely represent key features of the open, closed, and inactivated states of this channel. Molecular dynamics simulations confirm that ion conduction for structure models of the open but not the inactivated state. Moreover, drug docking in silico experiments show differential binding of drugs to the conformation of the three states; the inactivated one being preferentially bound by many of them. Docking results are then combined with a Markov model to get state-weighted binding free energies that are compared with experimentally measured ones.

Strengths:

The study uses state-of-the art modeling methods to provide detailed insights into the structure-function relationship of an important human potassium channel. AlphaFold modeling, MD simulations, and Markov modeling are nicely combined to investigate the impact of structural changes in the hERG channel on potassium conduction and drug binding.

We appreciate the reviewer’s recognition of our integration of state-of-the-art computational methods, including AlphaFold2, Rosetta, MD simulations, and Markov modeling. We are pleased that the reviewer found our approach to investigating the structure-function relationship of the hERG channel insightful.

Weaknesses:

(1) The selection of inactivated conformations based on AlphaFold modeling seems a bit biased. The authors base their selection of the "most likely" inactivated conformation on the expected flipping of V625 and the constriction at G626 carbonyls. This follows a bit of the "Streetlight effect". It would be better to have selection criteria that are independent of what they expect to find for the inactivated state conformations. Using cues that favour sampling/modeling of the inactivated conformation, such as the deactivated conformation of the VSD used in the modeling of the closed state, would be more convincing. There may be other conformations that are more accurately representing the inactivated state. I see no objective criteria that justify the non-consideration of conformations from cluster 3 of the inactivated state modeling. I am not sure whether pLDDT is a good selection criterion. It reports on structural confidence, but that may not relate to functional relevance.

We acknowledge the concern regarding the selection criteria for the inactivated state models. In the revised manuscript version, we plan to broaden our selection approach and explicitly include conformations from different clusters beyond those highlighted in the initial submission (e.g., from cluster 3). We will also incorporate structural metrics that do not solely depend on the known channel inactivation hallmarks or reply on the pLDDT scores to further justify our chosen representative inactivated state models.

(2) The comparison of predicted and experimentally measured binding affinities lacks an appropriate control. Using binding data from open-state conformations only is not the best control. A much better control is the use of alternative structures predicted by AlphaFold for each state (e.g. from the outlier clusters or not considered clusters) in the docking and energy calculations. Using these docking results in the calculations would reveal whether the initially selected conformations (e.g. from cluster 2 for the inactivated state) are truly doing a better job in predicting binding affinities. Such a control would strengthen the overall findings significantly.

We agree that a more rigorous control for our drug-binding predictions is desirable. To address this, we will include molecular docking simulations and associated drug binding affinity estimations for more hERG channel models, including alternate conformations from the initial clustering that were not chosen as the final models. This will allow us to test whether our inactivated state structure from cluster 2 indeed outperforms or differs significantly from other possible inactivated hERG channel conformations in reproducing experimental drug potencies.

(3) Figures where multiple datapoints are compared across states generally lack assessment of the statistical significance of observed trends (e,g. Figure 3d).

(4) Figure 3 and Figures S1-S4 compare structural differences between states. However, these differences are inferred from the initial models. The collection of conformations generated via the MD runs allow for much more robust comparisons of structural differences.

We will incorporate statistical analyses and measures of uncertainty for key comparisons. In Figures 3 and S1-S4 the consensus structural hERG channel models for open, inactivated and closed states are being compared, i.e. one representative model for each state. We believe this is a valid comparison, and the statistical analysis of the observed trends based on those models (e.g., in the bar plot of Figure 3d) alone might not be possible. However, we agree with the reviewer that instead of relying solely on those initial static models, we will also draw on the ensemble of states sampled during the MD simulations to quantify structural differences between different putative hERG channel states. Specifically, we will present ensemble-averaged measurements and highlight how these distributions differ significantly between states.

Reviewer #2:

Summary:

Ngo et al. use AlphaFold2 and Rosetta to model closed, open, and inactive states of the human ion channel hERG. Subsequent MD simulations and comparisons with experiments support the plausibility of their models.

Strengths:

This is thorough work studied from many different angles. It provides a self-consistent picture of how conformational changes in hERG may affect its function and binding to different targets.

We are grateful for the reviewer’s recognition of the thoroughness and multi-faceted nature of our study.

Weaknesses:

Though this work claims the methodologies can be generalized to other systems, it is not obvious how. Many modeling choices seem arbitrary and also seem to have required extensive expert knowledge of the system. This limits the applicability of the modeling strategy.

We appreciate the reviewer’s comment on the generalizability of our approach. In the revision, we will more explicitly discuss the rationale behind the modeling choices and the extent to which they reflect system-specific knowledge. We will clarify how the strategies we developed (e.g., iterative refinement with AlphaFold2 and Rosetta, followed by MD simulation validation) can be adapted to other ion channels or related proteins. We will also outline a more generalizable workflow, specifying which steps require system-specific information and which steps are broadly applicable.

Reviewer #3:

Summary:

The authors use Alphafold2, Rosetta, and Molecular Dynamics to model structures of the hERG K channel in open, inactive, and closed states. Experimental CryoEM data for open hERG (Wang and Mackinnon 2017), and closed EAG (Mandala and Mackinnon, 2002) were used as the main templates for channel models presented here. Given the importance of hERG as a safety pharmacology target, the identification of a robust simulation method to assess drug block is an important addition to the field.

Strengths

The key findings here are new inactivated and closed hERG channel conformations and hERG channel conformations with drugs docked in the inner vestibule below the selectivity filter. Amino acid pathways and interaction networks for different states are also presented.

The inactive state and drug block models are carefully correlated with experimental data for the inactivated state of hERG (Lau et al, 2024) and with experimental free energy data for drug binding and have overall good agreement.

It is remarkable that using cytoplasmic domain structures of hERG as a starting point revealed inactivation state structures in the hERG selectivity filter in Figures 2,3.

We thank the reviewer for highlighting the novelty and importance of our work, particularly regarding the identification of new inactivated and closed hERG channel conformations and the modeling of drug block. We are also pleased that the reviewer found the correlation with experimental data to be strong and the structural insights to be valuable.

Weaknesses

Figure 6, if each data point is for a different drug, then perhaps identify each point.

Thank you so much for this suggestion. Please note that Table 3 contains drug-specific data plotted in Figure 6 including drug names. We will provide a reference to Table 3 in the revised Figure 6 caption. We will also revise Figure 6 (and any similar figures) to clearly identify each data point with the corresponding drug and/or include a corresponding key in the Figure legend. This will make it easier to correlate each data point’s binding prediction with the experimental datasets.

The PAS domain was not included in the models as stated in Methods page 14 but the PAS does appear in some of the templates used as starting points for models in Figure 1 a,b,c. Perhaps mentioning that the PAS was not included in some (all?) of the final models should be moved into the main text and discussed.

The drug block of 1b channels (which do not contain PAS) has been reported to be slightly different than that for 1a channels (which contain PAS) and for 1a/1b channels (see London et al., 1997; https://doi.org/10.1161/01.RES.81.5.870 and Abi-Gerges et. al., 2011; DOI: 10.1111/j.1476-5381.2011.01378.x) and this should be discussed since the models presented here appear to be performed in the absence of the PAS.

It also appears that the N-linker region (between PAS and the S1) and distal C region of hERG (post CNBHD-COOH) are not included in models, please state this if correct, and discuss.

We appreciate the reviewer’s insightful comment regarding the PAS domain and the potential influence of other regions, such as the N-linker and distal C-region, on hERG channel drug binding and state transitions.

The PAS domain did appear in the starting templates used for initial structural modeling (as shown in Figure 1a, b, c), but it was not included in the final models used for subsequent analyses. Similarly, the N-linker and the distal C-region were also omitted from the final models. These omissions were primarily due to hardware constraints used for AlphaFold structural modeling, as including these additional protein regions would exceed the memory capacity of graphical processing unit (GPU) cards on our available intramural, external and cloud high-performance computing resources, leading to failures during the protein structure prediction step.

The PAS domain of hERG 1a isoform, even if not serving as a direct drug-binding site, can influence the gating kinetics of hERG channels as the reviewer pointed out. By altering the probability and duration with which those ion channels occupy specific conformational states, it can indirectly affect how well drugs bind. For example, if the presence of the PAS domain shifts channel gating so that more channels enter (and remain in) the inactivated state, drugs with a higher affinity for that state would appear to bind more potently, as observed in electrophysiological experiments. It is also plausible that the PAS domain could exert allosteric effects that alter the conformational landscape of the ion channel during gating transitions, potentially impacting drug accessibility or binding stability. This is an intriguing hypothesis and an important avenue for future research.

With access to more powerful computational resources, it would be valuable to explore the full-length hERG 1a channel, including the PAS domain and associated regions, to assess their potential contributions to drug binding and gating dynamics. We will incorporate a discussion of these points into the main text, acknowledging the limitations of our current models, citing the references provided by the reviewer, and highlighting the need for future studies to explore these protein regions in greater detail.

Author response:

Response to Reviewer 1

We will investigate the intracellular localization of ABCA1 in both EpH4 and EpH4-Snail cells. We will also examine the changes in ACAT expression levels within these cell lines.

Response to Reviewer 2

We will first investigate whether the chemoresistance exhibited by EpH4-Snail cells can be abolished not only through pharmacological inhibition of ABCA1 but also by knocking out the ABCA1 gene. Regarding causality, as demonstrated in Figure 2, we have already shown that reducing cholesterol levels in EpH4-Snail cells decreases ABCA1 expression. To further explore this relationship, we will assess whether increasing sphingomyelin levels by adding ceramide to the culture medium, thereby correcting the sphingomyelin-to-cholesterol ratio, would reduce ABCA1 expression. Furthermore, we will evaluate whether lowering cholesterol levels in EpH4-Snail cells via simvastatin treatment, along with normalization of the sphingomyelin-to-cholesterol ratio, attenuates their resistance to the anticancer drug nitidine chloride. Additionally, we will incorporate quantitative analyses for several experiments, as suggested in the reviewers’ comments, to enhance the robustness of our findings.

Author response:

The following is the authors’ response to the original reviews.

Overall authors’ response

We would like to thank the 3 reviewers for a thorough critique of our manuscript, and acknowledging the novelty and importance of our studies, in particular the relevance to collagenrelated pathologies such as idiopathic pulmonary fibrosis and chronic skin wound. We appreciate that there are shortcomings in these studies, as highlighted by reviewers; we have rewritten parts of our manuscript to clarify any misunderstandings, and conducted additional experiments to address concerns raised by reviewers (please see below red text within each response), which have been incorporated into our revised manuscript (modified text highlighted in yellow in revised manuscript). We believe that the revision had made our manuscript stronger in support of our original conclusions. 

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors describe that the endocytic pathway is crucial for ColI fibrillogenesis. ColI is endocytosed by fibroblasts, prior to exocytosis and formation of fibrils, which can include a mixture of endogenous/nascent ColI chains and exogenous ColI. ColI uptake and fibrillogenesis are regulated by circadian rhythm as described by the authors in 2020, thanks to the dependence of this pathway on circadian-clock-regulated protein VPS33B. Cells are capable of forming fibrils with recently endocytosed ColI when nascent chains are not available. Previously identified VPS33B is demonstrated not to have a role in endocytosis of ColI, but to play a role in fibril formation, which the authors demonstrate by showing the loss of fibril formation in VPS33B KO, and an excess of insoluble fibrils - along-side a decrease in soluble ColI secretion - in VPS33B overexpression conditions. A VPS33B binding protein VIPAS39 is also shown to be required for fibrillogenesis and to colocalise with ColI. The authors thus conclude that ColI is internalised into endosomal structures within the cell, and that ColI, VPS33B, and VIPA39 are co-trafficked to the site of fibrillogenesis, where along with ITGA11, which by mass spectrometric analysis is shown to be regulated by VPS33B levels, ColI fibrils are formed. Interestingly, in involved human skin sections from idiopathic pulmonary fibrosis (IPF) patients, ITGA11 and VPS33B expression is increased compared to healthy tissue, while in patient-derived fibroblasts, uptake of fluorescently-labelled ColI is also increased. This suggests that there may be a significant contribution of endocytosis-dependent fibrillogenesis in the formation of fibrotic and chronic wound-healing diseases in humans. 

Strengths: 

This is an interesting paper that contributes an exciting novel understanding of the formation of fibrotic disease, which despite its high occurrence, still has no robust therapeutic options. The precise mechanisms of fibrillogenesis are also not well understood, so a study devoted to this complex and key mechanism is well appreciated. The dependence of fibrillogenesis on VPS33B and VIPA39 is convincing and robust, while the distinction between soluble ColI secretion and insoluble fibrillar ColI is interesting and informative. 

Weaknesses: 

There are a number of limitations to this study in its current state. Inhibition of ColI uptake is performed using Dyngo4a, which although proposed as an inhibitor of Clathrin-dependent endocytosis is known to be quite un-specific. This may not be a problem however, as the endocytic mechanism for ColI also does not seem to be well defined in the literature, in fact, the principle mechanism described in the papers referred to by the authors is that of phagocytosis.

We thank the reviewer for pointing this out. Macropinocytosis or phagocytosis could be modelled using high molecular weight dextran, and we have used fluorescently-labelled dextran to investigate potential co-localisation with exogenous collagen to investigate the involvement of these mechanisms in addition to endocytosis, and showed very little co-localisation (revised Figure S2B, lines 123-126). Further, we have performed a competition experiment where unlabelled collagen was added in excess at the same time as labelled collagen and showed that excess unlabelled collagen led to a retention of labelled collagen at the cell periphery (revised Figure S2C, lines 126-129). This is suggestive of collagen-I uptake utilises a different pathway to dextran (i.e. fluid-phase endocytosis) and is a receptor-mediated process.  

It would be interesting to explore this important part of the mechanism further, especially in relation to the intracellular destination of ColI.

We agree with the reviewer that the intracellular destination of ColI is very interesting, which is what the current Chang lab is investigating, although we believe the research findings fall out of scope for the revised manuscript here. However, we have included additional immunofluorescence data to support that collagen is indeed taken up into endosomal compartments using GFP-tagged Rab5 constructs (revised Figure 1D, Figure S6A).

The circadian regulation does not appear as robust as the authors' last paper, however, there could be a larger lag between endocytosis of ColI and realisation of fibrils.

The authors state that the endocytic pathway is the mechanism of trafficking and that they show ColI, VPS33B, and VIPA39 are co-trafficked. However, the only link that is put forward to the endosomes is rather tenuously through VPS33B/VIPA39.

We would like to clarify that we meant the post-Golgi compartment. We did not mean VPS33b/VIPAS39 as an endosome marker; however as we see collagen entering the cell in intracellular compartments, which is then recycled, we take that as convention, the endosome would be involved. This is further supported that we see some colocalisation with the classic Rab5 endosome marker.

There is no direct demonstration of ColI localisation to endosomes (ie. immunofluorescence), and this is overstated throughout the text.

We appreciate the comment and have modified overstatements in the revised manuscript as appropriate. As stated above, we have included additional immunofluorescence data to support that collagen is indeed taken up into endosomal compartments.

Demonstrating the intracellular trafficking and localisation of ColI, and its actual relationship to VPS33B and VIPA39, followed by ITGA11, would broaden the relevance of this paper significantly to incorporate the field of protein trafficking. Finally, the "self-formation" of ColI fibrils is discussed in relation to the literature and the concentration of fluorescently-tagged ColI, however as the key message of the paper is the fibrillogenesis from exocytosed colI, I do not feel like it is demonstrated to leave no doubt. Specific inhibition of intracellular trafficking steps, or following the progressive formation of ColI fibrils over time by immunofluorescence would demonstrate without any further doubt that ColI must be endocytosed first, to form fibrils as a secondary step, rather than externally-added ColI being incorporated directly to fibrils, independent of cellular uptake.

We appreciate the concern raised here. This is precisely why we trypsinised and replated cells as part of the workflow, so we can make sure that there is no residual exogenous collagen which is not endocytosed being incorporated onto pre-existing fibrils. We have new data using flow imaging, which showed that cells that don’t endocytose exogenous collagen has accumulation of said collagen at the periphery of the cells, which is greatly reduced after trypsinisation. This new data is in a more detailed methodology-based study which is under preparation, which will allow future studies to further dissect the collagen intracellular trafficking process, and thus is not included in the revised manuscript. 

Reviewer #2 (Public Review): 

Summary: 

In this manuscript, the authors describe a mechanism, by which fluorescently-labelled Collagen type

I is taken up by cells via endocytosis and then incorporated into newly synthesized fibers via an ITGA11 and VPS33B-dependent mechanism. The authors claim the existence of this collagen recycling mechanism and link it to fibrotic diseases such as IPF and chronic wounds. 

Strengths: 

he manuscript is well-written, and experimentally contains a broad variation of assays to support their conclusions. Also, the authors added data of IPF patient-derived fibroblasts, patient-derived lung samples, and patient-derived samples of chronic wounds that highlight a potential in vivo disease correlation of their findings. 

The authors were also analyzing the membrane topology of VPS33B and could unravel a likely 'hairpin' like conformation in the ER membrane. 

Weaknesses: 

Experimental evidence is missing that supports the non-degradative endocytosis of the labeled collagen.

We thank the reviewer for raising this. We would like to clarify that we do not think that all endocytosed collagen-I is recycled, but rather sorted in the endosome which determines the fate of endocytosed collagen. Interestingly, results from Kadler’s group has shown that blocking lysosome function (through chloroqine and bafilomycin) significantly reduced endogenous collagen fibril formation (https://www.biorxiv.org/content/10.1101/2024.05.09.593302v1), suggesting a nondegradative role for lysosome in fibrillogenesis.   

The authors show and mention in the text that the endocytosis inhibitor Dyngo®4a shows an effect on collagen secretion. It is not clear to me how specific this readout is if the inhibitor affects more than endocytosis. This issue was unfortunately not further discussed.

We thank the reviewer for this comment and have included in discussion the specificity of Dyngo4a (revised manuscript lines 383392). The ponceau stain suggests that Dyngo4a treatment did not affect global secretion and thus the effects are specific to collagen-I (Fig 2B).

The authors use commercial rat tail collagen, it is unclear to me which state the collagen is in when it's endocytosed. Is it fully assembled as collagen fiber or are those single heterotrimers or homotrimers?

We apologise for the confusion and will clarify in our revision. These would be single helical trimers from acid-extracted rat tail collagen. We have performed additional light scattering and CD spectra to confirm the molecular weight and helicity, and confirm that adding fluorescent tags did not alter the readout. We have included this in the revised manuscript (revised Figure S1A-C, manuscript lines 82-86).    

The Cy-labeled collagen is clearly incorporated into new fibers, but I'm not sure whether the collagen is needed to be endocytosed to be incorporated into the fibers or if that is happening in the extracellular space mediated by the cells.

We appreciate the concern raised here, which is also raised by reviewer 1. As answered above, this is why we trypsinised and replated cells as part of the workflow, so we can make sure that there is no residual exogenous collagen being incorporated onto pre-existing fibrils. We also have new data using flow imaging, which shows that cells that don’t endocytose exogenous collagen has accumulation of said collagen at the periphery of the cells, which is greatly reduced after trypsinisation. This new data is in a methodology-based manuscript which is under preparation, thus will not be included in the revised manuscript.  

In general for the collagen blots, due to the lack of molecular weight markers, what chain/form of collagen type I are you showing here?

Apologies for the lack of molecular weight markers, it was an oversight by the authors and have been included in the revised figures.  

Besides the VPS33B siRNA transfected cells the authors also use CRISPR/Cas9-generated KO. The KO cells do not seem to be a clean system, as there is still a lot of mRNA produced. Were the clones sequenced to verify the KO on a genomic level?

Yes, the clones were verified and used in our previous paper on circadian control of collagen homeostasis. There are instances where despite knockout at the protein level, mRNA is still persistent; however these transcripts are likely then directed to degradation through nonsense-mediated mRNA decay. To fully understand this mechanism is beyond the scope of this paper. 

For the siRNA transfection, a control blot for efficiency would be great to estimate the effect size. To me it is not clear where the endocytosed collagen and VPS33B eventually meet in the cells and whether they interact. Or is ITGA11 required to mediate this process, in case VPS33B is not reaching the lumen?

This is an interesting question. We have conducted experiments with Col1-GFP11 containing conditioned media incubated with VPS33b-barrell in the revised paper, which showed that they interact within the cell and not at the cell periphery (revised Figure 6G, lines 293-296), again highlighting that VPS33b is not involved in the endocytosis step but interacts with endocytosed collagen-I intracellularly. We have attempted colocliasation studies using the split GFP approach with VPS33B and ITGA11 to investigate where they interact, but as the ITGA11 construct we used did not localise to the cell surface as expected, we are not confident that this system is appropriate for investigating how/if VPS33B interacts with ITGA11, and there are simply no good antibody for VPS33B for staining. 

The authors show an upregulation of ITGA11 and VPS33B in IPF patients-derived fibroblasts, which can be correlated to an increased level of ColI uptake, however, it is not clear whether this increased uptake in those cells is due to the elevated levels of VPS33B and/or ITGA11.

We would like to clarify here that we do not think collagen-I uptake is due to VPS33B and/or ITGA11, as siITGA11 and VPS33B in fibroblasts showed no consistent changes in uptake as determined by flow cytometry, which was included in the original manuscript (now revised Figure 6H, 7I). VPS33B and ITGA11 are involved in the ‘outward’ arm of recycled collagen-I, i.e. directing to fibrillogenesis route. We agree that the inclusion of additional functional studies using IPF patient-derived patient fibroblasts would add to the manuscript, and have performed siRNA against VPS33B and ITGA11 on IPF fibroblasts, and demonstrated a late of endocytic recycling events (revised Figure 8D, S6B, lines 351-353).  

Reviewer #3 (Public Review): 

Summary: 

Chang et al. investigated the mechanisms governing collagen fibrillogenesis, firstly demonstrating that cells within tail tendons are able to uptake exogenous collagen and use this to synthesize new collagen-1 fibrils. Using an endocytic inhibitor, the authors next showed that endocytosis was required for collagen fibrillogenesis and that this process occurs in a circadian rhythmic manner. Using knockdown and overexpression assays, it was then demonstrated that collagen fibril formation is controlled by vacuolar protein sorting 33b (VPS33b), and this VPS33b-dependent fibrillogenesis is mediated via Integrin alpha-11 (ITGA11). Finally, the authors demonstrated increased expression of VPS33b and ITGA11 at the gene level in fibroblasts from patients with idiopathic pulmonary fibrosis (IPF), and greater expression of these proteins in both lung samples from IPF patients and in chronic skin wounds, indicating that endocytic recycling is disrupted in fibrotic diseases. 

Strengths: 

The authors have performed a comprehensive functional analysis of the regulators of endocytic recycling of collagen, providing compelling evidence that VPS33b and ITGA11 are crucial regulators of this process. 

Weaknesses: 

Throughout the study, several different cell types have been used (immortalised tail tendon fibroblasts, NIHT3T cells, and HEK293T cells). In general, it is not clear which cells have been used for a particular experiment, and the rationale for using these different cell types is not explained. In addition, some experimental details are missing from the methods.

We thank the reviewer for pointing out the lack of clarity, and have filled in missing information in the methods. HEK293T cells were used for virus production for the VPSoe system, and we have clarified the cell types used in figure legends (predominantly iTTF). We have also provided justification when NIH3T3 cells were used (revised lines 290-291).    

There is also a lack of functional studies in patient-derived IPF fibroblasts which means the link between endocytic recycling of collagen and the role of VPS33b and ITGA11 cannot be fully established.

We thank the reviewer for this comment, which was also raised by reviewer 2 above. We agree that the inclusion of additional functional studies using IPF patient-derived patient fibroblasts would add to the manuscript and have performed siRNA against VPS33B and ITGA11 on IPF fibroblasts, and demonstrated a late of endocytic recycling events (revised Figure 8D, S6B, lines 351-353).  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

The authors inhibit Clathrin-dependent endocytosis with dyngo4a. It is well known that this inhibitor is not highly specific for this pathway. It is also not explained why the authors only inhibit the Clathrin uptake pathway, and not pinocytosis or Clathrin-independent endocytosis too. The authors refer to papers that describe pinocytosis for collagen endocytosis.

We thank the reviewer for raising this question. Based on the fact that inhibition of clathrin-dependent pathway does not completely abrogate endocytosis of collagen-I, we anticipate that other pathways are involved in mediating collagen-I uptake, although additional data suggested this is unlikely through fluid-phase endocytosis, and is receptor mediated (revised Figure S2B, C).  

Where does the ColI go in the cell? Depending on the uptake pathway, it is likely to pass through endocytic carriers to endosomes, where it may be recycled to the PM or degraded. From the start, the authors describe the ColI as being in vesicular structures, however, the imaging data that this is based on is not co-labelled with anything to determine the potential structure/localisation. This is not done at any point in the paper, until IF is shown of ColI with VIPA39, however without the relevant controls, this IF is unconvincing, as the general pattern of ColI and VIPA39 as an endosomal marker are not classically recognisable. Additionally, VPS33B is described as a late endosome/lysosome marker, which would have different connotations on ColI trafficking or destination than other types of endosomes.

We thank the reviewer for pointing out the weaknesses in our original IF. We have included new confocal images showing labelled collagen co-localisation with GFP-tagged Rab5 through transient transfection, which is a more traditional endosome marker (revised Figure 1D, Figure S6A).  

We are currently characterising the compartments to where ColI is trafficked to, which is being prepared as part of a methodology-based manuscript. We believe that this characterisation would be too detailed to be included in a revised version of this manuscript. The Kadler lab also have data suggesting that the lysosome is involved in collagen fibrillogenesis instead of its canonical degradation function, which is in another submitted manuscript (https://www.researchsquare.com/article/rs-1336021/v1). It was not included in this manuscript due to our focus (i.e. endocytic-recycling).   

In Figure 5H, the pattern of Cy5-ColI staining looks like it could even be ER/Golgi in the VPSKO zoom panel, but in the absence of co-labelling, we cannot conclude anything. In order for the authors to conclude that ColI is within the endosomes, co-labelled If should be performed to demonstrate ColIendosomal colocalization. Likewise for the role of VPS33B in ColI fibrillogenesis: dependence of the process is demonstrated, but the relationship is not defined. This could be clarified using IF. This would also support the authors' statements of co-trafficking between ColI, VPS33B, and VIPA39, which as the paper stands, is not demonstrated.

We would like to clarify that our hypothesis is that the endosome controls how collagen is being deposited outside the cell, i.e. whether it’s protomeric secretion or fibrillogenesis, and that the decision of whether an endocytosed collagen is recycled or degraded lies in this compartment. The reviewer is correct that it may not be just the endosome that endocytosed collagen-I ends up in, as we have new data suggesting involvement of other intracellular compartment, although the detailed mechanism is beyond the scope of this manuscript. Nonetheless, we have included new data showing co-localisation of endocytosed collagen with Rab5 in this revised manuscript (revised Figure 1D, Figure S6A).  

The basis of this paper is that endocytosis of ColI must occur before re-exocytosis as fibrillar ColI. The authors show this through pulse-chase experiments, with a trypsinisation step to remove any externally bound ColI. The authors also show nice time progression by flow cytometry, but it would truly demonstrate this point if they showed 0 timepoint, or low timepoint of IF to show progressive lengthening of ColI fibrils. This is used early on in Figure 1D, although the presentation here is not very clear. This is especially important as the authors address the self-seeding capabilities of Collagen in cell-free conditions in Figure 1F.

We would like to thank the reviewer for this suggestion.  From previous endogenously tagged collagen data, we know that the appearance of collagen fibrils is rather rapid, thus it may not be a gradual lengthening as expected, but rather a depletion of endocytosed collagen in the initial seeding/growth step (please see https://www.researchsquare.com/article/rs-1336021/v1). We have included an image of replated fibroblasts after 18 hours showing no appearance of extracellular collagen, endogenous or otherwise (revised Figures S2A, line 110).  

Finally, although the involvement of ITGA11 is interesting, it is not well described, and its role is not well demonstrated. This could likely be clarified by an additional introduction to ITGA11 and its role in collagen exocytosis/fibrillogenesis.

We would like to thank the reviewer for pointing this out and have included additional sentences to specifically introduce ITGA11 and its role in fibrillogenesis (see lines 320, 321; 446-450).  

Specific points: 

Line 73: You haven't compared reuse vs production, so you can't say that reuse is central rather than production. They may be both as important or production still may be the most crucial, maybe it depends on cell/collagen type. Using the ColI KD or CHX to block nascent synthesis, you could directly compare the impact of both.

We would like to clarify that we are not referring to reuse/recycling here. We meant that production of collagen (i.e. single hetero/homotrimer molecules within the cell) is not as crucial as the utilisation (i.e. are these being secreted as protomers, or assembled into fibrils) of these building blocks by the cells, which was supported by our finding that production (as suggested by mRNA levels) of IPF fibroblasts are similar to that in control fibroblasts (now revised Figure 8A). We have conducted ColI siRNA to block nascent synthesis in the original manuscript and showed that fibroblasts can efficiently make new fibrils by recycling exogenous collagen (Figure 3B, C), although we appreciate that siRNA may not completely inhibit endogenous production. Thus, we have also included new data using collagen-I knockout cells to support our hypothesis that without endogenous production, fibroblasts can still effectively make collagen fibrils if they can reuse what is available in the extracellular space (revised Figure 4, Figure S3C, D; lines 178-199).  

Lines 83-87: The rationale for this experiment is not clear. Cy3-ColI is added, taken up into cells, and incorporated into fibrils coming from cells. 5FAM-ColI is added at a later stage, then at 2 days (when incorporation is demonstrated in Fig 1B), it is also incorporated into cells as expected. Why does this comment on ColI not being degraded any more than Cy3-ColI alone?

We believe that the pulse chase experiment using the differently tagged collagen demonstrated a dimension of dynamics that is not demonstrated with Cy3-ColI alone. In this case, Cy3-ColI was initially added, and removed after 3 days; 5FAM-ColI is then added and incubated for 2 more days. Thus after 5 days since the initial pulse, the Cy3-ColI persisted and was not degraded. We would like to apologise for causing this confusion, and have clarified in the revised manuscript (lines 542-549; Figure S1D figure legend).  

Figure 1A: I would like to see a negative control: either dark colI or no Cy3-Col, or timescale. Is B quantified from these images?

We thank the reviewer for this comment. We have added the nocollagen control image in our revision (revised Figure S1D). 1B is not quantified from the ex vivo tendon experiments, but rather the in vitro cell culture experiments (i.e. those from 1D-1F, although they are all from independent experiments).  

Figure 1B: in iTTF cells (immortalised tendon cells) Corrected to max: What does that mean?

As there are variations between individual experiments (e.g. changes in the amount of collagen added due to pipetting) we have normalised to the maximum value obtained in each individual experiments so that we can display all biological repeats within the same graph.  

Figure 1C: You can't say ColI is in vesicular structures from this, they are spots, yes, but that could also be in Golgi/ER (unlikely to be cytosolic but not impossible).

We appreciate this comment and have change the wording accordingly and call them intracellular/punctate structures.

Figure 1D: Not the best presentation: The cell mask has structures: what are these? It's not clear if this is a single cell, would be better with a defined marker (endocytic marker, lysosome etc). Instead of a low-resolution 3D view, it would be clearer with normal confocal XY and zooms of "vesicular structures" using appropriate markers as 3D reconstructions I think it could be removed.

This is a single cell and the cell mask is staining plasma membrane. We didn’t use defined marker as we wanted to visualise the whole intracellular cell compartment. We appreciate that further proof is needed to verify the location of the endocytosed collagen, and have included additional confocal imaging data to support the localisation of collagen into Rab5 positive intracellular compartments (revised Figure 1D, Figure S6B).  

Figure 1 E/F: Cy3 is only visible in extracellular structure, not also intracellular. Why? Would be useful to see the time points of incorporation at the end of the pulse, then at an early point into the chase, to demonstrate 1) Cy3-ColI uptake into cells and progressive incorporation rather than potential direct binding of ColI-Cy3 to ECM, or other non-specific factors. Showing the image at 0t would demonstrate an absence of external labelled colI and therefore its appearance later could be presumed that it had been internalised before.

As the cells were trypsinized and replated after one hour labelled collagen feeding to ensure we are only tracking endocytosed collagen, t=0 in this case would be cells that are unattached. We have included t=18hr images post replate instead to show baseline level of collagen (revised Figures S2A, line 110).

Figure S1A: yellow box: doesn't show only Cy3-ColI, there is red and yellow in the central cell, and large yellow blobs in the cell above. These images do not support this claim, including the Fiber Zoom box. They should also be shown in single channels to demonstrate the authors' points better.

Apologies for the confusion – this is to show that newly added FAM5 Collagen is also co-localising with previously endocytosed Cy3-ColI, i.e. the Cy3-ColI is persisting rather than being degraded.  

Line 92: endocytosed into distinct structures: These images are very vague, but I don't think you can call them distinct structures, all you can say from this is that they are spots.

We have changed the wording to ‘distinct puncta’.  

It is not clear why the authors use Cy3, Cy5, and 5FAM labelled colI. A brief explanation would be useful.

Apologies for the confusion, we initially included our justification (to show that the fluorescence labels do not change the way collagen is internalised) but removed it in the final manuscript due to length. We have added the justification (revised line 101-102).   

Figure 1F: It would be useful to see a quantification of the Cy3 channel here: I agree with the conclusions, and find the 0.5 ug/ml condition more convincing than 0.1 actually, although there is some feint Cy3 in cell-free samples there seems to be quite a big increase in the presence of cells, and this would look more convincing if quantified.

We thank the reviewer for this suggestion and have included quantification in the revised manuscript (revised Figure 1G-I).  

Figure 2B: Dyng is not an abbreviation of Dyng. Standardise Dyng/Dyngo/Dyngo4a. WB is soluble colI and represents little (if any) insoluble col. IF is more or less the other way round. How do they compare this?

Thank you for pointing out the inconsistencies, we have corrected this in the revised manuscript. We took the conditioned media from the same experiment where cells are fixed for IF and carried out Western blot analyses. The IF showed some collagen still present, albeit significantly reduced. This is in agreement with the western blot results (i.e. Dyng4a inhibits both soluble and insoluble forms of collagen deposition).  

Figure 2C: not an image series. Quant: no cells/independent exps and STATS?

Apologies for the missing experimental details in figure legends, it should say ‘representative of N=3 experiments’. We are not sure what the reviewer meant by Figure 2C not being an image series, as we meant it to be an image series of the individual fluorescence channels. We have changed this terminology to avoid confusion, and have included statistical analyses in the methods section. The statistical analyses of the fibril quantification is next to the fluorescence images.  

Figures 2D/E: The authors show that internalised ColI peaks at 20h and decreases to 60h, Fibers peak at 40h. How is this measured? ECM removed? Why would there be less in the cells, degradation? Whats the synchronisation?

We apologise for omitting the synchronisation method in methods section, and have included in our revised manuscript (revised lines 542-544). This is through dexamethasone addition (and removal after 1hr incubation) as standard. The internalised Col-I is measured using Cy3ColI so the cells would have both nascent and external collagen. Total intracellular collagen at the different time points would likely be higher than represented as a result, but here we are demonstrating that internalisation is a rhythmic event using the external labelled collagen. Fibers are measured using standard IF and then fibril counting.  

Please note that we are only overlaying the two graphs to form our hypothesis that endocytosis may be used for accumulation of collagen protomers that then allows for efficient fibrillogenesis. They are not directly comparable as the quantification are of different things (internalised Cy3-ColI, total collagen fibrils). We have clarified this in our discussion (revised lines 399-401).  

Discussion: Where does the ColI go? Solubilised? Degraded? Taken up by other cells? 

The inverse correlation is not very tight. In fact, at 38h where fiber count peaks, Cy3-ColI also peaks (esp in normalised data, Figure S2D).

We thank the reviewer for this comment and have reworded our main text to reflect this, and included additional discussion in our revised manuscript (revised lines 401-404).  

Line 123: What is the turnover rate of Fibrils? Don't know for how long the transcription has been done, or when this would affect the fibril number. You have the quant for Fn1, where is the quant for ColI?

We have included the quantification of collagen-I in original Figure 2A. We appreciate that it might cause confusion in Figure 2C (as we co-stained ColI and Fn1 in the same experiment) we have removed the collagen-I panel from the revised Figure 2C. We know from previous results that the number of fibrils fluctuate over 24hour period, although the turnover of one specific fibril is unlikely going to be 24 hours (https://www.biorxiv.org/content/10.1101/331496v2)

Line 124: no accumulation of col in extracellular space, but you don't know how much endogenous colI (or other endogenous ECM proteins) they're taking up as it isn't measured here. If the author wants to comment on this, should use either exogenous col to monitor take up and resection or block transcription/translation to show fibril formation endo/exocytosis independent of endogenous synthesis.

This experiment has been done in the original manuscript – siCol1a1 experiment was done with two rounds of siRNA, first round is normal transfection followed by reverse transfection onto fresh coverslips (this will ensure no prior ECM is being deposited, see Figure 3). However we appreciate that there may still be low levels of endogenous collagen-I, and thus have included new data using collagen-I knock-out fibroblasts to strengthen our findings (revised Figure 4).  

Line 142: Why is fibronectin synthesis also decreased in Col KD? This is clear in the image but no explanation/reference is given.

Due to the dynamic and complex nature of ECM, it is unsurprising if there is a knockon effect when knocking down one matrix protein. However, we have quantified the amount of fibronectin fibril deposited by scr and siCol1a1 fibroblasts, and showed that there was in fact no significant change between the two treatments (revised Figure 3A).

Figure 3A: Need labels for which colour/protein is shown. Needs quantifying, especially as the Fn1 decrease is not so obvious here, it is consistent between Figure 3A and 2C?

We have provided quantification in the revision (revised Figure 3A). Figure 3A and 2C are two separate experiments (one is Dyngo treatment and one is siCol1a1), and neither showed significant changes in fibronectin fibril areas.   

Figure 3B: Line 151: the text states that "The observation of fibrillar Cy3 signals in siCol1a1 cells showed that the cells can repurpose collagen into fibrils without the requirement for intrinsic collagen-I production (red arrow Figure 3B), however, there is clearly endogenous colI here too (along the fiber and also strongly at each end). Does the ColI antibody recognise the exogenous ColI?

In our hands the ColI antibody does not recognise exogenous ColI, as the cell-free Cy3-ColI images were also stained with ColI antibody to ensure the two experimental conditions were treated exactly the same.

This conclusion could only be made in the true absence of collagen: either in knock-out cells, or where collagen production/trafficking has been blocked (ie knockout of ColI chaperone or ERES block), or in a cell type that produces collagens but not ColI. Alternatively, if there are any fibrils seen that are completely negative, they should be shown in the figure and quantified (number of Cy3-ColI+-ColI+ vs Cy3-ColI+-ColI-).

We thank the reviewer for this suggestion. We have included new data from collagen knock-out fibroblasts in this revision (revised Figure 4).  

Figure S4A: the quality of this blot isn't very high, the result is not very clear and the high intensity (unspecific?) band below confounds the interpretation. In the author's previous paper (NCB 2020) the blots for VPS33B were much clearer, as is Fig S4D. It would be nice to include a clearer blot, maybe from the other repeats.

This is the only blot that we used to select which knockout clones to use for our previous paper, which is why the quality is not as high. Knockout clones were all verified with additional western blots, and we do not think that endogenous VPS33b is expressed at high levels (also verified by MS analyses).  Fig S4D is overexpression of VPS33b, which is much easier to detect.  

Figure S4D: This blot is much clearer, it would be useful to include a high gain to show the VPS33B band in CT to be able to understand the true increase.

From the qPCR data one can see that the increase at mRNA is 20+ fold increase; we’ve always had problems trying to detect endogenous VPS33b using western blot or mass spectrometry analysis.  

Figure 4A: The fibrils here in the CT are not obvious, and the difference between CT and KOs is not appreciable. Would this be clearer shown at a lower magnification, with zooms where needed? Or immunogold labelling/CLEM to label the ColI?

It is not trivial to carry out immunogold labelling/CLEM. These are cell-derived matrices in culture and thus lower magnification may not show as many collagen fibrils as one would expect. We are not confident that lower magnification will provide more information as the characteristic D-banded collagen pattern will be lost.  

Line 167/Figure 4B: It looks like there is more internal ColI in KO, but the images are not good enough to tell. This could be better shown by flow cytometry.

We have previously seen that VPSKO leads to accumulation of collagen-I in intracellular punctas (NCB2020) which is also seen here. Flow cytometry data for internalisation of external collagen is already included in original Figure 5G (revised Figure 6H).  

Again you mention intercellular vesicles, but based on these images, it is not possible to conclude this. These large spots could be aggregation elsewhere in the cell. Specific localisation should be shown by co-labelled IF/confocal, or it could be nicely shown by EM + fluorescent element (CLEM / Immunogold), or these statements removed from the text.

We appreciate that the term ‘vesicles’ is very defined in the trafficking field, and have changed it to ‘intracellular compartments’.  

Line 173-174 / Figure 4E: Why do you think the matrix mass is not increased in VPSoe by the approach shown in E when there is seemingly a huge increase by IF? E must also measure other ECM matrix proteins, which do you expect to be secreted by these cells? Could this confound the data if they too are affected by VPSoe?

IF is showing specifically collagen-I. Hydroxyproline detects multiple collagens, and shows a trend of increase (although not significant due to one outlier). Matrix mass is a very generic measurement of total ECM deposited based on decellularized ECM weight. The reviewer is correct that VPSoe may also affect other ECM deposition, however here we are focussing specifically with its effect on collagen-I. How VPSoe changes other types of ECM deposition would be something that could be addressed in future studies and is not within scope of this manuscript.   

Are the results in E paired?

Individual values between control and VPSoe in each separate experiments are paired.  

Figure 4F: Is quantification from IF shown in D? Specify which kind of microscopy it is based on.

Quantification is based on fibril counting using standard fluorescence microscopy, as used in our previous paper. D is independent of F, as F is specifically looking at synchronised circadian effects, and D (and elsewhere) we are looking at global collagen deposition effects, irrespective of what time of day the cells are in.  

Figure S5F: What do the yellow/red spots in the blots represent?

We apologise for the initial unclear description of what the yellow/magenta circles depict in relation to the phosphoimages of the radiolabelled cell free translation products displayed in Supplementary Figure 5, panels F, G and I. These circles indicate non-glycosylated (yellow) and N-glycosylated (magenta) species respectively, as is now clearly descried in the revised manuscript.

Figure 5 title: You can't conclude this from these images, need confocal and PM or cytosolic marker.

We have changed the title to ‘VPS33B co-trafficks with collagen-I”. There is no good commercial VPS33b antibody for immunofluorescence staining, which is why we used the split GFP approach in this paper, and the images were acquired using confocal imaging (Olympus SpinSR system).  

Figure 5E: The authors describe that ColI is in endosomes throughout most of the paper, and this is based on the involvement of VPS33B in the colI pathway. VPS33B is thought to be at the late endosome/lysosome. However, these images do not look like classic endosomes or lysosomes, or other normal organelle IF phenotypes. The fluorescent intensity looks saturated, and it is difficult to conclude anything from these images. It is unclear where in the cell the largest blob in the zoom would be localised and in which cell. I would suggest that this image is replaced and proper controls included (IgG controls and single channels) as well as using different markers for other potential intracellular structures.

We appreciate the reviewers comment with regards to the classification of VPS33b localisation in the endosome compartment. We did not mean to use VPS33b as an endosome marker, as the focus of our studies are the function of VPS33b in directing endogenous or exogenous collagen to fibrillogenesis. With live imaging we could see endocytosed collagen moving in intracellular compartments, and have conducted additional staining to show co-localisation with Rab5 (revised Figure 1), which we take to indicate, through convention, that it is occupying an endosome compartment. We have included single channel images in the revised manuscript (revised Figure 6E).

Line 255/ Figure 5G: no consistent change in uptake. Why are the results so varied in the KO and oe, here and in Fig 4C/E? N=4, what does that mean? 4 cells? 4 independent exps?

In all cases, “N” represents independent biological experiments in this manuscript. Thus “N=4” in this case is 4 independent biological experiments, with at least 10,000 cells analysed per experiment. 

We don’t know why there is a variation in response, however that is also why we concluded that it is unlikely that VPS33B is directly involved with collagen uptake. We have changed 5G (now revised Figure 5H) to a paired line graph for better representation.  

Figure 5H shows the uptake of Cy5ColI. At this resolution, VP2ko looks like the col is ER, in one of the cells in the zoom, it looks like it is at Golgi. I think that the uptake route of ColI needs to be better defined, as there is no way to tell here where the colI goes. ColI being recycled/degraded would be most likely. But this figure looks like that might not be the case. It is also not clear where the zooms come from, they should be indicated with dashed boxes in the lower mag image

We thank the reviewer for this comment, and agree that we need to define the uptake route of ColI. This is currently being assembled as a methodology manuscript, and how ColI is being recycled/degraded is one major research area of the Chang lab. 

We have added dashed boxes in the lower mag images to indicate where the zooms derived from, and we would also like to thank the reviewer for pointing this out as we realised we have accidentally cropped the image to a slightly different area for the VPSko image, and have now corrected this.  

Line 257: Based on this data, it could be trafficking through the cell as well as into the extracellular space.

We think that VPS33B is involved in trafficking collagen through the cell to plasma membrane but not secreted, as based on our split-GFP experiment we never observed extracellular GFP signal, which suggests VPS33b is not deposited extracellularly.

Line 259: "highlighting the role in recycling col to fibril formation sites" is an overstatement based on the data shown here, there is no data on colI trafficking or its regulation

We respectfully disagree that we have not shown data on col-I trafficking or regulation by VPS33b – split GFP highlighted cotrafficking to the plasma membrane, and we have shown a clear relationship between VPS33b and collagen-I fibril formation, with minimal changes to collagen-I mRNA levels. We acknowledge that we have not shown specifically the location of VPS33b at fibrillogenic sites and have modified this statement in revised manuscript (revised line 302).  

Line 262: "Having identified VPS33B as specifically driving collagen-I fibril formation" is also an overstatement.

We refer here the data that VPS33b is not controlling collagen-I secretion (as demonstrated by the CM westerns) and specifically fibrillogenesis. We have clarified this in the revised text (revised line 304).  

Line 286: It would be useful to have a brief intro to PLOD3.

We have included a brief intro to PLOD3 in the introduction, as well as the results highlighted by the reviewer, in our revised manuscript (revised line 54-58).  

Line 289/290: There could be other explanations for disruption to exo-endocytosis when disrupting col trafficking. Is VPS33B controlling exocytosis in general? Why should it be specific to col? Likewise with siITGA11 KD? Hypothesis for ITGA11 and fibrillogenesis?

The relationship between ITGA11 and collagen fibrillogenesis is currently in a manuscript by Donald Gullberg and Cedric Zeltz, under revision at Matrix Biology (see reference 63 in revised manuscript). We do not think that VPS33b is controlling exocytosis in general, which is supported by the minimal change in ponceau stain of the western blots in the manuscript. Previously it has been shown that VPS33B co-trafficks with PLOD3, a collagen-I modifier.  

Figure 6I: Why only quant Scr + siITGA11, not in VPSoe? It looks like there is still an increase in intracellular or fibril formation in VPSoe + siITGA11, which would be a key result to discuss.

We would like to clarify that 6I (now revised Figure 7I) is on the endocytosis of exogenous collagen-I, not quantification of Figure 6H.  

Line 307: Discuss fibrillogenic sites, what are they?

As we have not shown direct evidence of VPS33B delivering endocytosed collagen at the site of fibrillogenesis, we have decided to alter the text to avoid overstatement, as suggested from previous reviewers’ comments.  

Figure 8: What does pentachrome label?

Pentachrome staining allows for simultaneous staining of multiple species: collagen in red, sulphated mucopolysaccharides in violet, red blood cells in yellow, muscle in orange, nuclei in green.

Line 326: "In this study we have identified the endosome as a major protagonist in..." This is an overstatement and cant be drawn from this data.

We have modified this statement to “In this study we have identified an endocytic recycling mechanism for type I collagen fibrillogenesis that is under circadian regulation”

Line 330/331: "Collagen-I co-traffics with VPS33B in a VIPAS-containing endosomal compartment that directs collagen-I to sites of fibril assembly," This is also an overstatement that cannot be drawn from this data.

We have modified this statement to “Collagen-I co-traffics with VPS33B to the plasma membrane for fibrillogenesis”.  

Line 340: again, the demonstration of the involvement of the endocytic pathway is very limited.

We have provided new evidence in the revised manuscript that support the involvement of classical endosomal compartments.  

Line 366: You cant conclude this, you have not manipulated these proteins to show a functional effect or modulation of fibrillogenesis, it could still be a secondary effect.

We have provided new evidence in the revised manuscript that supports this conclusion. 

Line 569: "Unless otherwise stated, incubation and washes were done at room temperature." Which incubations? Specify if this is just post-fixation during the EM prep or during cell culture.

This is specific to the EM preparation and we have clarified in the revised manuscript (revised line 663).  

Small text alterations:

Overall we would like to thank the reviewer for highlighting these errors and mistakes in our manuscript, and have corrected them in our revised manuscript.  

Figure 1E: Fluoro image series? This is only one image.

We wrote this to mean single channel images, we have corrected the terminology.  

Line 111: Ref for Dyngo4a?

We have included this in the revised manuscript  

Line 121: introduction/abbreviation definition for Fn1? Instead it is on Line 140.

Thank you for highlighting this, we have corrected this in revised manuscript.  

Figure S2C: Alignment of labels cleaves x-axis.

We thank the reviewer for catching this and have corrected this with our revised manuscript.  

Figure S4F and G should be inverted to mention sequentially in the text.

We thank the reviewer for catching this and have corrected this in our revised manuscript.  

Line 182: Figure 4J should be G.

We thank the reviewer for catching this and have corrected this in our revised manuscript.

Line 209: typo: N-glycosylated.

We have corrected this typo in our revised manuscript.

Fig 6E: Very big as a figure element compared to others.

We have made this smaller in the revised manuscript to fit better with rest of the figure.  

Line 313: Figure 7E not F.

Thank you for spotting this, we have corrected it.  

Line 555: Typo: Scraped.

We have corrected this typo in our revised manuscript.

Line 562: missing )

We have corrected this typo in our revised manuscript.

Standardise

We thank the reviewer for spotting the mistakes below and have corrected in our revised manuscript.  

Legends: Include numbers of repeats and STATs throughout. 

Terminology: Dyng etc. 

Scale bars: some included as editable lines, some with size on top, small/large etc.

In certain cases we have positioned the scale bars in different regions of the figures to ensure no obscuring of the images.

VPS33b v B. 

Reviewer #2 (Recommendations For The Authors):  

The authors can improve the experimental part of the manuscript the following: 

-  For all the western blots please include molecular weight markers.

We thank the reviewer for noticing this omission and have included molecular weight markers in the revised manuscript.  

- Performing immunofluorescence and western blot analysis of endocytosed collagen -/+ inhibitors for lysosomal degradation (BafA1 or E64d+PepstatinA) in order to exclude endocytosis for degradation.

We thank the reviewer for this comment, another paper from the lab has identified lysosome to be involved in collagen fibrillogenesis (https://www.biorxiv.org/content/10.1101/2024.05.09.593302v1), thus  

- Figure out how Dyngo4a is affecting Col1 secretion in the first place? Does it interfere with the secretory pathway. Alternatively, use a different model to block endocytosis (e.g. siRNA Dynamin).

We thank the reviewer for raising this. The Dyngo CM blot for total ponceau stain (revised Figure 2B) showed minimal changes, which suggest that global secretion is not affected.  

- Further characterization of the VPS33B / collagen vesicles by immunofluorescence containing markers for early, late, and recycling endosomes. Block endocytic recycling by depletion of either Rabs or e.g. EHD1.

There are no good VPS33b antibody for staining. We have included images of GFP-tagged Rab5 co-localisation with labelled collagen-I (revised Figure 1D, Figure S6B).  

- Further clarify the status of the VPS33B knockouts e.g. by sequencing. also provide a readout of the siRNA KD, besides the mRNA levels, since there the difference is not striking.

The knockout cell lines were characterised previously in our 2020 paper, which is referred to in our revised manuscript. We have always had issues detecting endogenous VPS33b due to reagents limitations, which is why we resorted to mRNA as the key readout.  

- Doing siRNA knockdowns and endocytosis inhibition in the IPF fibroblasts to further strengthen the link between elevated expression of VPS33B/ ITGA11 and increased collagen uptake.

We thank the reviewer for suggesting these experiments. Due to limitations of the patient-derived fibroblasts (cell numbers and passage numbers) we had to prioritise experiments, and thus have performed siRNA against VPS33B and ITGA11 in the IPF fibroblasts. We showed that in both cases the amount of recycled labelled-collagen in collagen fibrils is significantly reduced (revised Figure 8D).  

Reviewer #3 (Recommendations For The Authors): 

Major points 

(1) Choice of cells: Please provide a rationale for why each cell line was used, and make sure that it is clear throughout the manuscript which cell line was used for each particular experiment. The HEK293T cell line is also missing from the reagent table.

We thank the reviewer for pointing out this omission, and have clarified in our revised manuscript which cell lines were used in each experiment. We used HEK293T to generate lentiviruses as described in the methods section.  

(2) Missing information from methods. Experimental details are missing from the methods in several places, making it difficult for someone to replicate an experiment. For example, no details are given in the methods describing the explant culture of murine tail tendons (described in results lines 78100), and there are no details on how the skin samples were obtained or stained. Further, no ethical approval details are provided for the use of human skin tissue.

We apologise for leaving the ethical approval details and skin sample collection out, this was an oversight and will be included in the revised manuscript. We have also included the method to how murine tail tendons were cultured ex vivo (revised lines 527-531, 546-553).  

(3) Functional studies in patient-derived cells. To fully establish the role of VPS33b and ITGA11 in fibrotic diseases, functional studies including the knockdown/overexpression of these genes could be performed to establish if the same response is seen as in non-diseased cells.

We agree that this will add much to the paper, and have performed siRNA against VPS33B and ITGA11 in the IPF fibroblasts. We showed that in both cases the amount of recycled labelled-collagen in collagen fibrils is significantly reduced (revised Figure 8D).

Minor Points

We thank the reviewer for pointing out these mistakes, and have corrected and included additional details in the revised manuscript.  

(1) Lines 51-52. Wording of this sentence is unclear, please rephrase. 

(2) Line 182. Should this be Fig 4G rather than J? 

(3) Line 209. Correct spelling of glycosylated. 

(4) Line 463. Incomplete brackets and details missing? 

(5) Line 590. Correct tense - was rather than are. 

(6) Line 593. Specify centrifugation speed. 

(7) Line 619. Nuclei rather than nucleus. 

(8) Ln 650. Statistical analysis - was normality tested? 

(9) Figure 1e - Difficult to read labels for coll/DAPI.

Author response:

The following is the authors’ response to the original reviews.

Joint Public review:

Summary:

This work provides a new general tool for predicting post-ERCP pancreatitis before the procedure depending on pancreatic calcification, female sex, intraductal papillary mucinous neoplasm, a native papilla of Vater, or the use of pancreatic duct procedures. Even though it is difficult for the endoscopist to predict before the procedure which case might have post-ERCP pancreatitis, this new model score can help with the maneuver and when the patient is at high risk of pancreatitis, sometimes can be deadly), so experienced endoscopists can do the procedure from the start. This paper provides a model for stratifying patients before the ERCP procedure into low, moderate, and high risk for pancreatitis. To be validated, this score should be done in many countries and on large numbers of patients. Risk factors can also be identified and added to the score to increase rank.

Thank you for reviewing our manuscript. We hope that this score will be validated in other countries from now on.

Strengths

(1) One of the severe complications of endoscopic retrograde cholangiopancreatography procedure is pancreatitis, so investigators try all the time to find a score that can predict which patients will probably have pancreatitis after the procedure. Most scores depend on the intraprocedural maneuver. Some studies discuss the preprocedural score that can predict pancreatitis before the procure. This study discusses a new preprocedural score for post-ERCP pancreatitis.

Thank you for evaluating our manuscript and raising a strength of this manuscript.

(2) Depending on this score that identifies low, moderate, and high-risk patients for post-pancreatitis, so from the start, experienced and well-trained endoscopists can do the procedure or can refer patients to tertiary hospitals or use interventional radiology or endoscopic retrograde cholangiopancreatography.

Thank you for evaluating our manuscript and raising a strength of this manuscript.

(3) The number of patients in this study is sufficient to analyze data correctly.

Thank you for evaluating our manuscript and raising a strength of this manuscript.

Weaknesses:

(1) It is a single-country, retrospective study.

Thank you for this comment. It’s exactly as you said. This is a limitation (Lines 326-327).

(2) Many cases were excluded, so the score cannot be applied to those patients.

Thank you for this valuable comment. The predictive PEP score is not necessary for the excluded patients. The reasons were as follows. Biliary duct cannulation was not attempted in patients for whom it was difficult to identify the Vater papilla. The biliary tract was separated from the pancreas in patients with a past history of choledochojejunostomy, pancreatojejunostomy, or pancreatogastrostomy. PEP risk was thought to be low in these patients and patients who underwent bile duct cannulation via the choledochoduodenal fistula. PEP diagnosis is difficult in patients with acute pancreatitis, whose diagnosis is currently in progress. We added these explanations (Lines 98-106).

(3) Many other studies, e.g., https://link.springer.com/article/10.1007/s00464-021-08491-1, https://pubmed.ncbi.nlm.nih.gov/36344369/, that have been published before discussing the same issue, so what is the new with this score?

Thank you for raising the new reference written by Archibugi et al. in 2023. The novelty of our score is that it is calculated using the factors that are investigated before ERCP procedures. The study written by Archibugi et al. involved procedure time and cannulation attempts for PEP prediction. These two factors are unknown before ERCP procedures. Therefore, a preprocedural predictive risk model for PEP was not created before our study was performed. We added the content of the past study written by Archibugi and included the report as a reference (Lines 65-67, 73-74).

(4) The discussion section needs reformulation to express the study's aim and results.

Thank you for this valuable comment. I have rewritten the first paragraph of the discussion. In the paragraph, we showed that the study achieved the aim on the basis of the results (Lines 245-255).

(5) Why did the authors select these items in their scoring system and did not add more variables?

Thank you for this valuable comment. We selected the items listed in the Japanese guidelines for acute pancreatitis and post-ERCP pancreatitis. We added this description (Lines 123-126). The original references of the guidelines were cited in the first draft version.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Comment1. Please revise these documents: copyright, disclaimer, ethics approval, consent to participate, consent for publication, data and material availability, competing interests, funding, authors' contributions, and acknowledgments.

First, thank you for reviewing our manuscript. We have already described the required information in the “author information” section. The sentences containing this information were proofread in English.

Reviewer #2 (Recommendations for the authors):

Comment 1. It would be best if you did this study in a Prospective way for more validation.

First, thank you for reviewing our manuscript. We have revised our manuscript according to your comments. It’s exactly as you said. These points are limitations (Lines 312-318, lines 326-327). We hope that future validation studies over wider geographic regions will prove our opinions.

Comment 2. The model name should be Acronyum (the first letter of the five items in the risk model).

Thank you for this valuable comment. Sorry, we could not create a memorable model name using the first letter of the five items.

Comment 3. You say that you include the pre-procedure criteria that predict PEP. You state one of the items, pancreatic duct procedure. Do you mean it is a history?

Thank you for this valuable comment. This means that the main purpose is the pancreatic duct. Therefore, the pancreatic duct procedure is listed as “planned pancreatic duct procedures” in Figure 2 (Lines 40-41, 231-234). When an unintended pancreatic duct procedure is performed, we can calculate the risk score by adding two points for “planned pancreatic duct procedures” (Lines 48-49, 247-250).

Comment 4. Regarding calcification, do you mean chronic pancreatitis? It needs more clarification regarding its degree.

Thank you for this valuable comment. We regard pancreatic calcification as a finding of chronic pancreatitis. Pancreatic calcification was defined as the degree that was confirmed by imaging, such as CT, MRI, and EUS. These definitions have been written in the first draft version (Lines 134-137).

Comment 5. Why don't you include young age in the model? Your result found that age less than 50 is significantly associated with PEP.

Thank you for this valuable comment. We selected the PEP risk factors listed in the Japanese guidelines for acute pancreatitis and post-ERCP pancreatitis. Age less than 50 years was listed as a PEP risk factor in the Japanese guidelines for acute pancreatitis. We added this description (Lines 123-126).

Comment 6. There is an ancient reference, some of them in 1994,1996.

Sorry for the old references. These references were written by Cotton et al. 1991, Freeman et al. 1996, and Loperfido et al. 1998. These are still important today. The diagnostic criteria for PEP were determined in the report written by Cotton et al., which is Cotton’s criteria. The other two references are representative reports that described risk factors for PEP, and these two reports were cited in the Japanese guidelines for pancreatitis written by Takada et al. 2022 (Lines 123-126).

Comment 7. In the introduction, you say that the first score includes one of the items for PEP pain during the procedure. It is a little bit strange.

Thank you for this comment. The first PEP risk score did not involve PEP pain but involved pain during the procedure (Line 68).

Comment 8. We know that once ERCP is indicated, you justify the importance of the risk model, stating that if one or more risks are found, we can do EUS or PTD. It is not reasonable to abort the procedure in case of frequent pancreatic duct cannulation or cancel ERCP if pt has one or more risk factors.

Thank you for this valuable comment. If ERCP is performed for high-risk patients, prophylaxes for PEP, such as procedures by experts, pancreatic stent placement, and NSAID suppository insertion, should be performed as much as possible (Lines 281-287, 308-311).

Comment 9. Regarding ERCP pancreatitis criteria, does it include amylase 3t or lipase?

Thank you for this comment. We used Cotton’s criteria for diagnosing PEP. Cotton’s criteria include hyperamylasemia (more than three times the normal upper limit) at least 24 hours after ERCP (114-116).

Comment 10. It is well known that pr with functional biliary disorder has a high incidence of PEP; it doesn't need a manometer for diagnosis. It needs to be included.

Thank you for this comment. Moreover, functional biliary disorders are difficult to diagnose before ERCP procedures (Lines 259-262). The factor that is not apparent before ERCP could not be included in the predictive PEP scoring system.

Comment 11: What is gabexare and nafamost.

Thank you for this comment, and sorry for our insufficient explanation. These compounds include gabexate masilate and nafamostat masilate, which are protease inhibitors. In some institutions, protease inhibitors are used as prophylaxis for PEP. We added “protease inhibitors” (Lines 138-139, Tables 1 and 2).

Reviewer #3 (Recommendations for the authors):

Comment 1. The sample size needs clarification.

First, thank you for reviewing our manuscript. The sample size has been included in the “Methods” section (Lines 157-165).

Comment 2. They need to be mentioned cause they depend on old references in discussion and background.

Thank you for this comment. The previous references were written by Cotton et al. 1991, Freeman et al. 1996, and Loperfido et al. 1998. These are still important today. The diagnostic criteria for PEP were determined in the report written by Cotton et al., which is Cotton’s criteria. The other two references are representative reports that described risk factors for PEP, and these two reports were cited in the Japanese guidelines for pancreatitis written by Takada et al. 2022 (Lines 122-126). In the background and discussion, we added new recent references and information related to the references (Lines 65-67, 285-287, 291-295, 308-311).

Comment 3. Case definition should be added to the methodology.

Thank you for this comment. We added patient information. Please refer to the response against the eLife assessment, weakness, (2).

Comment 4. Do you include all who met the inclusion criteria, or was there any random sampling technique?

No, we did not use random sampling techniques.

Comment 5. What is the value of comparing the development and validation groups? I do not think it adds anything new as if you want to exclude confounders. Has the comparison revealed that a confounder does exist? What was your point of view concerning that?

Thank you for this valuable comment, and sorry for the insufficient explanation. The differences between the development cohort and the validation cohort are important because the goodness of fit for the score could be confirmed in significantly different groups. We added this explanation (Lines 197-199, 251-253).

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary

The authors determine the phylogenetic relation of the roughly two dozen wtf elements of 21 S. pombe isolates and show that none of them in the original S. pombe are essential for robust mitotic growth. It would be interesting to test their meiotic function by simply crossing each deletion mutant with the parent and analyzing spores for non-Mendelian inheritance. If this has been reported already, that information should be added to the manuscript. If not, I suggest the authors do these simple experiments and add this information.

Thanks for the great summary! Most of the wtf genes have been tested for meiotic drive phenotypes previously by Bravo Nunez et al. (2020; http://doi.org/10.1371/journal.pgen.1008350). The reference was cited in our original manuscript, and we added the details in the revised manuscript.

Strengths:

The most interesting data (Figure 4) show that one recombinant (wtfC4) between wtf18 and wtf23 produces in mitotic growth a poison counteracted by its own antidote but not by the parental antidotes. Again, it would be interesting to test this recombinant in a more natural setting - meiosis between it and each of the parents.

We will test the meiotic driver phenotype of the wtfC4 we constructed in S. pombe as suggested.

Weaknesses:

In the opinion of this reviewer, some minor rewriting is needed.

We did the rewriting as this reviewer suggested in the comments to authors.

Reviewer #2 (Public review):

Summary:

This important study provides a mechanism that can explain the rapid diversification of poison-antidote pairs (wtf genes) in fission yeast: recombination between existing genes.

Thanks!

Strengths:

The authors analyzed the diversity of wtf in S. pombe strains, and found pervasive copy number variations. They further detected signals of recurrent recombination in wtf genes. To address whether recombination can generate novel wtf genes, the authors performed artificial recombination between existing wft genes, and showed that indeed a new wtf can be generated: the poison cannot be detoxified by the antidotes encoded by parental wtf genes but can be detoxified by own antidote.

Thanks for the great summary!

Weaknesses:

The study can benefit from demonstrating that the novel poison-antidote constructed by the authors can serve as a meiotic driver.

We will test the meiotic driver phenotype of the wtfC4 we constructed in S. pombe as suggested.

Reviewer #3 (Public review):

Summary:

In this manuscript, Wang and colleagues explore factors contributing to the diversification of wtf meiotic drivers. wtf genes are autonomous, single-gene poison-antidote meiotic drivers that encode both a spore-killing poison (short isoform) and an antidote to the poison (long isoform) through alternative transcriptional initiation. There are dozens of wtf drivers present in the genomes of various yeast species, yet the evolutionary forces driving their diversification remain largely unknown. This manuscript is written in a straightforward and effective manner, and the analyses and experiments are easy to follow and interpret. While I find the research question interesting and the experiments persuasive, they do not provide any deeper mechanistic understanding of this gene family.

Thanks! Please see the following for our point-to-point response.

Strengths:

(1) The authors present a comprehensive compendium and analysis of the evolutionary relationships among wtf genes across 21 strains of S. pombe.

(2) The authors found that a synthetic chimeric wtf gene, combining exons 1-5 of wtf23 and exon 6 of wtf18, behaves like a meiotic driver that could only be rescued by the chimeric antidote but neither of the parental antidotes. This is a very interesting observation that could account for their inception and diversification.

Thanks for the great summary!

Weaknesses:

(1) Deletion strains

The authors separately deleted all 25 Wtf genes in the S. pombe ference strain. Next, the authors performed a spot assay to evaluate the effect of wtf gene knockout on the yeast growth. They report no difference to the WT and conclude that the wtf genes might be largely neutral to the fitness of their carriers in the asexual life cycle at least in normal growth conditions.

The authors could have conducted additional quantitative growth assays in yeast, such as growth curves or competition assays, which would have allowed them to detect subtle fitness effects that cannot be quantified with a spot assay. Furthermore, the authors do not rule out simpler explanations, such as genetic redundancy. This could have been addressed by crossing mutants of closely related paralogs or editing multiple wtf genes in the same genetic background.

Another concern is the lack of detailed information about the 25 knockout strains used in the study. There is no information provided on how these strains were generated or, more importantly, validated. Many of these wtf genes have close paralogs and are flanked by repetitive regions, which could complicate the generation of such deletion strains. As currently presented, these results would be difficult to replicate in other labs due to insufficient methodological details

We will generate growth curves for all the 25 wtf deletion strains. We will also provide detailed for wtf gene knockout. However, for 25 wtf genes, there are too many combinations for editing two genes, and it is technically challenging to knock out multiple wtf together. Nevertheless, our results suggest single wtf gene has little effect on the host fitness under normal condition.  

(2) Lack of controls

The authors found that a synthetic chimeric wtf gene, constructed by combining exons 1-5 of wtf23 and exon 6 of wtf18, behaves as a meiotic driver that can be rescued only by its corresponding chimeric antidote, but not by either of the parental antidotes (Figure 4F). In contrast, three other chimeric wtf genes did not display this property (Figure 4C-E). No additional experiments were conducted to explain these differences, and basic control experiments, such as verifying the expression of the chimeric constructs, were not performed to rule out trivial explanations. This should be at the very least discussed. Also, it would have been better to test additional chimeras.

We will verify the expression of the chimeric genes, and test the phenotype of meiotic diver for wtfC4 in S. pombe.

(3) Statistical analyses

In line 130 the authors state that: "Given complex phylogenetic mixing observed among wtf genes (Figure 1E), we tested whether recombination occurred. We detected signals of recombination in the 25 wtf genes of the S. pombe reference genome (p = 0) and in the wtf genes of the 21 S. pombe strains (p = 0) using pairwise homoplasy index (HPI) test. ". Reporting a p-value of 0 is not appropriate. Exact P-values should be reported.

We will report the exact p values in the revised manuscript.

Author response:

We appreciate the reviewers' thoughtful and constructive comments. In this provisional response, we aim to address what we see as the key critiques, with a detailed, point-by-point reply to be provided alongside the revised manuscript. Below, we outline how we intend to address these critiques in the revised manuscript.

(1) We will revise sections of the manuscript to ensure that all results, particularly those concerning the effects of lesions, are described more clearly and with sufficient context. This includes providing additional visualizations and rewording any ambiguous statements.

(2) In this study, we examined a subset of 7,396 blocks where animals quickly adapted after block switches (achieving LCriterion in 20 or fewer trials), thereby focusing on expert-level performance and avoiding periods that might be affected by low motivation. It is valid to question whether the same observations would hold if the full dataset were analyzed. To address this, we expanded our analysis to include a supplementary figure Supplementary Figure 1.1 that illustrate the same relationships based on block length (BL) instead of LRandom, both with and without the restriction on LCriterion (n = 9,156 blocks in which the block length is under 100 trials, without any LCriterion restrictions), and based on LRandom without any LCriterion restrictions and with a less stringent LCriterion restriction (with ≤ 50 Trials for the criterion). This method allowed us to include all trials in our dataset. We observed similar effects of block length on choice behavior around switches (Figure 3), confirming the consistency of our findings across different analytical conditions.

(3) We agree that robust validation of model selection is crucial. To address this, we will generate a confusion matrix to assess whether our model selection process accurately identifies the correct model class across a range of generative parameters. Include additional model selection metrics, such as cross-validation, to complement the BIC analysis and provide a more robust comparison of models.

(4) We acknowledge the concern regarding our comparison of the "best" and the "4th best" models. The "4th best" model was chosen because it is the most widely recognized in the literature. Our intention was to demonstrate the performance of the most commonly used model, but we understand how this may have been misleading. To address this, we will revise our comparison to focus on the "best" and the "2nd best" models, ensuring greater clarity in the manuscript. Additionally, we will include supplementary simulation results and figures to provide a more comprehensive analysis on models.

Author response:

We appreciate the expression of enthusiasm for our paper by the editors and the three reviewers and the suggestions on how to improve the study. Here we outline how we will address the reviewers’ concerns and suggestions in a planned revision of our manuscript.

Reviewer #1 listed two primary weaknesses:

(1) the need for discussion of the extent to which the cell line we used resembles CRH neurons and

(2) that we did not test for the effect of blockade of the glucocorticoid receptor.

(1) As the reviewer acknowledges, our experiments called for the use of a cell line to dissect intracellular trafficking of the α1 adrenoreceptor. We selected the N42 cell line for this purpose because it is an immortalized hypothalamic cell line (developed by Belsham and colleagues, Belsham et al., 2004) that expresses CRH. We have used this cell line successfully in the past to study transcriptional and rapid non-genomic actions of glucocorticoids, which indicated that, in addition to expressing CRH, these cells also express both the nuclear glucocorticoid receptor and a membrane-associated receptor that binds glucocorticoids (Rainville et al., 2019; Weiss et al., 2019). We believe that this hypothalamic cell line is the most closely related to native PVN CRH neurons of any cell line available. As requested, we will add to the Discussion of the manuscript to further justify our choice of cells.

(2) We agree that this experiment should be performed. We will test the classical GR (and progesterone) antagonist RU486 (mifepristone) for its effect on the cort regulation of α1 adrenoreceptor trafficking. Our ex vivo electrophysiology studies have indicated that the rapid glucocorticoid effect in native hypothalamic CRH neurons is not blocked by RU486 and is not, therefore, dependent on activation of the classical nuclear GR (Di et al., 2003; Di et al., 2016).

Reviewer #2 also listed two main weaknesses of the study:

(1) that we did not test whether the adrenoreceptor desensitization by restraint stress generalizes to other stress modalities and might be more robust with a pure somatic stressor, and

(2) the lack of identification of a target protein as a mechanism for the role of nitrosylation.

(1) We used restraint stress as a means to elicit corticosterone release, which desensitized the HPA response to a NE-dependent somatic stressor (lipopolysaccharide injection) but not to a NEindependent psychological stressor (predator odor) (Jiang et al., 2021). We got a near-complete loss of the sensitivity of CRH neurons to NE with restraint (i.e., near ceiling effect), such that a different stressor, including a more purely somatic stressor, should not increase the Cort-induced desensitization further. For that reason, we would argue that testing other stressors would not add value to the current study. That said, we plan and have received new funding to test in the future whether the Cort desensitization of the HPA response to LPS stress generalizes to other somatic stressors. We also have future plans to test for the Cort desensitization of other Gq-coupled receptors.

(2) We agree that finding the molecular target of nitrosylation as the mechanism for Cort desensitization of α1 adrenoreceptors would significant improve the study, but this is a potentially enormous undertaking as it will require the screening and validation of multiple proteins involved in protein trafficking to find the one(s) targeted for nitrosylation by Cort. We tested β-arrestin as a possible target in the paper, but did not find Cort to regulate β-arrestin nitrosylation. We plan to undertake a general nitrosylation screen of proteins to identify multiple possible targets, but prefer to defer this and the validation of possible targets to a future, more thorough analysis.

Reviewer #3 also pointed out two main weaknesses of our study:

(1) that the glucocorticoidnitrosylation link was confusing, and

(2) that it was unclear how blocking α1 adrenoreceptors reversed the Cort-induced cytosolic accumulation of the receptor.

We appreciate the reviewer pointing out these deficiencies in our interpretation and explanation of our findings. We plan to address them directly in the revised version of the paper. 

References

Belsham DD, Cai F, Cui H, Smukler SR, Salapatek AMF, Shkreta L (2004) Generation of a phenotypic array of hypothalamic neuronal cell models to study complex neuroendocrine disorders. Endocrinology 145:393–400.

Weiss GL, Rainville JR, Zhao Q, Tasker JG (2019) Purity and stability of the membrane-limited glucocorticoid receptor agonist dexamethasone-BSA. Steroids 142:2-5. 

Rainville JR, Weiss GL, Evanson N, Herman JP, Vasudevan N, Tasker JG (2019) Membrane-initiated nuclear trafficking of the glucocorticoid receptor in hypothalamic neurons. Steroids 142:55-64.

Di S, Malcher-Lopes R, Halmos KCs, Tasker JG (2003) Non-genomic glucocorticoid inhibition via endocannabinoid release in the hypothalamus: a fast feedback mechanism. Journal of Neuroscience 23:4850-4857.

Di S, Itoga CA, Fisher MO, Solomonow J, Roltsch EA, Gilpin NW, Tasker JG (2016) Acute stress suppresses inhibition and increases anxiety via endocannabinoid release in the basolateral amygdala. Journal of Neuroscience 36:8461-8470.

Jiang Z, Chen C, Weiss GL, Fu X, Stelly CE, Sweeten BLW, Tirrell PS, Pursell I, Stevens CR, Fisher MO, Begley JC, Harrison LM, Tasker JG (2022) Stress-induced glucocorticoid desensitizes adrenoreceptors to gate the neuroendocrine response to somatic stress in male mice. Cell Reports 41(3):111509.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Summary:

"Neural noise", here operationalized as an imbalance between excitatory and inhibitory neural activity, has been posited as a core cause of developmental dyslexia, a prevalent learning disability that impacts reading accuracy and fluency. This study is the first to systematically evaluate the neural noise hypothesis of dyslexia. Neural noise was measured using neurophysiological (electroencephalography [EEG]) and neurochemical (magnetic resonance spectroscopy [MRS]) in adolescents and young adults with and without dyslexia. The authors did not find evidence of elevated neural noise in the dyslexia group from EEG or MRS measures, and Bayes factors generally informed against including the grouping factor in the models. Although the comparisons between groups with and without dyslexia did not support the neural noise hypothesis, a mediation model that quantified phonological processing and reading abilities continuously revealed that EEG beta power in the left superior temporal sulcus was positively associated with reading ability via phonological awareness. This finding lends support for analysis of associations between neural excitatory/inhibitory factors and reading ability along a continuum, rather than as with a case/control approach, and indicates the relevance of phonological awareness as an intermediate trait that may provide a more proximal link between neurobiology and reading ability. Further research is needed across developmental stages and over a broader set of brain regions to more comprehensively assess the neural noise hypothesis of dyslexia, and alternative neurobiological mechanisms of this disorder should be explored.

Strengths:

The inclusion of multiple methods of assessing neural noise (neurophysiological and neurochemical) is a major advantage of this paper. MRS at 7T confers an advantage of more accurately distinguishing and quantifying glutamate, which is a primary target of this study. In addition, the subject-specific functional localization of the MRS acquisition is an innovative approach. MRS acquisition and processing details are noted in the supplementary materials according to the experts' consensus-recommended checklist (https://doi.org/10.1002/nbm.4484). Commenting on the rigor, the EEG methods is beyond my expertise as a reviewer.

Participants recruited for this study included those with a clinical diagnosis of dyslexia, which strengthens confidence in the accuracy of the diagnosis. The assessment of reading and language abilities during the study further confirms the persistently poorer performance of the dyslexia group compared to the control group.

The correlational analysis and mediation analysis provide complementary information to the main case-control analyses, and the examination of associations between EEG and MRS measures of neural noise is novel and interesting.

The authors follow good practice for open science, including data and code sharing. They also apply statistical rigor, using Bayes Factors to support conclusions of null evidence rather than relying only on non-significant findings. In the discussion, they acknowledge the limitations and generalizability of the evidence and provide directions for future research on this topic.

Weaknesses:

Though the methods employed in the paper are generally strong, there are certain aspects that are not clearly described in the Materials & Methods section, such as a description of the statistical analyses used for hypothesis testing.

Thank you for pointing this out. A description of the statistical models used in the analyses of EEG biomarkers has been added to the Materials and Methods:

“First, exponent and offset values were averaged across all electrodes and analyzed using a 2x2 repeated measures ANOVA with group (dyslexic, control) as a between-subjects factor and condition (resting state, language task) as a within-subjects factor. Age was included in the analyses as a covariate due to the correlation between variables. Next, exponent and offset values were averaged across electrodes corresponding to the left (F7, FT7, FC5) and right inferior frontal gyrus (F8, FT8, FC6), and to the left (T7, TP7, TP9) and right superior temporal sulcus (T8, TP8, TP10). The electrodes were selected based on the analyses outlined by Giacometti and colleagues (2014) and Scrivener and Reader (2022). For these analyses, a 2x2x2x2 repeated measures ANOVA with age as a covariate was conducted with group (dyslexic, control) as a between-subjects factor and condition (resting state, language task), hemisphere (left, right), and region (frontal, temporal) as within-subjects factors. Results for the alpha and beta bands were calculated for the same clusters of frontal and temporal electrodes and analyzed with a similar 2x2x2x2 repeated measures ANOVA; however, for these analyses, age was not included as a covariate due to a lack of significant correlations.”

We also expanded the description of the statistical models used in the analyses of MRS biomarkers:

“To analyze the metabolite results, separate univariate ANCOVAs were conducted for Glu, GABA+, Glu/GABA+ ratio and Glu/GABA+ imbalance measures with group (control, dyslexic) as a between-subjects factor and voxel gray matter volume (GMV) as a covariate. Additionally, for the Glu analysis, age was included as a covariate due to a correlation between variables. Both frequentist and Bayesian statistics were calculated. Glu/GABA+ imbalance measure was calculated as the square root of the absolute residual value of a linear relationship between Glu and GABA+ (McKeon et al., 2024).”

With regard to metabolite quantification, it is unclear why the authors chose to analyze and report metabolite values in terms of creatine ratios rather than quantification based on a water reference given that the MRS acquisition appears to support using a water reference.

We have decided to use the ratio of Glu and GABA to total creatine (tCr), as this is still a common practice in MRS studies at 7T (e.g., Nandi et al., 2022; Smith et al., 2021). This approach normalizes the signal, reducing the impact of intensity variations across different regions and tissue compositions. Additionally, total creatine concentration is considered relatively stable across different brain regions, which is particularly important in our study, where a functional localizer was used to establish the left STS region individually. Our decision was further influenced by previous studies on dyslexia (Del Tufo et al., 2018; Pugh et al., 2014) which have reported creatine ratios and included GM volume as a covariate in their models, thus providing comparability. It is now indicated in the Results:

“For comparability with previous studies in dyslexia (Del Tufo et al., 2018; Pugh et al., 2014) we report Glu and GABA as a ratio to total creatine (tCr).”

and in the Method sections:

“Glu and GABA+ concentrations were expressed as a ratio to total-creatine (tCr; Creatine + Phosphocreatine) following previous MRS studies in dyslexia (Del Tufo et al., 2018; Pugh et al., 2014).

We did not estimate absolute concentrations using water signals as a reference, as this would require accounting for water relaxation times, which may vary across our age range. Nevertheless, our dataset has been made publicly available for future researchers to calculate and compare absolute values.

Del Tufo, S. N., Frost, S. J., Hoeft, F., Cutting, L. E., Molfese, P. J., Mason, G. F., Rothman, D. L., Fulbright, R. K., & Pugh, K. R. (2018). Neurochemistry Predicts Convergence of Written and Spoken Language: A Proton Magnetic Resonance Spectroscopy Study of Cross-Modal Language Integration. Frontiers in Psychology, 9, 1507. https://doi.org/10.3389/fpsyg.2018.01507

Nandi, T., Puonti, O., Clarke, W. T., Nettekoven, C., Barron, H. C., Kolasinski, J., Hanayik, T., Hinson, E. L., Berrington, A., Bachtiar, V., Johnstone, A., Winkler, A. M., Thielscher, A., Johansen-Berg, H., & Stagg, C. J. (2022). tDCS induced GABA change is associated with the simulated electric field in M1, an effect mediated by grey matter volume in the MRS voxel. Brain Stimulation, 15(5), 1153–1162. https://doi.org/10.1016/j.brs.2022.07.049

Pugh, K. R., Frost, S. J., Rothman, D. L., Hoeft, F., Del Tufo, S. N., Mason, G. F., Molfese, P. J., Mencl, W. E., Grigorenko, E. L., Landi, N., Preston, J. L., Jacobsen, L., Seidenberg, M. S., & Fulbright, R. K. (2014). Glutamate and choline levels predict individual differences in reading ability in emergent readers. Journal of Neuroscience, 34(11), 4082–4089. https://doi.org/10.1523/JNEUROSCI.3907-13.2014

Smith, G. S., Oeltzschner, G., Gould, N. F., Leoutsakos, J. S., Nassery, N., Joo, J. H., Kraut, M. A., Edden, R. A. E., Barker, P. B., Wijtenburg, S. A., Rowland, L. M., & Workman, C. I. (2021). Neurotransmitters and Neurometabolites in Late-Life Depression: A Preliminary Magnetic Resonance Spectroscopy Study at 7T. Journal of Affective Disorders, 279, 417–425. https://doi.org/10.1016/j.jad.2020.10.011

GABA is typically quantified using J-editing sequences as lower field strengths (~3T), and there is some evidence that the GABA signal can be reliably measured at 7T without editing, however, the authors should discuss potential limitations, such as reliability of Glu and GABA measurements with short-TE semi-laser at 7T.

In addition, MRS measurements of GABA are known to be influenced by macromolecules, and GABA is often denoted as GABA+ to indicate that other compounds contribute to the measured signal, especially at a short TE and in the absence of symmetric spectral editing.

A general discussion of the strengths and limitations of unedited Glu and GABA quantification at 7T is warranted given the interest of this work to researchers who may not be experts in MRS.

While we agree with the Reviewer that at 3T, it is recommended to use J-edited MRS to measure GABA (Mullins et al., 2014), the better spectral resolution at 7T allows for more reliable results for both metabolites using moderate echo-time, non-edited MRS (Finkelman et al., 2022). In this study, we used a short echo time (TE), which is optimal for Glu but not ideal for GABA, as it interferes with other signals. We are grateful to the Reviewer for suggesting the addition of a short paragraph to the Discussion, describing the practicalities of 3T and 7T MRS and changing the abbreviation to GABA+ to inform readers of possible macromolecule contamination:

“We chose ultra-high-field MRS to improve data quality (Özütemiz et al., 2023), as the increased sensitivity and spectral resolution at 7T allows for better separation of overlapping metabolites compared to lower field strengths. Additionally, 7T provides a higher signal-to-noise ratio (SNR), improving the reliability of metabolite measurements and enabling the detection of small changes in Glu and GABA concentrations. Despite these theoretical advantages, several practical obstacles should be considered, such as susceptibility artifacts and inhomogeneities at higher field strengths that can impact data quality. Interestingly, actual methodological comparisons (Pradhan et al., 2015; Terpstra et al., 2016) show only a slight practical advantage of 7T single-voxel MRS compared to optimized 3T acquisition. For example, fitting quality yielded reduced estimates of variance in concentration of Glu in 7T (CRLB) and slightly improved reproducibility levels for Glu and GABA (at both fields below 5%). Choosing the appropriate MRS sequence involves a trade-off between the accuracy of Glu and GABA measurements, as different sequences are recommended for each metabolite. J-edited MRS is recommended for measuring GABA, particularly with 3T scanners (Mullins et al., 2014). However, at 7T, more reliable results can be obtained using moderate echo-time, non-edited MRS (Finkelman et al., 2022). We have opted for a short-echo-time sequence, which is optimal for measuring Glu. However, this approach results in macromolecule contamination of the GABA signal (referred to as GABA+).”

Finkelman, T., Furman-Haran, E., Paz, R., & Tal, A. (2022). Quantifying the excitatory-inhibitory balance: A comparison of SemiLASER and MEGA-SemiLASER for simultaneously measuring GABA and glutamate at 7T. NeuroImage, 247, 118810. https://doi.org/10.1016/j.neuroimage.2021.118810

Mullins, P. G., McGonigle, D. J., O'Gorman, R. L., Puts, N. A., Vidyasagar, R., Evans, C. J., Cardiff Symposium on MRS of GABA, & Edden, R. A. (2014). Current practice in the use of MEGA-PRESS spectroscopy for the detection of GABA. NeuroImage, 86, 43–52. https://doi.org/10.1016/j.neuroimage.2012.12.004

Özütemiz, C., White, M., Elvendahl, W., Eryaman, Y., Marjańska, M., Metzger, G. J., Patriat, R., Kulesa, J., Harel, N., Watanabe, Y., Grant, A., Genovese, G., & Cayci, Z. (2023). Use of a Commercial 7-T MRI Scanner for Clinical Brain Imaging: Indications, Protocols, Challenges, and Solutions-A Single-Center Experience. AJR. American Journal of Roentgenology, 221(6), 788–804. https://doi.org/10.2214/AJR.23.29342

Pradhan, S., Bonekamp, S., Gillen, J. S., Rowland, L. M., Wijtenburg, S. A., Edden, R. A., & Barker, P. B. (2015). Comparison of single voxel brain MRS AT 3T and 7T using 32-channel head coils. Magnetic Resonance Imaging, 33(8), 1013–1018. https://doi.org/10.1016/j.mri.2015.06.003

Terpstra, M., Cheong, I., Lyu, T., Deelchand, D. K., Emir, U. E., Bednařík, P., Eberly, L. E., & Öz, G. (2016). Test-retest reproducibility of neurochemical profiles with short-echo, single-voxel MR spectroscopy at 3T and 7T. Magnetic Resonance in Medicine, 76(4), 1083–1091. https://doi.org/10.1002/mrm.26022

Further, the single MRS voxel location is a limitation of the study as neurochemistry can vary regionally within individuals, and the putative excitatory/inhibitory imbalance in dyslexia may appear in regions outside the left temporal cortex (e.g., network-wide or in frontal regions involved in top-down executive processes). While the functional localization of the MRS voxel is a novelty and a potential advantage, it is unclear whether voxel placement based on left-lateralized reading-related neural activity may bias the experiment to be more sensitive to small, activity-related fluctuations in neurotransmitters in the CON group vs. the DYS group who may have developed an altered, compensatory reading strategy.

We agree that including only one region of interest for the MRS measurements is a potential limitation of our study, and we have now added this information to the Discussion:

“Moreover, since the MRS data was collected only from the left STS, it is plausible that other areas might be associated with differences in Glu or GABA concentrations in dyslexia.”

However, differences in Glu and GABA concentrations in this region were directly predicted by the neural noise hypothesis of dyslexia. We acknowledge that this information was missing in the previous version of the manuscript. It is now included in the Results:

“Moreover, the neural noise hypothesis of dyslexia identifies perisylvian areas as being affected by increased glutamatergic signaling, and directly predicts associations between Glu and GABA levels in the superior temporal regions and phonological skills (Hancock et al., 2017).”

as well as in the Discussion:

“Nevertheless, the neural noise hypothesis predicted increased glutamatergic signaling in perisylvian regions, specifically in the left superior temporal cortex (Hancock et al., 2017).”

Figure 1 contains a lot of information, and it may be helpful to split it into 2 figures (EEG vs. MRS) so that the plots could be made larger and the reader could more easily digest the information.

(a) I would also recommend displaying separate metabolite fit plots for each group, since the current presentation in panel F makes it appear that the MRS data is examined by testing differences between groups across the full spectrum (where the lines diverge), which really isn't the case.

(b) The GABA peak is not visible in the spectrum, and Glutamate and GABA both have multiple peaks that should be shown on the spectrum. This may be best achieved by displaying the individual metabolite sub-spectra below the full spectrum

Thank you for these suggestions. We have split the information into two Figures following the Reviewer’s recommendations.

It is not clear why the 3T structural images were used for segmentation and calculation of tissue fraction if 7T structural images were also acquired (which would presumably have higher resolution).

Generally, T1-weighted images from the 7T scanner exhibit more artifacts than those from the 3T scanner due to higher magnetic field inhomogeneity. These artifacts are especially pronounced in regions near air-tissue interfaces, such as the temporal lobes. Therefore, we chose the 3T structural images for segmentation and tissue fraction calculations and clarified this in the Method section:

“Voxel segmentation was performed on structural images from a 3T scanner, coregistered to 7T structural images in SPM12, as the latter exhibited excessive artifacts and intensity bias in the temporal regions”.

The basis set includes a large number of metabolites (27), including many low-concentration metabolites/compounds (e.g., bHG, bHB, Citrate, Threonine, ethanol) that are typically only included in studies targeting specific metabolites in disease/pathology. Please justify the inclusion of this maximal set of metabolites in the basis set, given that the inclusion of overlapping low-concentration metabolites may influence metabolite measurements of interest (https://doi.org/10.1002/mrm.10246).

There is still no consensus in the MR community on which metabolites should be included in the model of human cerebral 1H-MR spectra. Typically, only major contributors such as NAA, Cr, Cho, Lac, mI, and possibly Glx are evaluated. Some studies also include additional metabolites like Ace, Ala, Asp, GABA, Glc, Gly, sI, NAAG, and Tau. In this study, as in a few others, further metabolites such as PCh, GPC, PCr, GSH, PE, and Thr were introduced and this approach seems suitable for high-field spectra (Hofmann et al., 2002).

Hofmann, L., Slotboom, J., Jung, B., Maloca, P., Boesch, C., & Kreis, R. (2002). Quantitative 1H-magnetic resonance spectroscopy of human brain: Influence of composition and parameterization of the basis set in linear combination model-fitting. Magnetic Resonance in Medicine, 48(3), 440–453. https://doi.org/10.1002/mrm.10246

Please provide a figure indicating the localization of the MRS voxel for a sample subject.

A figure indicating the localization of the MRS voxel for a sample subject was added to the MRS checklist.

It would be helpful to include Table S1 in the main article.

Table S1 from the Supplementary Material has now been added to the main manuscript as Table 1 in the Results section.

Please report descriptive statistics for EEG and MRS measures in Table S1.

We have added a new Table S1 in the Supplementary Material, providing descriptive statistics for EEG and MRS E/I balance measures, presented separately for the dyslexic and control groups.

I recommend avoiding using the terms "direct" and "indirect" to contrast MRS and EEG measures of E/I balance. Both of these measures are imperfect and it is misleading to say that MRS is a "direct" measure of neurotransmitters. There is also ambiguity in what is meant by "direct": in contrast to EEG, MRS does not measure neural activity and does not provide high-resolution temporal information, so in a sense, it is less direct.

Thank you for this suggestion. We have replaced the terms 'direct' and 'indirect' biomarkers with 'MRS' and 'EEG' biomarkers throughout the text.

There are many cases throughout the results in which Bayes and frequentist stats seem to contradict each other in terms of significance and what should be included in the models, especially with regard to the interaction effects (the Bayes factors appear to favor non-significant interactions). I think this is worth considering and describing to offer more clarity for the readers.

We agree that a discussion of the divergent results between Bayesian and frequentist models was missing in the previous version of the manuscript. To provide greater clarity for the readers, we have conducted follow-up Bayesian t-tests in every case where the results indicated the inclusion of non-significant interactions with the effect of group in the model. These additional analyses have been performed for the exponent, offset, as well as for beta bandwidth in the Supplementary Material. We have also added a paragraph addressing these discrepancies in the Discussion:

“Remarkably, in some models, results from Bayesian and frequentist statistics yielded divergent conclusions regarding the inclusion of non-significant effects. This was observed in more complex ANOVA models, whereas no such discrepancies appeared in t-tests or correlations. Given reports of high variability in Bayesian ANOVA estimates across repeated runs of the same analysis (Pfister, 2021), these results should be interpreted with caution. Therefore, following the recommendation to simplify complex models into Bayesian t-tests for more reliable estimates (Pfister, 2021), we conducted follow-up Bayesian t-tests in every case that favored the inclusion of non-significant interactions with the group factor. These analyses provided further evidence for the lack of differences between the dyslexic and control groups. Another source of discrepancy between the two methods may stem from the inclusion of interactions between covariates and within-subject effects in frequentist ANOVA, which were not included in Bayesian ANOVA to adhere to the recommendation for simpler Bayesian models (Pfister, 2021).”

Pfister, R. (2021). Variability of Bayes factor estimates in Bayesian analysis of variance. The Quantitative Methods for Psychology, 17(1), 40-45. doi:10.20982/tqmp.17.1.p040

It would be helpful to indicate whether participants in the DYS group had a history of reading intervention/remediation. In addition to showing that the DYS group performed lower than the CON group on reading assessments as a whole and given their age, was the performance on the reading assessments at an individual level considered for inclusion in the study? (i.e., were participants' persistent poor reading abilities confirmed with the research assessments?)

We were unable to assess individual reading skills due to the lack of standardized diagnostic norms for adult dyslexia in Poland. Therefore, participants in the dyslexic group were recruited based on a previous clinical diagnosis of dyslexia, and reading and reading-related tasks were used for group-level comparisons only. This information has been added to the Methods section:

“Since there are no standardized diagnostic norms for dyslexia in adults in Poland, individuals were assigned to the dyslexic group based on a past diagnosis of dyslexia.”

Unfortunately, we did not collect information about participants' history of reading intervention or remediation. In this context, we acknowledge that including a sample of adult participants is a potential limitation of our study, however, this was already mentioned in the Discussion.

Regarding the fMRI task, please indicate whether the participants whose threshold and/or contrast was changed for localization were from the DYS or CON group.

This information is now added to the Method section:

“For 6 participants (DYS n = 2, CON n = 4), the threshold was lowered to p < .05 uncorrected, while for another 6 participants (DYS n = 3, CON n = 3) the contrast from the auditory run was changed to auditory words versus fixation cross due to a lack of activation for other contrasts.”

Reviewer #2 (Public Review):

Summary:

This study utilized two complementary techniques (EEG and 7T MRI/MRS) to directly test a theory of dyslexia: the neural noise hypothesis. The authors report finding no evidence to support an excitatory/inhibitory balance, as quantified by beta in EEG and Glutamate/GABA ratio in MRS. This is important work and speaks to one potential mechanism by which increased neural noise may occur in dyslexia.

Strengths:

This is a well-conceived study with in-depth analyses and publicly available data for independent review. The authors provide transparency with their statistics and display the raw data points along with the averages in figures for review and interpretation. The data suggest that an E/I balance issue may not underlie deficits in dyslexia and is a meaningful and needed test of a possible mechanism for increased neural noise.

Weaknesses:

The researchers did not include a visual print task in the EEG task, which limits analysis of reading-specific regions such as the visual word form area, which is a commonly hypoactivated region in dyslexia. This region is a common one of interest in dyslexia, yet the researchers measured the I/E balance in only one region of interest, specific to the language network.

We agree with the Reviewer that including different tasks for the EEG biomarkers assessment would be valuable. However, this limitation was already addressed in the Discussion:

“Importantly, our study focused on adolescents and young adults, and the EEG recordings were conducted during rest and a spoken language task. These factors may limit the generalizability of our results. Future research should include younger populations and incorporate a broader array of tasks, such as reading and phonological processing, to provide a more comprehensive evaluation of the E/I balance hypothesis.”

Further, this work does not consider prior studies reporting neural inconsistency; a potential consequence of increased neural noise, which has been reported in several studies and linked with candidate-dyslexia gene variants (e.g., Centanni et al., 2018, 2022; Hornickel & Kraus, 2013; Neef et al., 2017). While E/I imbalance may not be a cause of increased neural noise, other potential mechanisms remain and should be discussed.

Thank you for referring us to other works reporting neural variability in dyslexia. We agree that a broader context regarding sources of reduced neural synchronization, beyond E/I imbalance, was missing in the previous version of the manuscript. We have now included these references in the Discussion:

“Furthermore, although our results do not support the idea of E/I balance alterations as a source of neural noise in dyslexia, they do not preclude other mechanisms leading to less synchronous neural firing posited by the hypothesis. In this context, there is evidence showing increased trial-to-trial inconsistency of neural responses in individuals with dyslexia (Centanni et al., 2022) or poor readers (Hornickel and Kraus, 2013) and its associations with specific dyslexia risk genes (Centanni et al., 2018; Neef et al., 2017). At the same time, the observed trial-to-trial inconsistency was either present only in a subset of participants (Centanni et al., 2018), limited to some experimental conditions (Centanni et al., 2022), or specific brain regions – e.g., brainstem in Hornickel and Kraus (2013), left auditory cortex in Centanni et al. (2018), or left supramarginal gyrus in Centanni et al. (2022).”

A better description of the exponent and offset components is needed at the beginning of the results, given that the methods are presented in detail at the end. I also do not see a clear description of these components in the methods.

A description of the aperiodic components is now included in the Results:

“In the initial step of the analysis, we analyzed the aperiodic (exponent and offset) components of the EEG spectrum. The exponent reflects the steepness of the EEG power spectrum, with a higher exponent indicating a steeper signal; while the offset represents a uniform shift in power across frequencies, with a higher offset indicating greater power across the entire EEG spectrum (Donoghue et al., 2020).”

as well as in the Materials and Methods:

“Two broadband aperiodic parameters were extracted: the exponent, which quantifies the steepness of the EEG power spectrum, and the offset, which indicates signal’s power across the entire frequency spectrum.”

Reviewer #3 (Public Review):

Summary:

This study by Glica and colleagues utilized EEG (i.e., Beta power, Gamma power, and aperiodic activity) and 7T MRS (i.e., MRS IE ratio, IE balance) to reevaluate the neural noise hypothesis in Dyslexia. Supported by Bayesian statistics, their results show solid 'no evidence' of EI balance differences between groups, challenging the neural noise hypothesis. The work will be of broad interest to neuroscientists, and educational and clinical psychologists.

Strengths:

Combining EEG and 7T MRS, this study utilized both the indirect (i.e., Beta power, Gamma power, and aperiodic activity) and direct (i.e., MRS IE ratio, IE balance) measures to reevaluate the neural noise hypothesis in Dyslexia.

Weaknesses:

The authors may need to provide more data to assess the quality of the MRS data.

We have addressed the following specific recommendations of the Reviewer providing more data about the quality of the MRS data.

The authors may need to explain how the number of subjects is determined in the MRS section.

We have clarified the MRS sample description in the Results section:

“Due to financial and logistical constraints, 59 out of the 120 recruited subjects, selected progressively as the study unfolded, were examined with MRS. Subjects were matched by age and sex between the dyslexic and control groups. Due to technical issues and to prevent delays and discomfort for the participants, we collected 54 complete sessions. Additionally, four datasets were excluded based on our quality control criteria, and three GABA+ estimates exceeded the selected CRLB threshold. Ultimately, we report 50 estimates for Glu (21 participants with dyslexia) and 47 for GABA+ and Glu/GABA+ ratios (20 participants with dyslexia).”

Is there a reason why theta and gamma peaks were not observed in the majority of participants? What are the possible reasons that likely caused the discrepancy between this study and previously reported relevant studies?

We have now added a discussion about the absence of oscillatory peaks in the theta and gamma bands to the Discussion section:

“We could not perform analyses for the gamma oscillations since in the majority of participants the gamma peak was not detected above the aperiodic component. Due to the 1/f properties of the EEG spectrum, both aperiodic and periodic components should be disentangled to analyze ‘true’ gamma oscillations; however, this approach is not typically recognized in electrophysiology research (Hudson and Jones, 2022). Indeed, previous studies that analyzed gamma activity in dyslexia (Babiloni et al., 2012; Lasnick et al., 2023; Rufener and Zaehle, 2021) did not separate the background aperiodic activity. For the same reason, we could not analyze results for the theta band, which often does not meet the criteria for an oscillatory component manifested as a peak in the power spectrum (Klimesch, 1999). Moreover, results from a study investigating developmental changes in both periodic and aperiodic components suggest that theta oscillations in older participants are mostly observed in frontal midline electrodes (Cellier et al., 2021), which were not analyzed in the current study.”

Hudson, M. R., & Jones, N. C. (2022). Deciphering the code: Identifying true gamma neural oscillations. Experimental Neurology, 357, 114205. https://doi.org/10.1016/j.expneurol.2022.114205

Klimesch, W. (1999). EEG alpha and theta oscillations reflect cognitive and memory performance: A review and analysis. Brain Research Reviews, 29(2-3), 169-195. https://doi.org/10.1016/S0165-0173(98)00056-3

Based on Figure 1F, the quality of the MRS data may be contaminated by the lipid signal, especially for the DYS group. To better evaluate the MRS data, especially the GABA measurements, the authors need to show:

(a) the placement of the MRS voxel on the anatomical images;

Averaged MRS voxel placement was already presented in Figure 1 (now Figure 2) in the manuscript. Now, we have also added exemplary single-subject images to the MRS checklist in the Supplement.

(b) Glu and GABA model functions

We have now provided more meaningful Glu and GABA indications in Figure 2.

(c) CRLB for GABA

We have added respective estimates to the Supplement:

%CRLB of Glu: mean 2.96, SD = 0.79

%CRLB of GABA: mean 10.59, SD = 2.76

%CRLB of NAA: 1.76 SD = 0.46

Further, the authors added voxel's gray matter volume as a covariate when performing separate ANCOVAs. The authors may need to use alpha correction or 1-fCSF correction to corroborate these results.

We chose to use the ratio of Glu and GABA to total creatine (tCr), as this remains a common practice in MRS studies at 7T (e.g., Nandi et al., 2022; Smith et al., 2021). This decision was also influenced by previous dyslexia studies (Del Tufo et al., 2018; Pugh et al., 2014) and is now clarified in the Results and Methods sections.

Regarding alpha correction, a recent paper (García-Pérez et al., 2023) recommends: 'In general, avoid corrections for multiple testing if statistical claims are to be made for each individual test, in the absence of an omnibus null hypothesis.' Since we report null findings, further alpha correction would not significantly impact the results.

García-Pérez, M. A. (2023). Use and misuse of corrections for multiple testing. Methods in Psychology, 8, 100120. https://doi.org/10.1016/j.metip.2023.100120

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review): 

Though the Norrin protein is structurally unrelated to the Wnt ligands, it can activate the Wnt/βcatenin pathway by binding to the canonical Wnt receptors Fzd4 and Lrp5/6, as well as the tetraspanin Tspan12 co-receptor. Understanding the biochemical mechanisms by which Norrin engages Tspan12 to initiate signaling is important, as this pathway plays an important role in regulating retinal angiogenesis and maintaining the blood-retina-barrier. Numerous mutations in this signaling pathway have also been found in human patients with ocular diseases. The overarching goal of the study is to define the biochemical mechanisms by which Tspan12 mediates Norrin signaling. Using purified Tspan12 reconstituted in lipid nanodiscs, the authors conducted detailed binding experiments to document the direct, high-affinity interactions between purified Tspan12 and Norrin. To further model this binding event, they used AlphaFold to dock Norrin and Tspan12 and identified four putative binding sites. They went on to validate these sites through mutagenesis experiments. Using the information obtained from the AlphaFold modeling and through additional binding competition experiments, it was further demonstrated that Tspan12 and Fzd4 can bind Norrin simultaneously, but Tspan12 binding to Norrin is competitive with other known co-receptors, such as HSPGs and Lrp5/6. Collectively, the authors proposed that the main function of Tspan12 is to capture low concentrations of Norrin at the early stage of signaling, and then "hand over" Norrin to Fzd4 and Lrp5/6 for further signal propagation. Overall, the study is comprehensive and compelling, and the conclusions are well supported by the experimental and modeling data. 

Strengths: 

• Biochemical reconstitution of Tspan12 and Fzd4 in lipid nanodiscs is an elegant approach for testing the direct binding interaction between Norrin and its co-receptors. The proteins used for the study seem to be of high purity and quality. 

• The various binding experiments presented throughout the study were carried out rigorously. In particular, BLI allows accurate measurement of equilibrium binding constants as well as on and off rates. 

• It is nice to see that the authors followed up on their AlphaFold modeling with an extensive series of mutagenesis studies to experimentally validate the potential binding sites. This adds credence to the AlphaFold models. 

• Table S1 is a further testament to the rigor of the study. 

• Overall, the study is comprehensive and compelling, and the conclusions are well supported by the experimental and modeling data. 

Suggestions for improvement: 

• It would be helpful to show Coomassie-stained gels of the key mutant Norrin and Tspan12 proteins presented in Figures 2E and 2F. 

We have included Stain-Free SDS-PAGE gels from the purification of the Norrin and Tspan12 mutants in a new Figure S4.

• Many Norrin and Tspan12 mutations have been identified in human patients with FEVR. It would be interesting to comment on whether any of the mutations might affect the NorrinTspan12 binding sites described in this study. 

Thank you for this suggestion. We have inspected human mutation databases gnomAD, ClinVar, and HGMD for known mutations in the predicted Tspan12-Norrin binding interface and their occurrence in human patients with FEVR or Norrie disease.

While a number of Tspan12 residues that we predict to interact with Norrin are impacted by rare mutations in humans (e.g., L169M, E170V, E173K, D175N, E196G, S199C, as found in the gnomAD database), these alleles are of unknown clinical significance (as found in ClinVar or HGMD databases). It is possible that mutations that slightly weaken the Norrin-Tspan12 interface may not produce a strong phenotype, especially given the avidity we expect from this system. By our examination, the missense variants of clinical significance that have been found in the Tspan12 LEL would be expected to destabilize the protein (i.e., mutations to or from cysteine or proline, or mutations to residues involved in packing interactions within the LEL fold), and therefore these mutations may produce a disease phenotype by impacting Tspan12 protein expression levels.  

Several Norrin mutations that are associated with Norrie disease, FEVR, or other diseases of the retinal vasculature have been found in the predicted Tspan12 binding site. For example, Norrin mutations at positions L103 (L103Q, L103V), K104 (K104N, K104Q), and A105 (A105T, A105P, A105E, A105S, A105T, A105V) have been found in patients, all of which may disrupt binding to Tspan12. However, the deleterious effect of K104 mutations on Norrin-stimulated signaling could also be explained by a weakened Norrin-Fzd4 binding interface. Norrin mutations at R115 (R115L and R115Q), as well as R121 (R121L, R121G, R121Q, and R121W) have also been found in patients with various diseases of the retinal vasculature. Additionally, the Norrin mutation T119P has been found in patients with Norrie disease, but we would expect this mutation to destabilize Norrin in addition to disrupting the Tspan12 binding site. 

While we commented briefly on mutations R115L and R121W in the original draft (page 5, paragraphs 4 and 1, respectively), we have updated the manuscript with more comments on disease-associated mutations to the predicted Tspan12 binding site on Norrin (page 5, first partial paragraph; page 9, first partial paragraph). 

• Some of the negative conclusions (e.g. the lack of involvement of Tspan12 in the formation of the Norrin-Lrp5/6-Fzd4-Dvl signaling complex) can be difficult to interpret. There are many possible reasons as to why certain biological effects are not recapitulated in a reconstitution experiment. For instance, the recombinant proteins used in the experiment may not be presented in the correct configurations, and certain biochemical modifications, such as phosphorylation, may also be missing. 

We agree that different Tspan12 and Fzd4 stoichiometries, lipid compositions, and posttranslational modifications could impact the results of our study, and that it is important to mention these possibilities. We have added these caveats to the discussion section (page 10, last paragraph).  

Reviewer #2 (Public Review): 

This is an interesting study of high quality with important and novel findings. Bruguera et al. report a biochemical and structural analysis of the Tspan12 co-receptor for norrin. Major findings are that Norrin directly binds Tspan12 with high affinity (this is consistent with a report on BioRxiv: Antibody Display of cell surface receptor Tetraspanin12 and SARS-CoV-2 spike protein) and a predicted structure of Tspan12 alone or in complex with Norrin. The

Norrin/Tspan12 binding interface is largely verified by mutational analysis. An interaction of the Tspan12 large extracellular loop (LEL) with Fzd4 cannot be detected and interactions of fulllength Tspan12 and Fzd4 cannot be tested using nano-disc based BLI, however, Fzd4/Tspan12 heterodimers can be purified and inserted into nanodiscs when aided by split GFP tags. An analysis of a potential composite binding site of a Fzd4/Tspan12 complex is somewhat inconclusive, as no major increase in affinity is detected for the complex compared to the individual components. A caveat to this data is that affinity measurements were performed for complexes with approximately 1 molecule Tspan12 and FZD4 per nanodisc, while the composite binding site could potentially be formed only in higher order complexes, e.g., 2:2 Fzd4/Tspan12 complexes. Interestingly, the authors find that the Norrin/Tspan12 binding site and the Norrin/Lrp6 binding site partially overlap and that the Lrp6 ectodomain competes with Tspan12 for Norrin binding. This result leads the authors to propose a model according to which Tspan12 captures Norrin and then has to "hand it off" to allow for Fzd4/Lrp6 formation. By increasing the local concentration of Norrin, Tspan12 would enhance the formation of the Fzd4/Lrp5 or Fzd4/Lrp6 complex. 

Thank you for pointing out the BioRxiv report showing Norrin-Tspan12 LEL binding. We have cited this in the introduction of our revised manuscript (page 2, paragraph 3).

The experiments based on membrane proteins inserted into nano-discs and the structure prediction using AlphaFold yield important new insights into a protein complex that has critical roles in normal CNS vascular biology, retinal vascular disease, and is a target for therapeutic intervention. However, it remains unclear how Norrin would be "handed off" from Tspan12 or Tspan12/Fzd4 complexes to Fzd4/Lrp6 complexes, as the relatively high affinity of Norrin to Fzd4/Tspan12 dimers likely does not favor the "handing off" to Fzd4/Lrp6 complexes. 

While the Fzd4-Tspan12 interaction is strong, our data suggest that Fzd4 and Tspan12 bind Norrin with negative cooperativity, suggesting that Fzd4 binding may enhance Norrin-Tspan12 dissociation to facilitate handoff. This model is based on 1) the dissociation of Norrin from beadbound Tspan12 in the presence of saturating Fzd4 CRD (Figure 3D), and 2) a weaker measured affinity of Norrin-Tspan12LEL in the presence of saturating Fzd4 CRD (Figure 3F). We have now added wording to emphasize this in the discussion section (page 9, end of first full paragraph).

However, as you note, the Norrin-Tspan12 affinity that we measured in the presence of Fzd CRD (tens of nM) is still much stronger than the known Norrin-LRP6 affinity (0.5-1µM), which predicts that the efficiency of this handoff may be low. We have now commented on this in the discussion section and mentioned an alternative model in which Tspan12 presents the second Norrin protomer to LRP5/6 for signaling, instead of dissociating (page 9, paragraph 2). However, the handoff efficiency could also be impacted by other factors such as the relative abundance and surface distribution of Tspan12, Fzd4, LRP6 and HSPGs.  

Areas that would benefit from further experiments, or a discussion, include: 

-  The authors test a potential composite binding site of Fzd4/Tspan12 heterodimers for norrin using nanodiscs that contain on average about 1 molecule Fzd4 and 1 molecule Tspan12. The Fzd4/Tspan12 heterodimer is co-inserted into the nanodiscs supported by split-GFP tags on Fzd4 and Tspan12. The authors find no major increase in affinity, although they find changes to the Hill slope, reflecting better binding of norrin at low norrin concentrations. In 293F cells overexpressing Fzd4 and Tspan12 (which may result in a different stoichiometry) they find more pronounced effects of norrin binding to Fzd4/Tspan12. This raises the possibility that the formation of a composite binding requires Fzd4/Tspan12 complexes of higher order, for example, 2:2 Fzd4/Tspan12 complexes, where the composite binding site may involve residues of each Fzd4 and Tspan12 molecule in the complex. This could be tested in nanodiscs in which Fzd4 and Tspan12 are inserted at higher concentrations or using Fzd4 and Tspan12 that contain additional tags for oligomerization. 

It is quite possible that Tspan12 and Fzd4 cluster into complexes with a stoichiometry greater than 1:1 in cells (this is supported by e.g., BRET experiments in (Ke et al., 2013)), and we mention in the discussion that that receptor clustering may be an additional mechanism by which Tspan12 exerts its function (page 10, paragraph 4). We would be quite interested to know the stoichiometry of Fzd4 and Tspan12 complexes in cells at endogenous expression levels, both in the presence and absence of Norrin, and to biochemically characterize these putative larger complexes in the future. We have amended the discussion to mention the caveat that our reconstitution experiments do not test higher-stoichiometry Fzd4/Tspan12 complexes (page 10, last paragraph).

- While Tspan12 LEL does not bind to Fzd4, the successful reconstitution of GFP from Tspan12 and Fzd4 tagged with split GFP components provides evidence for Fzd4/Tspan12 complex formation. As a negative control, e.g., Fzd5, or Tspan11 with split GFP tags (Fzd5/Tspan12 or Fzd4/Tspan11) would clarify if FZD4/Tspan12 heterodimers are an artefact of the split GFP system. 

The split-GFP system allows us to co-purify receptors that do not normally co-localize (for example, as we have shown with Fzd4 and LRP6 in the absence of ligand (Bruguera et al., 2022)) so we do not mean to claim that it provides evidence for Fzd4/Tspan12 complex formation. In fact, we were unable to co-purify co-expressed Fzd4 and Tspan12 unless they were tethered with the split GFP system, and separately-purified Fzd4 and Tspan12 did not incorporate into nanodiscs together unless they were tethered by split GFP. Based on these experiments, we expect that the purported Fzd4-Tspan12 interaction that others have found by co-IP or co-localization is easily disrupted by detergent, may require a specific lipid, and/or may not be direct.

To clarify this point, we have noted in the results section that without the split GFP tags, Tspan12 and Fzd4 did not co-purify or co-reconstitute into nanodiscs, and that co-reconstitution was enabled by the split GFP system (page 6, first full paragraph).   

- Fzd4/Tspan12 heterodimers stabilized by split GFP may be locked into an unfavorable orientation that does not allow for the formation of a composite binding site of FZD4 and Tspan12, this is another caveat for the interpretation that Fzd4/Tspan12 do not form a composite binding site. This is not discussed. 

While the split GFP does enforce a Fzd4/Tspan12 dimer, the split GFP is removed by protease cleavage during the final step of the purification process, after the dimer is contained in a nanodisc. This should allow Fzd4 and Tspan12 to freely adopt any pose and to diffuse within the confines of the nanodisc lipid bilayer. However, it has been shown that the phospholipid bilayer in small nanodiscs is not as fluid as the physiological plasma membrane, and although we used the slightly larger belt protein (MSP1E3D1, 13 nm diameter nanodiscs), perhaps the receptors are indeed locked in some unfavorable state for this reason. Additionally, the nanodiscs are planar, so if the formation of a composite binding site requires membrane curvature, this would not be recapitulated in our system. We have cited these caveats in the discussion section (page 10, last paragraph).  

- Mutations that affect the affinity of norrin/fzd4 are not used to further test if Fzd4 and Tspan12 form a composite binding site. Norrin R41E or Fzd4 M105V were previously reported to reduce norrin/frizzled4 interactions and signaling, and both interaction and signaling were restored by Tspan12 (Lai et al. 2017). Whether a Fzd4/Tspan12 heterodimer has increased affinity for Norrin R41E was not tested. Similarly, affinity of FZD4 M105V vs a Fzd4 M105V/Tspan12 heterodimer were not tested. 

Since the high affinity of Norrin for both Fzd4 and Tspan12 may have obscured any enhancement of Norrin affinity for Fzd4/Tspan12 compared to either receptor alone, we did consider weakening Fzd-Norrin affinity to sensitize this experiment, inspired by the experiments you mention in (Lai et al., 2017). However, we suspected that the slight increase in Norrin affinity for the Fzd4/Tspan12 dimer compared to Fzd4 alone was driven mainly by increased avidity that enhanced binding of low Norrin concentrations, and this avidity effect would likely confound the interpretation of any experiment monitoring 2:2 complex formation. Additionally, on the basis that soluble Fzd4 extracellular domain and Tspan12 bind Norrin with negative cooperativity (Figures 3D and 3F), we concluded that this composite binding site was unlikely.

- An important conclusion of the study is that Tspan12 or Lrp6 binding to Norrin is mutually exclusive. This could be corroborated by an experiment in which LRP5/6 is inserted into nanodiscs for BLI binding tests with Norrin, or Tspan12 LEL, or a combination of both. Soluble LRP6 may remove norrin from equilibrium binding/unbinding to Tspan12, therefore presenting LRP6 in a non-soluble form may yield different results. 

We agree that testing this conclusion in an orthogonal experiment would be a valuable addition to this study. We have now performed a similar experiment to the one you described, but with Norrin immobilized on biosensors, and with LRP6 in detergent competing with Tspan12 LEL for Norrin binding (Figure S12, discussed on page 8, first full paragraph). The results of this experiment show that biosensor-immobilized Norrin will bind LRP6, and that soluble Tspan12 inhibits LRP6 binding in a concentration-dependent manner. The LRP6 construct we use (residues 20-1439) includes the transmembrane domain but has a truncated C terminus, since LRP6 constructs containing the full C terminus tend to aggregate during purification. We chose to immobilize Norrin to make the experiment as interpretable as possible, since immobilizing LRP6 and competing Norrin off with the LEL could result in an increase in signal (from the LEL binding the second available Norrin protomer) as well as a decrease (from Norrin being competed off of the immobilized LRP6). We conducted the experiment in detergent (DDM) instead of nanodiscs to be able to test higher concentrations of LRP6.

- The authors use LRP6 instead of LRP5 for their experiments. Tspan12 is less effective in increasing the Norrin/Fzd4/Lrp6 signaling amplitude compared to Norrin/Fzd4/Lrp5 signaling, and human genetic evidence (FEVR) implicates LRP5, not LRP6, in Norrin/Frizzled4 signaling. The authors find that Norrin binding to LRP6 and Tspan12 is mutually exclusive, however this may not be the case for Lrp5. 

This is an important point which we have now addressed in the text (page 8, end of first full paragraph). LRP5 is indeed the receptor implicated in FEVR and expressed in the relevant tissues for Tspan12/Norrin signaling. Unfortunately, LRP5 expresses poorly and we are unable to purify sufficient quantities to perform these experiments. However, LRP5 and LRP6 both transduce Tspan12-enhanced Norrin signaling in TOPFLASH assays (as you mention and as shown by (Zhou and Nathans, 2014)), bind Norrin, and are highly similar (they share 71% sequence identity overall and 73% sequence identity in the extracellular domain), so we expect their Norrin-binding sites to be conserved.

- The biochemical data are largely not correlated with functional data. The authors suggest that the Norrin R115L FEVR mutation could be due to reduced norrin binding to tspan12, but do not test if Tspan12-mediated enhancement of the norrin signaling amplitude is reduced by the R115L mutation. Similarly, the impressive restoration of binding by charge reversal mutations in site 3 is not corroborated in signaling assays. 

We agree that testing the impact of Norrin mutations in cell-based signaling assays would be an informative way to further test our model. However, the Norrin mutants we tested generated poor TopFlash signals in all conditions tested. This may be due to general protein instability, weakened affinity for LRP, or weaker interactions with HSPGs. Whatever the cause, the low signal made it challenging to conclusively say whether the Norrin mutations affected Tspan12mediated signaling enhancement.

When expressed for purification, Tspan12 mutants generally expressed poorly compared to WT Tspan12, so we were concerned that differences in protein stability or trafficking would lead to lower cell-surface levels of mutant Tspan12 relative to WT in TopFlash signaling assays, which would confound interpretation of mutant Tspan’s ability to enhance Norrin signaling.

Because of these challenges, follow-up experiments to investigate the signaling capabilities of Norrin and Tspan12 mutants were not informative and we have not included them in the revised manuscript.

Reviewer #3 (Public Review): 

Brugeuera et al present an impressive series of biochemical experiments that address the question of how Tspan12 acts to promote signaling by Norrin, a highly divergent TGF-beta family member that serves as a ligand for Fzd4 and Lrp5/6 to promote canonical Wnt signaling during CNS (and especially retinal) vascular development. The present study is distinguished from those of the past 15 years by its quantitative precision and its high-quality analyses of concentration dependencies, its use of well-characterized nano-disc-incorporated membrane proteins and various soluble binding partners, and its use of structure prediction (by AlphaFold) to guide experiments. The authors start by measuring the binding affinity of Norrin to Tspan12 in nanodiscs (~10 nM), and they then model this interaction with AlphaFold and test the predicted interface with various charge and size swap mutations. The test suggests that the prediction is approximately correct, but in one region (site 1) the experimental data do not support the model. [As noted by the authors, a failure of swap mutations to support a docking model is open to various interpretations. As AlphFold docking predictions come increasingly into common use, the compendium of mutational tests and their interpretations will become an important object of study.] Next, the authors show that Tspan12 and Fzd4 can simultaneously bind Norrin, with modest negative cooperativity, and that together they enhance Norrin capture by cells expressing both Tspan12 and Fzd4 compared to Fzd4 alone, an effect that is most pronounced at low Norrin concentration. Similarly, at low Norrin concentration (~1 nM), signaling is substantially enhanced by Tspan12. By contrast, the authors show that LRP6 competes with Tspan12 for Norrin binding, implying a hand-off of Norrin from a Tspan12+Fzd4+Norrin complex to a LRP5/6+Fzd4+Norrin complex. Thanks to the authors' careful dose-response analyses, they observed that Norrin-induced signaling and Tspan12 enhancement of signaling both have bell-shaped dose-response curves, with strong inhibition at higher levels of Norrin or Tspan12. The implication is that the signaling system has been built for optimal detection of low concentrations of Norrin (most likely the situation in vivo), and that excess Tspan12 can titrate Norrin at the expense of LRP5/6 binding (i.e., reduction in the formation of the LRP5/6+Fzd4+Norrin signaling complex). In the view of this reviewer, the present work represents a foundational advance in understanding Norrin signaling and the role of Tspan12. It will also serve as an important point of comparison for thinking about signaling complexes in other ligand-receptor systems. 

Recommendations for the authors: 

Reviewer #2 (Recommendations For The Authors):   

- In Figure 5F high concentrations of transfected Tspan12 plasmid inhibit signaling, which the authors interpret to support the model that Tspan12/Norrin binding prevents Norrin/LRP6/FZD4 complex formation. Alternatively, the cells do not tolerate the expression of the tetraspanin at high levels, for example, due to misfolding and aggregate formation. To distinguish these possibilities: Do high levels of Tspan12 overexpression also inhibit signaling induced by Wnt3a and appropriate Frizzled receptors, even though Tspan12 has no influence on Wnt/LRP6 binding? 

We thank the reviewer for suggesting this important control experiment. We have added the Wnt-simulated TOPFLASH values to the figure in 5F for all conditions. In repeating this experiment, we noticed that high levels of transfected Tspan12 may decrease cell viability and therefore have adjusted the range of transfected Tspan12 in the new Figure 5F (discussed on page 8, second full paragraph). Under this new protocol, both Norrin- and Wnt-stimulated signaling were inhibited by the highest amount of transfected Tspan12. However, Norrinstimulated signaling is inhibited by lower amounts of transfected Tspan12 than Wnt-stimulated signaling, and to a greater extent, supporting our proposed model that Tspan12 competes with LRP for Norrin binding.

- Is Tspan12 with c-terminal rho-tag (the form incorporated into nanodiscs) also used for functional luciferase assays, or was untagged Tspan12 used for the luciferase assays in Fig 4D and 5F? Does the c-terminal tag interfere with Tspan12-mediated enhancement of Norrin signaling? 

For the luciferase assays included in this manuscript, wildtype, full-length, untagged Tspan12 is used. We have clarified this in our methods section. When we tested the wildtype vs Cterminally rho1D4-tagged version of Tspan12 in TOPFLASH assays, we saw that the enhancement of Norrin signaling by Tspan12-1D4 was weaker than enhancement by untagged Tspan12. This is consistent with the finding reported in Cell Reports (Lai et al., 2017) that a chimeric Tspan12 receptor with its C-terminus replaced with that of Tspan11 was still capable of enhancing Norrin signaling, though to a lesser extent than WT Tspan12. The deficiency of signaling by our rho1D4-tagged Tspan12 could be due to a difference in receptor expression level or trafficking, but in the absence of a reliable antibody against Tspan12, we were unable to assess the expression levels or localization of the untagged Tspan12 to compare it to the rho1D4-tagged version. (For binding experiments, we reasoned that the C-terminal tag should not affect Tspan12’s ability to bind Norrin extracellularly, especially as we found that purified fulllength Tspan12 and Tspan12∆C (residues 1-252) bound Norrin equally well; we have added this comparison to table S1.)  

Reviewer #3 (Recommendations For The Authors): 

Minor comments. 

Based on the Fzd4-Dvl binding experiment, the authors might state explicitly the possibility that Tspan12's relevance is entirely accounted for by extracellular ligand capture. 

We have stated this possibility explicitly in the discussion section (page 9, last paragraph). 

Page 4, 3rd paragraph. I suggest "To experimentally test this structural prediction..." rather than "validate". 

Thank you for this suggestion; we have replaced this wording. 

This next item is optional, but I hope that the authors will consider it. This manuscript provides an opportunity for the authors to be more expansive in their thinking, and to put their work into the larger context of ligand+receptor+accessory protein interactions. The authors describe the Wnt7a/7b-Gpr124-RECK system and the role of HSPs in Norrin and Wnt signaling, but perhaps they can also comment on non-Wnt ligand-receptor systems where accessory proteins are found. They might add a figure (or supplemental figure) with a schematic showing the roles of HSP and Gpr124-RECK, and some non-Wnt ligand-receptor systems. This would help to make the present work more widely influential.

Thank you for this suggestion. We have added a figure (Figure 6, discussed on page 10, paragraphs 2 and 3) and expanded our discussion to include other co-receptor systems. We have specifically focused on co-receptors that both capture ligands and interact with their primary receptor(s), thus delivering ligands to their receptors, as we have proposed for Tspan12. Within Wnt signaling, other co-receptor systems with this mechanism are RECK/Gpr124 (for Wnt7a/b) and Glypican-3. We found it interesting that this mechanism is also shared by several growth factor pathways with cystine knot ligands (like Norrin), so we have illustrated and mentioned three of these examples.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Zhang et al., presented an electrophysiology method to identify the layers of macaque visual cortex with high density Neuropixels 1.0 electrode. They found several electrophysiology signal profiles for high-resolution laminar discrimination and described a set of signal metrics for fine cortical layer identification.

Strengths:

There are two major strengths. One is the use of high density electrodes. The Neuropixels 1.0 probe has 20 um spacing electrodes, which can provide high resolution for cortical laminar identification. The second strength is the analysis. They found multiple electrophysiology signal profiles which can be used for laminar discrimination. Using this new method, they could identify the most thin layer in macaque V1. The data support their conclusion.

Weaknesses:

While this electrophysiology strategy is much easier to perform even in awake animals compared to histological staining methods, it provides an indirect estimation of cortical layers. A parallel histological study can provide a direct matching between the electrode signal features and cortical laminar locations. However, there are technical challenges, for example the distortions in both electrode penetration and tissue preparation may prevent a precise matching between electrode locations and cortical layers. In this case, additional micro wires electrodes binding with Neuropixels probe can be used to inject current and mark the locations of different depths in cortical tissue after recording.

While we agree that it would be helpful to adopt a more direct method for linking laminar changes observed with electrophysiology to anatomical layers observed in postmortem histology, we do not believe that the approach suggested by the reviewer would be particularly helpful. The approach suggested involves making lesions, which are known to be quite variable in size, asymmetric in shape, and do not have a predictable geometry relative to the location of the electrode tip. In contrast, our electrophysiology measures have identified clear boundaries which precisely match the known widths and relative positions of all the layers of V1, including layer 4A, which is only 50 microns thick, much smaller than the resolution of lesion methods.

Reviewer #2 (Public Review):

Summary:

This paper documents an attempt to accurately determine the locations and boundaries of the anatomically and functionally defined layers in macaque primary visual cortex using voltage signals recorded from a high-density electrode array that spans the full depth of cortex with contacts at 20 um spacing. First, the authors attempt to use current source density (CSD) analysis to determine layer locations, but they report a striking failure because the results vary greatly from one electrode penetration to the next and because the spatial resolution of the underlying local field potential (LFP) signal is coarse compared to the electrical contact spacing. The authors thus turn to examining higher frequency signals related to action potentials and provide evidence that these signals reflect changes in neuronal size and packing density, response latency and visual selectivity.

Strengths:

There is a lot of nice data to look at in this paper that shows interesting quantities as a function of depth in V1. Bringing all of these together offers the reader a rich data set: CSD, action potential shape, response power and coherence spectrum, and post-stimulus time response traces. Furthermore, data are displayed as a function of eye (dominant or non-dominant) and for achromatic and cone-isolating stimuli.

This paper takes a strong stand in pointing out weaknesses in the ability of CSD analysis to make consistent determinations about cortical layering in V1. Many researchers have found CSD to be problematic, and the observations here may be important to motivate other researchers to carry out rigorous comparisons and publish their results, even if they reflect negatively on the value of CSD analysis.

The paper provides a thoughtful, practical and comprehensive recipe for assigning traditional cortical layers based on easily-computed metrics from electrophysiological recordings in V1, and this is likely to be useful for electrophysiologists who are now more frequently using high-density electrode arrays.

Weaknesses:

Much effort is spent pointing out features that are well known, for example, the latency difference associated with different retinogeniculate pathways, the activity level differences associated with input layers, and the action potential shape differences associated with white vs. gray matter. These have been used for decades as indicators of depth and location of recordings in visual cortex as electrodes were carefully advanced. High density electrodes allow this type of data to now be collected in parallel, but at discrete, regular sampling points. Rather than showing examples of what is already accepted, the emphasis should be placed on developing a rigorous analysis of how variable vs. reproducible are quantitative metrics of these features across penetrations, as a function of distance or functional domain, and from animal to animal. Ultimately, a more quantitative approach to the question of consistency is needed to assess the value of the methods proposed here.

We thank the reviewer for suggesting the addition of quantitative metrics to allow more substantive comparisons between various measures within and between penetrations. We have added quantification and describe this in the context of more specific comments made by this reviewer. We have retained descriptions of metrics that are well established because they provide an important validation of our approaches and laminar assignments.

Another important piece of information for assessing the ability to determine layers from spiking activity is to carry out post-mortem histological processing so that the layer determination made in this paper could be compared to anatomical layering.

We are not aware of any approach that would provide such information at sufficient resolution. For example, it is well known that electrolytic lesions often do not match to the locations expected from electrophysiological changes observed with single electrodes. As noted above, our observation that the laminar changes in electrophysiology precisely match the known widths and relative positions of all the layers of V1, including layer 4A, provides confidence in our laminar assignments.

On line 162, the text states that there is a clear lack of consistency across penetrations, but why should there be consistency: how far apart in the cortex were the penetrations? How long were the electrodes allowed to settle before recording, how much damage was done to tissue during insertion? Do you have data taken over time - how consistent is the pattern across several hours, and how long was the time between the collection of the penetrations shown here?

Answers to most of these questions can be found within the manuscript text. We have added text describing distance between electrode penetrations (at least 1mm, typically far more) and added a figure which shows a map of the penetration locations. The Methods section describes electrode penetration methods to minimize damage and settling times of penetrations. Data are provided regarding changes in recordings over time (see Methods, Drift Correction). The stimuli used to generate the data described are presented within a total of 30 minutes or less, minimizing any changes that might occur due to electrode drift. There is a minimum of 3 hours between different penetrations from the same animal.

The impact of the paper is lessened because it emphasizes consistency but not in a consistent manner. Some demonstrations of consistency are shown for CSDs, but not quantified. Figure 4A is used to make a point about consistency in cell density, but across animals, whereas the previous text was pointing out inconsistency across penetrations. What if you took a 40 or 60 um column of tissue and computed cell density, then you would be comparing consistency across potentially similar scales. Overall, it is not clear how all of these different metrics compare quantitatively to each other in terms of consistency.

As noted above, we have now added quantitative comparisons of consistency between different metrics. It is unclear why the reviewer felt that we use Figure 4A to describe consistency. That figure was a photograph from a previous publication simply showing the known differences in neuron density that are used to define layers in anatomical studies. This was intended to introduce the reader to known laminar differences. At any rate, we have been unable to contact the previous publishers of that work to obtain permission to use the figure. So we have removed that figure as it is unnecessary to illustrate the known differences in cell density that are used to define layers. We have kept the citation so that interested readers can refer to the publication.

In many places, the text makes assertions that A is a consistent indicator of B, but then there appear to be clear counterexamples in the data shown in the figures. There is some sense that the reasoning is relying too much on examples, and not enough on statistical quantities.

Without reference to specific examples we are not able to address this point.

Overall

Overall, this paper makes a solid argument in favor of using action potentials and stimulus driven responses, instead of CSD measurements, to assign cortical layers to electrode contacts in V1. It is nice to look at the data in this paper and to read the authors' highly educated interpretation and speculation about how useful such measurements will be in general to make layer assignments. It is easy to agree with much of what they say, and to hope that in the future there will be reliable, quantitative methods to make meaningful segmentations of neurons in terms of their differentiated roles in cortical computation. How much this will end up corresponding to the canonical layer numbering that has been used for many decades now remains unclear.

Reviewer #3 (Public Review):

Summary:

Zhang et al. explored strategies for aligning electrophysiological recordings from high-density laminar electrode arrays (Neuropixels) with the pattern of lamination across cortical depth in macaque primary visual cortex (V1), with the goal of improving the spatial resolution of layer identification based on electrophysiological signals alone. The authors compare the current commonly used standard in the field - current source density (CSD) analysis - with a new set of measures largely derived from action potential (AP) frequency band signals. Individual AP band measures provide distinct cues about different landmarks or potential laminar boundaries, and together they are used to subdivide the spatial extent of array recordings into discrete layers, including the very thin layer 4A, a level of resolution unavailable when relying on CSD analysis alone for laminar identification. The authors compare the widths of the resulting subdivisions with previously reported anatomical measurements as evidence that layers have been accurately identified. This is a bit circular, given that they also use these anatomical measurements as guidelines limiting the boundary assignments; however, the strategy is overall sensible and the electrophysiological signatures used to identify layers are generally convincing. Furthermore, by varying the pattern of visual stimulation to target chromatically sensitive inputs known to be partially segregated by layer in V1, they show localized response patterns that lend confidence to their identification of particular sublayers.

The authors compellingly demonstrate the insufficiency of CSD analysis for precisely identifying fine laminar structure, and in some cases its limited accuracy at identifying coarse structure. CSD analysis produced inconsistent results across array penetrations and across visual stimulus conditions and was not improved in spatial resolution by sampling at high density with Neuropixels probes. Instead, in order to generate a typical, informative pattern of current sources and sinks across layers, the LFP signals from the Neuropixels arrays required spatial smoothing or subsampling to approximately match the coarser (50-100 µm) spacing of other laminar arrays. Even with smoothing, the resulting CSDs in some cases predicted laminar boundaries that were inconsistent with boundaries estimated using other measures and/or unlikely given the typical sizes of individual layers in macaque V1. This point alone provides an important insight for others seeking to link their own laminar array recordings to cortical layers.

They next offer a set of measures based on analysis of AP band signals. These measures include analyses of the density, average signal spread, and spike waveforms of single- and multi-units identified through spike sorting, as well as analyses of AP band power spectra and local coherence profiles across recording depth. The power spectrum measures in particular yield compact peaks at particular depths, albeit with some variation across penetrations, whereas the waveform measures most convincingly identified the layer 6-white matter transition. In general, some of the new measures yield inconsistent patterns across penetrations, and some of the authors' explanations of these analyses draw intriguing but rather speculative connections to properties of anatomy and/or responsivity. However, taken as a group, the set of AP band analyses appear sufficient to determine the layer 6-white matter transition with precision and to delineate intermediate transition points likely to correspond to actual layer boundaries.

Strengths:

The authors convincingly demonstrate the potential to resolve putative laminar boundaries using only electrophysiological recordings from Neuropixels arrays. This is particularly useful given that histological information is often unavailable for chronic recordings. They make a clear case that CSD analysis is insufficient to resolve the lamination pattern with the desired precision and offer a thoughtful set of alternative analyses, along with an order in which to consider multiple cues in order to facilitate others' adoption of the strategy. The widths of the resulting layers bear a sensible resemblance to the expected widths identified by prior anatomical measurements, and at least in some cases there are satisfying signatures of chromatic visual sensitivity and latency differences across layers that are predicted by the known connectivity of the corresponding layers. Thus, the proposed analytical toolkit appears to work well for macaque V1 and has strong potential to generalize to use in other cortical regions, though area-targeted selection of stimuli may be required.

Weaknesses:

The waveform measures, and in particular the unit density distribution, are likely to be sensitive to the criteria used for spike sorting, which differ widely among experimenters/groups, and this may limit the usefulness of this particular measure for others in the community. The analysis of detected unit density yields fluctuations across cortical depth which the authors attribute to variations in neural density across layers; however, these patterns seemed particularly variable across penetrations and did not consistently yield peaks at depths that should have high neuronal density, such as layer 2. Therefore, this measure has limited interpretability.

While we agree that our electrophysiological measure of unit density does not strictly reflect anatomical neuronal density, we would like to remind the reader that we use this measure only to roughly estimate the correspondence between changes in density and likely layer assignments. We rely on other measures (e.g. AP power, AP power changes in response to visual stimuli) that have sharp borders and more clear transitions to assign laminar boundaries. Further, as noted in the reviewer’s list of strengths, the laminar assignments made with these measures are cross validated by differences in response latencies and sensitivity to different types of stimuli that are observed at different electrode depths.

More generally, although the sizes of identified layers comport with typical sizes identified anatomically, a more powerful confirmation would be a direct per-penetration comparison with histologically identified boundaries. Ultimately, the absence of this type of independent confirmation limits the strength of their claim that veridical laminar boundaries can be identified from electrophysiological signals alone.

As we have noted in response to similar comments from other reviewers, we are not aware of a method that would make this possible with sufficient resolution.

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

The reviewers have indicated that their assessment would potentially be stronger if their advice for quantitative, statistically validated comparisons was followed, for example, to demonstrate variability or consistency of certain measures that are currently only asserted. Also, if available, some histological confirmation would be beneficial. It was requested that the use and modification of the layering from Balaram & Kaas is addressed, as well as dealing with inconsistencies in the scale bars on those figures. There are two figure permission issues that need to be resolved prior to publication: Balaram & Kaas 2014 in Fig 1A, Kelly & Hawken 2017 in Fig. 4A.

Please see detailed responses to reviewer comments below. We have added new supplemental figures to quantitatively compare variability among metrics. As noted above, the suggested addition of data linking the electrophysiology directly to anatomical observations of laminar borders from the same electrode penetration is not feasible. The figure reused in Figure 1A is from open-access (CC BY) publication (Balaram & Kaas 2014). After reexamining the figure in the original study, we found that the inferred scale bar would give an obviously inaccurate result. So, we decided to remove the scale bar in Figure 1A. We haven’t received any reply from Springer Nature for Figure 4A permission, so we decided to remove the reused figure from our article (Kelly & Hawken 2017).

Reviewer #1 (Recommendations For The Authors):<br /> Figure 4A has a different scale to Figure 4B-4F. It is better to add dashed lines to indicate the relationship between the cortical layers or overall range from Figure 4A to the corresponding layers in 4B to 4F.

The reused figure in Figure 4A is removed due to permission issue. See also comments above.

Reviewer #2 (Recommendations For The Authors):

General comments

This paper demonstrates that voltage signals in frequency bands higher than those used for LFP/CSD analysis can be used from high-density electrical contact recording to generate a map of cortical layering in macaque V1 at a higher spatial resolution than previously attained.

My main concern is that much of this paper seems to show that properties of voltage signals recorded by electrodes change with depth in V1. This of course is well known and has been mapped by many who have advanced a single electrode micron-by-micron through the cortex, listening and recording as they go. Figure 4 shows that spike shapes can give a clear indication of GM to WM borders, and this is certainly true and well known. Figures 5 and 6 show that activity level on electrodes can indicate layers related to LGN input, and this is known. Figure 7 shows that latencies vary with layer, and this is certainly true as we know. A main point seems to be that CSD is highly inconsistent. This is important to know if CSD is simply never going to be a good measure for layering in V1, but it would require quantification and statistics to make a fair comparison.

We are glad to see that the reviewer understands that changes in electrical signals across layers are well known and are expected to have particular traits that change across layers. We do not claim that have discovered anything that is unexpected or unknown. Instead, we introduce quantitative measures that are sensitive to these known differences (historically, often just heard with an audio monitor e.g. “LGN axon hash”). While the primary aim of this paper is not to show that Neuropixels probes can record some voltage signal properties that cannot be recorded with a single electrode before, we would like to point out that multi-electrode arrays have a very different sampling bias and also allow comparisons of simultaneous recordings across contacts with known fixed distances between them. For example our measure of “unit spread” could not be estimated with a single electrode.

We’ve added Figure S3 to show quantitative comparison of variation between CSD and AP metrics. These figures add support to our prior, more anecdotal descriptions showing that CSDs are inconsistent and lack the resolution needed to identify thin layers.

Some things are not explained very clearly. Like achromatic regions, and eye dominance - these are not quantified, and we don't know if they are mutually consistent - are achromatic/chromatic the same when tested through separate eyes? How consistent are these basic definitions? How definitive are they?

The quantitative definitions of achromatic region/COFD and eye dominance column can be found in our previous paper (Li et al., 2022) cited in this article. The main theme of this study is to develop a strategy for accurately identifying layers, the more detailed functional analysis will be described in future publications.

Specific comments

The abstract refers to CSD analysis and CSD signals. Can you be more precise - do you aim to say that LFP signals in certain frequency bands are already known to lack spatial localization, or are you claiming to be showing that LFP signals lack spatial resolution? A major point of the results appears to be lack of consistency of CSD, but I do not see that in the Abstract. The first sentence in the abstract appears to be questionable based on the results shown here for V1.

We have updated the Abstract to minimize confusion and misunderstanding.

Scale bar on Fig 1A implies that layers 2-5 are nearly 3 mm thick. Can you explain this thickness? Other figures here suggest layers 1-6 is less than 2 mm thick. Note, in a paper by the same authors (Balaram et al) the scale bar (100 um, Figure 4) on similar macaque tissue suggests that the cortex is much thinner than this. Perhaps neither is correct, but you should attempt to determine an approximately accurate scale. The text defines granular as Layer 4, but the scale bar in A implies layer 4 is 1 mm thick, but this does not match the ~0.5 mm thickness consistent with Figure 1E, F. The text states that L4A is less then 100 um thick, but the markings and scale bar in Figure 1A suggests that it could be more than 100 um thick.

We thank the reviewer for pointing out that there are clearly errors in the scale bars used in these previously published figures from another group. In the original figure 1(Balaram & Kaas 2014), histological slices were all scaled to one of the samples (Chimpanzee) without scale bar. After reexamining the scale bar we derived based on figure 2 of the original study, we found the same problem. Since relative widths of layers are more important than absolute widths in our study, we decided to remove the scale bar that we had derived and added to the Figure 1A.

Line 157. Fix "The most commonly visual stimulus"

Text has been changed

Line 161. Fix "through dominate eye"

Text has been changed

Line 166. Please specify if the methods established and validated below are histological, or tell something about their nature here.

The Abstract and Introduction already described the nature of our methods

Line 184. Text is mixing 'dominant' and 'dominate', the former is better.

Text has been changed accordingly

Line 188. Can you clarify "beyond the time before a new stimulus transition". Are you generally referring to the fact that neuronal responses outlast the time between changes in the stimulus?

That is correct. We are referring to the fact that neuronal responses outlast the time between changes in the stimulus. We have edited the text for clarity.

Line 196. Fix "dominate eye" in two places.

Text has been changed

Line 196. The text seems to imply it is striking to find different response patterns for the two eyes, but given the OD columns, why should this be surprising?

Since we didn’t find systematic comparison for CSD depth profiles of dominant/non-dominant eyes, or black/white in the past studies, we just describe what we saw in our data. The rational for testing each eye is that it is known that LGN projections from two eyes remain separated in direct input layer of V1, so comparing CSDs from two eyes could potentially help identifying input layers, such as L4C. Here we provide evidence showing that CSD profiles from two eyes deviate from naive expectations. For example, CSDs from black stimulus show less variation between two eyes, whereas CSDs from white stimulus could range from similar profile to drastically different ones across eyes.

Line 198. Text like, "The most consistent..." is stating overall conclusions drawn by the authors before pointing the reader specifically to the evidence or the quantification that supports the statement.

We’ve adjusted the text pointing to Figure S2, where depth profiles of all penetrations are visualized, and a newly added Figure S3, where the coefficients of variation for several metric profiles were shown.

Line 200. "white stimulus is more variable" - the text does not tell us where/how this is supported with quantitative analysis/statistics.

We’ve adjusted the text pointing to Figure S2, S3

The metric in 4B is not explained, the text mentions the plot but the reader is unable to make any judgement without knowledge of the method, nor any estimate of error bars.

The figure is first mentioned in section: Unit Density, and text in this section already described the definition of neuron density and unit density.  We’ve also modified the text pointing to the method section for details.

Line 236. The text states the peak corresponds to L4C, but does not explain how the layer lines were determined.

As described early in the CSD section, all layer boundaries are determined following the guide which layouts the strategy for how to draw borders by combining all metrics.

At Line 296 the spike metrics section ends without providing a clear quantification of how useful the metrics will be. It is clear that the GM to WM boundary can be identified, but that can be found with single electrodes as well, as neurophysiologists get to see/hear the change in waveform as the electrode is advanced in even finer spatial increments than the 20 um spacing of the contacts here.

The aim of this study is to develop an approach for accurately delineating layers simultaneously. The metrics we explored are considered estimation of well-known properties, so they can provide support for the correctness we hope to achieve. Here we first demonstrate the usefulness and later show the average across penetrations (Figure 9C-F). We are less concerned in quantification of how different factors affect precision and consistency of these metrics or how useful a single metric is, but rather, as described in the guide section, whether we can delineate all layers given all metrics.

Line 302-306. Why this statement is made here is unclear, it interrupts the flow for a reason that perhaps will be explained later.

This statement notes the insensitivity of this measure to temporal differences, introducing the value of incorporating a measure of how AP powers changes over time in the next section of the manuscript.

Line 311. What is the reason to speculate about no canceling because of temporal overlap? Are you assuming a very sparse multi unit firing rate such that collisions do not happen?

Here we describe a simple theoretical model in which spike waveforms only add without cancelling, then the power would be proportional to the number of spikes. In reality, spike waveform sometimes cancels causing the theoretical relationship to deteriorate to some degree.

Lines 327-346. There is a considerable amount of speculation and arguing based on particular examples and there is a lack of quantification. Neuron density is mentioned, but not firing rate. would responses from fewer neurons with higher firing rate not be similar to more neurons with lower firing rates?

According to the theoretical model we described, power is proportional to numbers of spikes which then depend on both neuron density and firing rate. So fewer neurons with higher firing rate would generate similar power to more neurons with lower firing rate. We’ve expanded the explanation of the model and added Figure S4 about the depth profile of firing rate. Text has also been adjusted pointing to the Figure S2, S3 about quantitively comparisons of variability.

Line 348 states there is a precise link between properties and cortical layers, but the manuscript has not, up to this point, shown how that link was determined or quantified it.

Through our generative model of power and the similarity between depth profile of firing rate and depth profile of neuron density (Figure S4), depth profile of power can be used to approximate depth profile of neuron density which is known to be closely correlated to cortical layering.

Line 350. What is meant by "stochastic variability"?

The text essentially says distances from electrode contact to nearby cell bodies were random, so closer cells have higher spike amplitudes and in turn result in higher power on a channel.

The figures showing the two metrics, Pf and Cf, should be shown for the same data sets. The markings indicate that Fig 5 and Fig 6 show results from non-overlapping data sets. This does not build confidence about the results in the paper.

Here we use typical profiles to demonstrate the characteristics of the power spectrum/coherence spectrum because of the variation across penetrations. We show later, in the guide section, all metrics for one penetration (another two cases in supplemental figures) and how to combine all metrics to derive layer delineations.

Line 375 the statement is somewhat vague, "there are nevertheless sometimes cases where they can resolve uncertainties," can you please provide some quantitative support?

We provided 3 examples in Figure 6, and more examples are shown in Figure 8, Figure S5, S6.

Line 379. I believe the change you want to describe here is a change associated with a transition in the visual stimulus. It would be good to clarify this in the first several sentences here. Baseline can mean different things. I got the impression that your stimuli flip between states at a rate fast enough that signals do not really have time to return to a baseline.

We rephrased the sentence to describe the metric more precisely. A pair of uniform colors flipping in 1.5 second intervals is usually long enough for spiking activities to decay to a saturated level.

This section (379 - 398) continues a qualitative show-and-tell feel. There appears to be a lot of variability across the examples in Figure 7. How could you try to quantify this variability versus the variability in LFP? And, in this section overall, the text and figure legend don't really describe what the baseline is.

Text adjustments are made to briefly describe the baseline window and point to the Method section where definitions are described in detail. We’ve added Figure S3 together with Figure S2 to address the variability across penetrations, stimuli, and metrics.

Line 405 - 415. The discussion here does not consider that layers may not have well defined boundaries, the text gives the impression that there is some ultimate ground truth to which the metrics are being compared, but that may not be accurate.

Except for a few layers/sublayers, such as L2, L3A, L3B, most layer boundaries of neocortex are well defined (Figure 1A) and histological staining of neurons/density and correlated changes in chemical content show very sharp transitions. The best of these staining methods is cytochrome oxidase, which shows sharp borders at the top and bottom of layer 4A, top and bottom of layer 4C, and the layer 5/6 border. There is also a sharp transition in neuronal cell body size and density at the top and bottom of layer 4Cb. The definition and delineation of all possible layers are constantly being refined, especially by accumulated knowledge of genetic markers of different cell types and connection patterns. In our study, we develop metrics to estimate well known anatomical and functional properties of different layers. We have also discussed layer boundaries that have been ambiguous to date and explained the reason and criteria to resolve them.

Line 423. The text references Figure 1A in stating that relative thickness and position is crucial, but FIgure 1A does not provide that information and does not explain how it might be determined, or how much of a consensus there is. Also, the text does not consider that the electrode may go through the cortex at oblique angles, and not the same angle in each layer, and the relative thickness may not be a dependable reference.

There are numerous studies that describe criteria to delineate cortical layers, the referenced article (Balaram & Kaas 2014) is used here as an example. We are not aware of any publication that has systematically compared the relative thickness of layers across the V1 surface of a given animal or across animals. Nevertheless, it is clear from the literature that there is considerable similarity across animals. Accordingly, we cannot know what the source of variability in overall cortical thickness in our samples is, but we do see considerable consistency in the relative thickness of the layers we infer from our measures. We illustrate the differences that we see across penetrations and consider likely causes, such as the extent to which the coverslip pressing down on the cortex might differentially compress the cortex at different locations within the chamber.

The angle deviation of probe from surface will not change the relative thickness of layers, and the rigid linear probe is unlikely to bend in the cortex.

Line 433. The term "Coherence" is used, clarify is this is you Cf from Figure 6. The text states, "marked decrease at the bottom of layer 6". Please clarify this, I do not see that in Figure 6.

Text has been adjusted.

In Figure 6, the locations of the lines between L1 and 2 do not seem to be consistent with respect to the subtle changes in light blue shading, across all three examples, yet the text on line 436 states that there is a clear transition.

We feel that the language used accurately reflects what is shown in the figure. While the transition is not sharp, it is clear that there is a transition. This transition is not used to define this laminar border. We have edited the text to clarify that the L1/2 border is better defined based on the change in AP power which shows a sharp transition (Figure 7). 

The text states that the boundary is also "always clear" from metrics... and sites Figure 5, but I do not see that this boundary is clear for all three examples in Figure 5.

Text has been adjusted.

Line 438. The text states that "it is not unusual for unit density to fall to zero below the L1/2 border (Figure 8E)", but surprisingly, the line in Figure 8 E does not even cover the indicated boundary between L1 and L2.

At this point, the number of statements in the text that do not clearly and precisely correlate to the data in the figures is worrisome, and I think you could lose the confidence of readers at this point.

We do not see any inconstancy between what is stated in our text and what is noted by the reviewer. The termination of the blue line corresponds to the location where no units are detected. This is the location where “unit density falls to zero”.  In this example, no units resolved through spike sorting until ~100mm beneath the L1/L2 boundary, which is exactly zero unity density (Figure 8E). That there are electrical signals in this region is clear from the AP power change (Figure 8C) which also shows the location of the L1/L2 border.

Line 448. Text states that the 6A/B border is defined by a sharp boundary in AP power, but Figure 8A "AP power spectrum" does not show a sharp change at the A/B line. There is a peak in this metric in the middle to upper middle of 6A, but nothing so sharp to define a boundary between distinct layers, at least for penetration A2.

Text has been adjusted.

In Figure 8, the layer labels are not clear, whereas they are reasonably clear in the other figures.

This is a technical problem regarding vector graphics that were not properly converted in PDF generation. We will upload each high-quality vector graphics when we finalize the version of record.

The text emphasizes differences in L4B and L4C with respect to average power and coherence, but the transition seems a bit gradual from layer 3B to 4C in some examples in Figure 6. And in Figure 5, A3, there doesn't appear to be any particular transition along the line between 4B and 4C.

In this guide section, we pointed out early that some metrics are good for some boundaries and variation exists between penetrations. We’ve expanded text emphasizing the importance of timing differences in DP/P for differentiating sublayers in L4. Lastly, in case of several unresolvable boundaries given all the metrics, the prior knowledge of relative thickness should be used.

Line 466 provides prescriptions in absolute linear distances, but this is unwise given that cortex may be crossed at oblique angles by electrodes, particularly for parts of V1 that are not on the surface of the brain. Other parts of the text have emphasized relative measurements.

Text has been changed using relative measurements.

Line 507. The text says 9C and 4A are a good match, but the match does not look that good (4A has substantial dips at 0.5 and 0.75, and substantial peaks), and there is no quantification of fit. The error bars on 9C do not help show the variability across penetrations, they appear to be SEM, which shows that error bars get smaller as you average more data. It would seem more important to understand what is the variance in the density from one penetration to the next compared to the variance in density across layers.

We have replaced “good match” with “roughly corresponds”. We note that we do not use unit density as a metric for identification of laminar borders and instead show that the expected locations of layers with higher neuronal density correspond to the locations where there are similar changes in unit density. It should be noted that Figure 9C is an average across many penetrations so should not be expected to show transitions that are as sharp in individual penetrations. Because of the figure permission issue, we have removed Figure 4A, and changed the text accordingly.

Figure 9C-F show a lot of variability in the individual curves (dim gray lines) compared to the overall average. Does this show that these metrics are not reliable indicators at the level of single penetration, but show some trends across larger averages?

In the beginning of the guide, we emphasized that all metrics should be combined for individual penetration, because some metrics are only reliable for delineating certain layer boundaries and the quality of data for the various measures varies between penetrations. The penetration average serves the same purpose explained in the previous question as an indicator that our layer delineation was not far off.

The discussion mentions improvements in layer identification made here. Did this work check the assignments for these penetration against assignments made based on some form of ground truth? Previous methods would advance electrodes steadily, and make lesions, and carry out histology. Is there any way to tell how this method would compare to that?

Even electrolytic lesions do not necessarily reveal ground truth and can be quite misleading. And their resolution is limited by lesion size. Lesions are typically variable in size, asymmetric and have variable shape and position relative to the location of the electrode tip, likely affected by the quality and location of electrical grounding and variations in current flow due to locations of blood vessels. A review of the published literature with electrode lesions shows that electrophysiological transitions are likely a far more accurate indicator of recording locations than post-mortem histology from electrolytic lesions. It is extremely rare for the locations of lesions to be precisely aligned to expected laminar transitions. See for example Chatterjee et al (Nature 2004). Also see several manuscripts from the Shapley lab. The lone rare exception of which we are aware is Blasdel and Fitzpatrick1984 in which consistently small and round lesions were produced and even these would be too large (~100 microns) to accurately identify layers if it were not for the fact that the electrode penetrations were very long and tangential to the cortical layers. 

Reviewer #3 (Recommendations For The Authors):

- The authors say (lines 360-362) that "Assuming spikes of a neuron spread to at least two adjacent recording channels, then the coherence between the two channels would be directly proportional to number of spikes, independent of spike amplitude." Has this been demonstrated? Very large amplitude spikes should show up on more channels than small amplitude spikes. Do waveform amplitudes and unit densities from the spike waveform analyses show consistent relationships to the power and/or coherence distributions over depth across penetrations?

This part of the manuscript is providing a theoretical rational for what might be expected to affect the measures that we have derived. That is why we begin by stating that we are making an assumption. The answers to the reviewer’s questions are not known and have not been demonstrated. By beginning with this theoretical preface, we can point to cases where the data match these expectations as well as other cases where the data differ from the theoretical expectations.

Coherence, by definition, is a normalized metric that is insensitive to amplitude. Spike amplitude mainly depends on how close the signal source is to electrode, and spike spread mainly depends on cell body size and shape given the same distance to electrode. Therefore, a very large spike amplitude could stem from a very close small cell to electrode, but would result in a small spike spread, especially axonal spikes (Figure 4B, red spike). Spike amplitudes on average are higher in L4C which matches the expectation that higher cell density would result, on average, closer cell body to electrode (Figure S4A). Nonetheless, the high-density small cell bodies in L4C result in a small spike spread (Figure 9D).

- I suggest clarifying what is defined as the baseline window for the ΔP/P measure - is it the entire 10-150 ms response window used for the power spectrum analysis?

Text adjustments are made in the Methods where the time windows are defined at the beginning of the CSD section. Only temporal change metrics (ΔCSD and ΔP/P) use the baseline window ([-40, 10]ms). The other two spectrum metrics (Power and Coherence) use the response window ([10, 150]ms).

- Firing rate differs by cell type and, on average, differs by layer in V1. Many layer 2/3 neurons, for example, have low maximum firing rates when driven with optimized achromatic grating stimuli. To the extent that the generative models explaining the sources of power and coherence signals rely on the assumption that firing rates are matched across cortical depth, these models may be inaccurate. This assumption is declared only subtly, and late in the paper, but it is relevant to earlier claims.

Text adjustments are made to explicitly describe the possibility that uneven depth profile of firing rate could counteract the depth profile of neuron density, resulting distorted or even a flat depth profile of power/coherence that deviates far from the depth profile of neuron density. In a newly added Figure S4, we first show the average firing rate profile during a set of stimuli (uniform color, static/drifting, achromatic/chromatic gratings), then specifically the PSTHs of the same stimuli shown in this study. It can be seen that layers receiving direct LGN inputs tend to fire at a higher rate (L4C, L6A). Firing rates in the PSTHs either roughly match across layers or are much higher in the densely packed layers. Therefore, the depth profile of firing rate contributes to rather than counteracting that of neuron density, enhancing the utility of the power/coherence profile for identification of correct layer boundaries.

- Given the acute preparation used for recordings, I wonder whether tissue is available for histological evaluation. Although the layers identified are generally appropriate in relative size, it would be particularly compelling if the authors could demonstrate that the fraction of the cortical thickness occupied by each layer corresponded to the proportion occupied by that layer along the probe trajectory in histological sections. This would lend strength to the claim that these analyses can be used to identify layers in the absence of histology. Furthermore, variations in apparent cortical thickness could arise from different degrees of deviation from surface normal approach angles, which might be apparent by evaluation of histological material. I would add that variation in thickness on the scale shown in Fig. S4 is more likely to have an explanation of this kind.

To serve other purposes unrelated to this study (identification of CO blobs), we cut the postmortem tissue in horizontal slices, so the histological comparison suggested cannot be made. The cortical thickness measured in this study had been affected not only by the angle deviation from the surface normal but also the swelling and compression of cortex. Nevertheless, evaluating the absolute thickness of cortex is not the main purpose of this study.

Text and figure suggestions:

- Fig 1A has been modified from Balaram & Kaas (2014) to revert to the Brodmann nomenclature scheme they argue against using in that paper; I wonder if they would object to this modification without explanation. Related, in the main text the authors initially refer to layers using Brodmann's labels with a secondary scheme (Hassler's) in parentheses and later drop the parenthetical labels; these conventions are not described or explained. Readers less familiar with the multiple nomenclature schemes for monkey V1 layers might be confused by the multiple labels without context, and could benefit from a brief description of the convention the authors have adopted.

Throughout our article, we only used Brodmann’s naming convention because it has historically been adopted for old world monkey which we use in our study, whereas Hassler’s naming convention is more commonly used for new world monkey. Different naming conventions do not change our result, and it is out of scope for our study to discuss which nomenclature is more appropriate.

- References to "dominate eye" throughout the text and figure legends should be replaced with "dominant eye."

It has been changed throughout the article.

- It is a bit odd to duplicate the same example in Fig. 2C and 2E. Perhaps a unique example would be a better use of the space.

Here we first demonstrate the filtering effect, then compare profiles across different penetrations. The same example bridges the transition allowing side-by-side comparison.

- The legend for Fig. 3 might be clearer if it simply listed the stimulus transitions for each column left to right, i.e. "black to white (non-dominant eye), white to black (non-dominant eye), black to white (dominant eye), ..."

We feel that the icons are helpful. Here we want to show the stimulus colors directly to readers.

- The misalignment between Fig. 4A vs. 4B-F, combined with the very small font size of the layer labels in Fig. 4B-F, make the visual comparison difficult. In Figs. 7 and 8, layer labels (and most labels in general) are much too small and/or low resolution to read easily. Overall, I would recommend increasing font size of labels in figures throughout the paper.

The reused figure in Figure 4A is removed due to permission issue. Font sizes are adjusted.

- Line 591 "using of high-density probes" should be "using high-density probes"

Text has been changed accordingly

Author response:

The following is the authors’ response to the original reviews.

Response to Editor and Reviewer Comments:

Many thanks to the editor and reviewers for the thoughtful assessment of our manuscript “Commissureless acts as a substrate adapter in a conserved Nedd4 E3 ubiquitin ligase pathway to promote axon growth across the midline.” Thank you also for the positive comments about the quality of our writing, and for deeming our study rigorous and thorough. We are very pleased that, overall, you believe our combination of genetic and biochemical approaches offers useful insight into the mechanism of Robo regulation at the Drosophila embryonic midline and effectively reconciles the contradictory findings of previous studies done in this field.

Response to the previous Public Reviews:

We appreciate the concerns expressed by the reviewers and the suggestions of areas in which the study and manuscript could be improved. The reviewer suggestions were very helpful as we revised our manuscript in order to strengthen our mechanistic understanding of Robo downregulation and better characterize the role Nedd4 plays in this process. We strongly agree with Reviewer 1 that our insight into the mechanism of Robo downregulation via Comm would be much stronger had we not solely relied on overexpression experiments to investigate the effects of PY motif mutations on Comm function. While it is outside the scope of this particular paper, we appreciate your suggestion to use gene editing to investigate the role of PY motif mutation on endogenous comm function and believe this would be a useful question to address in future papers. In addition to this concern, both reviewers identified additional opportunities to strengthen the paper. We have done our best to incorporate reviewer suggestions and will outline how we addressed the following four areas that were identified by both reviewers as areas where additional data could strengthen our conclusions:

(1) Additional experiments to examine Comm and Robo1 localization in vivo: Characterizing Robo localization in vivo when co-expressed with PY-mutant Comm variants.

(2) Testing biochemical interactions in embryonic protein extracts: Examining the biochemical interaction between Robo, Comm, and Nedd4 in a more biologically relevant context than cell culture.

(3) Additional genetic interaction experiments: A) Investigating whether Nedd4 overexpression enhances the Comm G.O.F phenotype of enhanced ectopic crossing. B) Testing for additional genetic interactions with comm.

(4) Editing the text of the manuscript for clarity.

(1) Characterizing Robo localization in vivo when co-expressed with Comm variants.

In the first version of our manuscript, we characterized the localization of wild-type and PY mutant Comm variants expressed in apterous neurons (Figure 5C), but did not examine how these variants of Comm affected localization of their cargo Robo1. To address this gap, we co-expressed 10X UAS Comm-myc (WT, 1PY, 2PY) with 10X UAS Robo-HA under the ap gal4 driver, visualized Comm and Robo by immunostaining for Myc and HA, and measured colocalization between Comm and Robo. We found that Robo colocalizes equally with all comm variants and that its expression pattern mimics that of the Comm variant with which it is expressed. We observe that Robo is restricted to cell bodies when overexpressed with WT Comm but “leaks out” into axons when co-expressed with Comm 1PY or 2PY. This finding suggests that PY motifs are not only required for effective Comm localization to the appropriate cellular areas, but also for proper routing of its cargo, Robo1. These new data are presented in a new supplemental figure: Figure S3.

(2) Examining the biochemical interaction between Robo, Comm, and Nedd4 in vivo.

To examine biochemical interaction between Comm, Robo, and Nedd4 in a more biologically relevant context, we performed immunoprecipitations in fly embryonic lysate prepared from the following categories: WT, elav gal4: 5X UAS Comm-myc WT, and elav gal4: 5X UAS Comm-myc WT + 10X UAS Nedd4-HA. We performed immunoprecipitation for myc (Comm), and blotted for endogenous Robo, Myc (Comm), and HA (Nedd4). Corroborating our results in cell culture (Figure 7 A-C), we were able to pull down a three-protein complex consisting of Comm, Nedd4 and Robo in embryonic fly tissue. These new data are presented in a new supplemental figure: Figure S8.

(3) Investigating additional genetic interactions between Comm and Nedd4.

A) In our submitted manuscript, we demonstrated that overexpression of Nedd4 enhances Comm-induced downregulation of Robo levels (Figure 7 D-G). To determine whether Nedd4 also increases ectopic crossing, which is a morphological output of Comm activity/Robo downregulation, we analyzed nerve cord phenotypes in embryos from the following categories: WT, embryos expressing WT Comm under the elav gal4, and embryos co-expressing WT Comm and Nedd4 under the elav gal4 driver. We measured nerve cord widths and sorted them into three different “bins” of phenotypic severity, with more severe phenotypes being characterized by thinner nerve cords. We find that the distribution of phenotypes in embryos expressing Comm alone differs significantly from embryos expressing Comm + Nedd4, with the latter shifted toward more severe/thinner phenotypic classes. In addition to examining nerve cord width, we investigated whether Nedd4 can enhance collapse of the nerve cord segments (defined by loss of negative space within the segment) induced by Comm overexpression. We determined percentage of collapsed nerve cord segments and divided these values into three phenotypic classes: no collapse, partial collapse, and total collapse. The distribution of phenotypes in embryos co-expressing Nedd4 and Comm differs significantly from those expressing Comm alone. In the Comm expressing population, we only observe nerve cords with no or partial collapse, but in flies co-expressing Comm and Nedd4 we observe the more severe complete collapse phenotype. These findings suggest that addition of Nedd4 enhances the Comm gain of function phenotype both by further reducing nerve cord width and increasing the occurrence of defects related to ectopic crossing. These new data are presented in a new supplemental figure: Figure S9.

B) The reviewers also suggested additional genetic interaction experiments between Nedd4 and Comm. It was suggested that we included experiments to look at Nedd4 manipulations in Comm null mutant backgrounds. However, given the complete penetrance and expressivity of the Comm null mutation in which no axons cross the midline, these experiments would not be informative. As an alternative, we attempted to use the described hypomorphic Comm allele, but here too, the baseline commissural axon guidance defects are too strong to allow meaningful detection of enhanced phenotypes. Finally, we tested whether removing one copy of comm could reveal phenotypes in the nedd4 zygotic mutants, but we did not detect defects. This is perhaps unsurprising given that comm heterozygotes have no detectable midline crossing defects.

(4) Text edits.

We have made a variety of changes to decrease ambiguity in the text and create a more user-friendly experience for the reader. In the text, as opposed to just the figures, we now explicitly state whether we use 5X or 10X UAS constructs for each of our overexpression constructs. We also edited all mentions of the truncated frazzled construct (FraDc) so that they are uniform. We have also edited all mentions of MiMIC so that they are uniform. In addition, we answer a few questions the reviewers posed. First, we clarify that S2R+ cells express endogenous Comm at very low levels. In addition, we clarify about how we know expression levels are similar across the three Comm variants by explaining that transgenes incorporated into the fly genome by targeted insertion into the same location on the third chromosome.

We hope that these changes adequately address reviewer concerns, strengthen our study, and enhance readability of the paper. We appreciate the time you took to evaluate our manuscript and the thoughtful commentary and suggestions that you provided.

Author response:

Public Reviews:

Reviewer #1 (Public review):

This work addresses an important question in the field of Drosophila aggression and mating- prior social isolation is known to increase aggression in males by increased lunging, which is suppressed by group housing (GH). However, it is also known that single-housed (SH) males, despite their higher attempts to court females, are less successful. Here, Gao et al., developed a modified aggression assay, to address this issue by recording aggression in Drosophila males for 2 hours, over a virgin female which is immobilized by burying its head in the food. They found that while SH males frequently lunge in this assay, GH males switch to higher intensity but very low-frequency tussling. Constitutive neuronal silencing and activation experiments implicate cVA sensing Or67d neurons promoting high-frequency lunging, similar to earlier studies, whereas Or47b neurons promote low-frequency but higher intensity tussling. Using optogenetic activation they found that three pairs of pC1 neurons- pC1SS2 increase tussling. While P1a neurons, previously implicated in promoting aggression and courtship, did not increase tussling in optogenetic activation (in the dark), they could promote aggressive tussling in thermogenetic activation carried out in the presence of visible light. It was further suggested, using a further modified aggression assay that GH males use increased tussling and are able to maintain territorial control, providing them mating advantage over SI males and this may partially overcome the effect of aging in GH males.

Strengths:

Using a series of clever neurogenetic and behavioral approaches, subsets of ORNs and pC1 neurons were implicated in promoting tussling behaviors. The authors devised a new paradigm to assay for territory control which appears better than earlier paradigms that used a food cup (Chen et al, 2002), as this new assay is relatively clutter-free, and can be eventually automated using computer vision approaches. The manuscript is generally well-written, and the claims made are largely supported by the data.

Thank you for your precise summary of our study and being very positive on the novelty and significance of the study.

Weaknesses:

I have a few concerns regarding some of the evidence presented and claims made as well as a description of the methodology, which needs to be clarified and extended further.

(1) Typical paradigms for assaying aggression in Drosophila males last for 20-30 minutes in the presence of nutritious food/yeast paste/females or all of these (Chen et al. 2002, Nilsen et al., 2004, Dierick et al. 2007, Dankert et al., 2009, Certel & Kravitz 2012). The paradigm described in Figure 1 A, while important and more amenable for video recording and computational analysis, seems a modification of the assay from Kravitz lab (Chen et al., 2002), which involved using a female over which males fight on a food cup. The modifications include a flat surface with a central food patch and a female with its head buried in the food, (fixed female) and much longer adaptation and recording times respectively (30 minutes, 2 hours), so in that sense, this is not a 'new' paradigm but a modification of an existing paradigm and its description as new should be appropriately toned down. It would also be important to cite these earlier studies appropriately while describing the assay.

We will tone down the description and cite related references.

(2) Lunging is described as a 'low intensity' aggression (line 111 and associated text), however, it is considered a mid to high-intensity aggressive behavior, as compared to other lower-intensity behaviors such as wing flicks, chase, and fencing. Lunging therefore is lower in intensity 'relative' to higher intensity tussling but not in absolute terms and it should be mentioned clearly.

Ww will textually address this issue.

(3) It is often difficult to distinguish faithfully between boxing and tussling and therefore, these behaviors are often clubbed together as box, tussle by Nielsen et al., 2004 in their Markov chain analysis as well as a more detailed recent study of male aggression (Simon & Heberlein, 2020). Therefore, authors can either reconsider the description of behavior as 'box, tussle' or consider providing a video representation/computational classifier to distinguish between box and tussle behaviors.

We will textually address this issue.

(4) Simon & Heberlein, 2020 showed that increased boxing & tussling precede the formation of a dominance hierarchy in males, and lunges are used subsequently to maintain this dominant status. This study should be cited and discussed appropriately while introducing the paradigm.

We will cite this paper and discuss on this issue.

(5) It would be helpful to provide more methodological details about the assay, for instance, a video can be helpful showing how the males are introduced in the assay chamber, are they simply dropped to the floor when the film is removed after 30 minutes (Figures 1-2)?

We will provide more methodological details.

(6) The strain of Canton-S (CS) flies used should be mentioned as different strains of CS can have varying levels of aggression, for instance, CS from Martin Heisenberg lab shows very high levels of aggressive lunges. Are the CS lines used in this study isogenized? Are various genetic lines outcrossed into this CS background? In the methods, it is not clear how the white gene levels were controlled for various aggression experiments as it is known to affect aggression (Hoyer et al. 2008).

We will textually address this issue.

(7) How important it is to use a fixed female for the assay to induce tussling? Do these females remain active throughout the assay period of 2.5 hours? Is it possible to use decapitated virgin females for the assay? How will that affect male behaviors?

We will textually address this issue and provide additional videos.

(8) Raster plots in Figure 2 suggest a complete lack of tussling in SH males in the first 60 minutes of the encounter, which is surprising given the longer duration of the assay as compared to earlier studies (Nielsen et al. 2004, Simon & Heberlein, 2020 and others), which are able to pick up tussling in a shorter duration of recording time. Also, the duration for tussling is much longer in this study as compared to shorter tussles shown by earlier studies. Is this due to differences in the paradigm used, strain of flies, or some other factor? While the bar plots in Figure 2D show some tussling in SH males, maybe an analysis of raster plots of various videos can be provided in the main text and included as a supplementary figure to address this.

We will textually address the first question and provide more detailed analysis for the second question.

(9) Neuronal activation experiments suggesting the involvement of pC1SS2 neurons are quite interesting. Further, the role of P1a neurons was demonstrated to be involved in increasing tussling in thermogenetic activation in the presence of light (Figure 4, Supplement 1), which is quite important as the role of vision in optogenetic activation experiments, which required to be carried out in dark, is often not mentioned. However, in the discussion (lines 309-310) it is mentioned that PC1SS2 neurons are 'necessary and sufficient' for inducing tussling. Given that P1a neurons were shown to be involved in promoting tussling, this statement should be toned down.

We will tone down this statement.

(10) Are Or47b neurons connected to pC1SS2 or P1a neurons?

We conducted pathway analysis in the FlyWire electron microscopy database to investigate the connection between Or47b neurons and pC1 neurons. The results indicate that at least three intermediate neurons are required to establish a connection from Or47b neurons to pC1 neurons. Although the FlyWire database currently only contains neuronal data from female brains, they provide a reference for circuit connect in males. Using the currently available upstream and downstream tracing tools (e.g., retro-/trans-Tango), it is not possible to establish a direct connection between the two. Identifying the intermediate neurons involved in this connection is beyond this study. We will discuss on this concern in our revised manuscript.

(11) The paradigm for territory control is quite interesting and subsequent mating advantage experiments are an important addition to the eventual outcome of the aggressive strategy deployed by the males as per their prior housing conditions. It would be important to comment on the 'fitness outcome' of these encounters. For instance, is there any fitness advantage of using tussling by GH males as compared to lunging by SH males? The authors may consider analyzing the number of eggs laid and eclosed progenies from these encounters to address this.

We will discuss on this concern.

Reviewer #2 (Public review):

Summary:

Gao et al. investigated the change of aggression strategies by the social experience and its biological significance by using Drosophila. Two modes of inter-male aggression in Drosophila are known: lunging, high-frequency but weak mode, and tussling, low-frequency but more vigorous mode. Previous studies have mainly focused on the lunging. In this paper, the authors developed a new behavioral experiment system for observing tussling behavior and found that tussling is enhanced by group rearing while lunging is suppressed. They then searched for neurons involved in the generation of tussling. Although olfactory receptors named Or67d and Or65a have previously been reported to function in the control of lunging, the authors found that these neurons do not function in the execution of tussling, and another olfactory receptor, Or47b, is required for tussling, as shown by the inhibition of neuronal activity and the gene knockdown experiments. Further optogenetic experiments identified a small number of central neurons pC1[SS2] that induce the tussling specifically. In order to further explore the ecological significance of the aggression mode change in group rearing, a new behavioral experiment was performed to examine territorial control and mating competition. Finally, the authors found that differences in the social experience (group vs. solitary rearing) are important in these biologically significant competitions. These results add a new perspective to the study of aggressive behavior in Drosophila. Furthermore, this study proposes an interesting general model in which the social experience-modified behavioral changes play a role in reproductive success.

Strengths:

A behavioral experiment system that allows stable observation of tussling, which could not be easily analyzed due to its low frequency, would be very useful. The experimental setup itself is relatively simple, just the addition of a female to the platform, so it should be applicable to future research. The finding about the relationship between the social experience and the aggression mode change is quite novel. Although the intensity of aggression changes with the social experience was already reported in several papers (Liu et al., 2011, etc.), the fact that the behavioral mode itself changes significantly has rarely been addressed and is extremely interesting. The identification of sensory and central neurons required for the tussling makes appropriate use of the genetic tools and the results are clear. A major strength of the neurobiology in this study is the finding that another group of neurons (Or47b-expressing olfactory neurons and pC1[SS2] neurons), distinct from the group of neurons previously thought to be involved in low-intensity aggression (i.e. lunging), function in the tussling behavior. Further investigation of the detailed circuit analysis is expected to elucidate the neural substrate of the conflict between the two aggression modes.

Thank you for the acknowledgment of the novelty and significance of the study, and your suggestions for improving the manuscript.

Weaknesses:

The experimental systems examining the territory control and the reproductive competition in Figure 5 are novel and have advantages in exploring their biological significance. However, at this stage, the authors' claim is weak since they only show the effects of age and social experience on territorial and mating behaviors, but do not experimentally demonstrate the influence of aggression mode change itself. In the Abstract, the authors state that these findings reveal how social experience shapes fighting strategies to optimize reproductive success. This is the most important perspective of the present study, and it would be necessary to show directly that the change of aggression mode by social experience contributes to reproductive success.

We will either tone down this statement or provide additional analysis.

In addition, a detailed description of the tussling is lacking. For example, the authors state that the tussling is less frequent but more vigorous than lunging, but while experimental data are presented on the frequency, the intensity seems to be subjective. The intensity is certainly clear from the supplementary video, but it would be necessary to evaluate the intensity itself using some index. Another problem is that there is no clear explanation of how to determine the tussling. A detailed method is required for the reproducibility of the experiment.

We will provide more detailed methods and data analysis regarding tussling behavior.

Reviewer #3 (Public review):

In this manuscript, Gao et al. presented a series of intriguing data that collectively suggest that tussling, a form of high-intensity fighting among male fruit flies (Drosophila melanogaster) has a unique function and is controlled by a dedicated neural circuit. Based on the results of behavioral assays, they argue that increased tussling among socially experienced males promotes access to resources. They also concluded that tussling is controlled by a class of olfactory sensory neurons and sexually dimorphic central neurons that are distinct from pathways known to control lunges, a common male-type attack behavior.

A major strength of this work is that it is the first attempt to characterize the behavioral function and neural circuit associated with Drosophila tussling. Many animal species use both low-intensity and high-intensity tactics to resolve conflicts. High-intensity tactics are mostly reserved for escalated fights, which are relatively rare. Because of this, tussling in the flies, like high-intensity fights in other animal species, has not been systematically investigated. Previous studies on fly aggressive behavior have often used socially isolated, relatively young flies within a short observation duration. Their discovery that 1) older (14-days-old) flies tend to tussle more often than younger (2-days-old) flies, 2) group-reared flies tend to tussle more often than socially isolated flies, and 3) flies tend to tussle at a later stage (mostly ~15 minutes after the onset of fighting), are the result of their creativity to look outside of conventional experimental settings. These new findings are key for quantitatively characterizing this interesting yet under-studied behavior.

Precisely because their initial approach was creative, it is regrettable that the authors missed the opportunity to effectively integrate preceding studies in their rationale or conclusions, which sometimes led to premature claims. Also, while each experiment contains an intriguing finding, these are poorly related to each other. This obscures the central conclusion of this work. The perceived weaknesses are discussed in detail below.

Thank you for the precise summary of the key findings and novelty of the study, and your insightful suggestions.

Most importantly, the authors' definition of "tussling" is unclear because they did not explain how they quantified lunges and tussling, even though the central focus of the manuscript is behavior. Supplemental movies S1 and S2 appear to include "tussling" bouts in which 2 flies lunge at each other in rapid succession, and supplemental movie S3 appears to include bouts of "holding", in which one fly holds the opponent's wings and shakes vigorously. These cases raise a concern that their behavior classification is arbitrary. Specifically, lunges and tussling should be objectively distinguished because one of their conclusions is that these two actions are controlled by separate neural circuits. It is impossible to evaluate the credibility of their behavioral data without clearly describing a criterion of each behavior.

We will add more details in methods.

It is also confusing that the authors completely skipped the characterization of the tussling-controlling neurons they claimed to have identified. These neurons (a subset of so-called pC1 neurons labeled by previously described split-GAL4 line pC1SS2) are central to this manuscript, but the only information the authors have provided is its gross morphology in a low-resolution image (Figure 4D, E) and a statement that "only 3 pairs of pC1SS2 neurons whose function is both necessary and sufficient for inducing tussling in males" (lines 310-311). The evidence that supports this claim isn't provided. The expression pattern of pC1SS2 neurons in males has been only briefly described in reference 46. It is possible that these neurons overlap with previously characterized dsx+ and/or fru+ neurons that are important for male aggressions (measured by lunges), such as in Koganezawa et al., Curr. Biol. 2016 and Chiu et al., Cell 2020. This adds to the concern that lunge and tussling are not as clearly separated as the authors claim.

Reply: we will perform additional morphological and functional experiments on pC1^SS2 neurons, e.g., whether they are fru or dsx positive and comparing them with P1a neurons.

While their characterizations of tussling behaviors in wild-type males (Figures 1 and 2) are intriguing, the remaining data have little link with each other, making it difficult to understand what their main conclusion is. Figure 3 suggests that one class of olfactory sensory neurons (OSN) that express Or47b is necessary for tussling behavior. While the authors acknowledged that Or47b-expressing OSNs promote male courtship toward females presumably by detecting cuticular compounds, they provided little discussion on how a class of OSN can promote two different types of innate behavior. No evidence of a functional or circuitry relationship between the Or47b pathway and the pC1SS2 neurons was provided. It is unclear how these two components are relevant to each other. Lastly, the rationale of the experiment in Figure 5 and the interpretation of the results is confusing. The authors attributed a higher mating success rate of older, socially experienced males over younger, socially isolated males to their tendency to tussle, but tussling cannot happen when one of the two flies is not engaged. If, for instance, a socially isolated 14-day-old male does not engage in tussling as indicated in Figure 2, how can they tussle with a group-housed 14-day-old male? Because aggressive interactions in Figure 5 were not quantified, it is impossible to conclude that tussling plays a role in copulation advantage among pairs as authors argue (lines 282-288).

Regarding why Or47b-expressing OSNs regulate two types of innate behaviors, we will add a discussion in the revised manuscript to explore the possible mechanisms underlying this phenomenon.

Regarding the relationship between Or47b-expressing OSNs and pC1^SS2 neurons, we conducted pathway connection analyses using the FlyWire database. Although the FlyWire database currently only contains neuronal data from female brains, these findings provide a certain degree of reference. The results indicate that at least three intermediate neurons are required to establish the connection between these two neuronal types. We hope the editor and reviewers would agree with us that identifying these intermediate neurons involved in this connection is beyond this study.

Regarding the rationale and conclusions from the experiments in Figure 5, we acknowledge the difficulty in quantifying tussling and lunging behaviors in these experiments. In the revised manuscript, we will tone down the statements about the relationship between fighting strategies and reproductive success. Additionally, we will provide further behavioral experiments to support the association between these two factors.

Despite these weaknesses, it is important to acknowledge the authors' courage to initiate an investigation into a less characterized, high-intensity fighting behavior. Tussling requires the simultaneous engagement of two flies. Even if there is confusion over the distinction between lunges and tussling, the authors' conclusion that socially experienced flies and socially isolated flies employ distinct fighting strategies is convincing. Questions that require more rigorous studies are 1) whether such differences are encoded by separate circuits, and 2) whether the different fighting strategies are causally responsible for gaining ethologically relevant resources among socially experienced flies. Enhanced transparency of behavioral data will help readers understand the impact of this study. Lastly, the manuscript often mentions previous works and results without citing relevant references. For readers to grasp the context of this work, it is important to provide information about methods, reagents, and other key resources.

We will add more details in methods and cite additional references, we will also perform additional experiment on pC1^SS2 function.

Author response:

The authors plan to respond in full in due course.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study investigates the role of macrophage lipid metabolism in the intracellular growth of Mycobacterium tuberculosis. By using a CRISPR-Cas9 gene-editing approach, the authors knocked out key genes involved in fatty acid import, lipid droplet formation, and fatty acid oxidation in macrophages. Their results show that disrupting various stages of fatty acid metabolism significantly impairs the ability of Mtb to replicate inside macrophages. The mechanisms of growth restriction included increased glycolysis, oxidative stress, pro-inflammatory cytokine production, enhanced autophagy, and nutrient limitation. The study demonstrates that targeting fatty acid homeostasis at different stages of the lipid metabolic process could offer new strategies for host-directed therapies against tuberculosis.

The work is convincing and methodologically strong, combining genetic, metabolic, and transcriptomic analyses to provide deep insights into how host lipid metabolism affects bacterial survival.

Strengths:

The study uses a multifaceted approach, including CRISPR-Cas9 gene knockouts, metabolic assays, and dual RNA sequencing, to assess how various stages of macrophage lipid metabolism affect Mtb growth. The use of CRISPR-Cas9 to selectively knock out key genes involved in fatty acid metabolism enables precise investigation of how each step-lipid import, lipid droplet formation, and fatty acid oxidation affect Mtb survival. The study offers mechanistic insights into how different impairments in lipid metabolism lead to diverse antimicrobial responses, including glycolysis, oxidative stress, and autophagy. This deepens the understanding of macrophage function in immune defense.

The use of functional assays to validate findings (e.g., metabolic flux analyses, lipid droplet formation assays, and rescue experiments with fatty acid supplementation) strengthens the reliability and applicability of the results.

By highlighting potential targets for HDT that exploit macrophage lipid metabolism to restrict Mtb growth, the work has significant implications for developing new tuberculosis treatments.

Weaknesses:

The experiments were primarily conducted in vitro using CRISPR-modified macrophages. While these provide valuable insights, they may not fully replicate the complexity of the in vivo environment where multiple cell types and factors influence Mtb infection and immune responses.

We thank the reviewer for pointing this out. We acknowledge that our in vitro system may indeed not fully replicate the complex in vivo environment in light of the heterogenous responses of macrophages to Mtb infection in whole animal models. We do believe, however, that the Hoxb8 in vitro model provides a powerful genetic tool to interrogate host-Mtb interactions using primary macrophages that represent the bone marrow-derived macrophage lineage. Reviewer #1 also made several helpful suggestions in their recommendations to authors relating to the reorganization of the data in our Figures in both the manuscript and the supplemental data.  We will incorporate these suggestions into the revised version of the manuscript upon resubmission.

Reviewer #2 (Public review):

Summary:

Host-derived lipids are an important factor during Mtb infection. In this study, using CRISPR knockouts of genes involved in fatty acid uptake and metabolism, the authors claim that a compromised uptake, storage, or metabolism of fatty acid restricts Mtb growth upon infection. Further, the authors claim that the mechanism involves increased glycolysis, autophagy, oxidative stress, pro-inflammatory cytokines, and nutrient limitation. The authors also claim that impaired lipid droplet formation restricts Mtb growth. However, promoting lipid droplet biogenesis does not reverse/promote Mtb growth.

Strengths:

The strength of the study is the use of clean HOXB8-derived primary mouse macrophage lines for generating CRISPR knockouts.

Weaknesses:

There are many weaknesses of this study, they are clubbed into four categories below

(1) Evidence and interpretations: The results shown in this study at several places do not support the interpretations made or are internally contradictory or inconsistent. There are several important observations, but none were taken forward for in-depth analysis. A

a) The phenotypes of PLIN2-/-, FATP1-/-, and CPT-/- are comparable in terms of bacterial growth restriction; however, their phenotype in terms of lipid body formation, IL1B expression, etc., are not consistent. These are interesting observations and suggest additional mechanisms specific to specific target genes; however, clubbing them all as altered fatty acid uptake or catabolism-dependent phenotypes takes away this important point.

We thank the reviewer for highlighting this. Our main focus was on assessing the impact of manipulating lipid homeostasis in macrophages and the consequences this has on the intracellular growth of Mtb.  It was never our intention to imply these mutants generated equivalent phenotypes, and we will modify the revised manuscript to reflect this point.  We will stress that interfering with lipid processing at different stages in macrophages results in both shared and divergent anti-microbial conditions against Mtb.

b) Finding the FATP1 transcript in the HOXB8-derived FATP1-/- CRISPR KO line is a bit confusing. There is less than a two-fold decrease in relative transcript abundance in the KO line compared to the WT line, leaving concerns regarding the robustness of other experiments as well using FATP1^-/- cells.

CRISPR-Cas9 targeting of genes with single sgRNAs as is the case with our mutants generates insertions and deletions (INDELs) at the CRISPR cut site. These INDELs do not block mRNA transcription totally, and this is widely reported and accepted in the field.  In these cases, RT-PCR or RNA-seq methods are not used to verify CRISPR knockouts as they are not sensitive enough to identify INDELs. We provide knockout efficiencies by ICE analysis in supplemental information file 1 for all the mutants used in the study. We also demonstrate protein depletion by western blot and flow cytometry for all the mutants (Figure 1 - figure supplement 1). Only mutants with greater than >90% protein depletion were used for subsequent characterization.

c) No gene showing differential regulation in FATP1^-/- macrophages, which is very surprising.

We assume the reviewer is referring to the Mtb transcriptome response in FATP1^-/- macrophages, which we agree was unexpected.  However, we saw a significant compensatory response in the host cell (at transcriptional level) in FATP1-/- macrophages as evidenced by an upregulation of other fatty acid transporters (Figure 5 - figure supplement 1). We postulate that these compensatory responses could, in part, alleviate the stresses the bacteria experience within the cell, and these were discussed in the manuscript.

d) ROS measurements should be done using flow cytometry and not by microscopy to nail the actual pattern.

We thank the reviewer for the suggestion. However, confocal imaging is also widely used to measure ROS with similar quantitative power and individual cell resolution (PMID: 32636249, 35737799).

(2) Experimental design: For a few assays, the experimental design is inappropriate

a) For autophagy flux assay, immunoblot of LC3II alone is not sufficient to make any interpretation regarding the state of autophagy. This assay must be done with BafA1 or CQ controls to assess the true state of autophagy.

We would like to point out that monitoring LC3I to LC3II conversion by western blot, confocal imaging of LC3 puncta and qPCR analysis of autophagy related genes are all validated assays for monitoring autophagic flux in a wide variety of cells. We refer the reviewer to the latest extensive guidelines on the subject (PMID: 33634751). Furthermore, Bafilomycin A and chloroquine are not specific inhibitors of autophagy and therefore are of limited value as controls. BafA is an inhibitor of the proton-ATPase apparatus as well impacting autophagy through activity on the Ca-P60A/SERCA pathway. Chloroquine impacts vacuole acidification, autophagosome/lysosome fusion and slows phagosome maturation. So, while BafA and chloroquine will reduce autophagy their effects are pleotropic and their impact on Mtb is unknown.

b) Similarly, qPCR analyses of autophagy-related gene expression do not reflect anything on the state of autophagy flux.

See our response above.

(3) Using correlative observations as evidence:

a) Observations based on RNAseq analyses are presented as functional readouts, which is incorrect.

We are not entirely sure where we used our RNA-seq data sets as functional readouts. We used our transcriptome data to provide a preliminary identification of anti-microbial responses in the mutant macrophages infected with Mtb. Where applicable, we followed up and confirmed the more compelling RNA-seq data either by metabolic flux analyzes, qPCR, ROS measurements, and quantitative imaging.

b) Claiming that the inability to generate lipid droplets in PLIN2-/- cells led to the upregulation of several pathways in the cells is purely correlative, and the causal relationship does not exist in the data presented.

Again, it was not our intention to infer causality. Throughout the manuscript, we endeavor to present our data with a specific focus on describing the consequences of interfering with either fatty acid import, lipid droplet biogenesis and fatty acid oxidation on macrophage responses to Mtb.  We will revisit the revised manuscript to remove any sections that imply causality.

(4) Novelty: A few main observations described in this study were previously reported. That includes Mtb growth restriction in PLIN2 and FATP1 deficient cells. Similarly, the impact of Metformin and TMZ on intracellular Mtb growth is well-reported. While that validates these observations in this study, it takes away any novelty from the study.

To the best of our knowledge, Mtb growth restrictions in PLIN2 and FATP1 deficient macrophages have not been reported elsewhere. To the contrary, PLIN2 knockout macrophages obtained from PLIN2 deficient mice have been reported to robustly support Mtb replication (PMID: 29370315), quite the opposite to our data. We extensively discuss these discrepancies in the manuscript. We also discuss and cite appropriate references where Mtb growth restriction for similar macrophage mutants have been reported (CD36^-/- and CPT2^-/-). Our aim was to carry out a systematic myeloid specific genetic interference of fatty acid import, storage and catabolism to assess the effect on Mtb growth at all stages of lipid handling instead of focusing on one target. In the chemical approach, we used TMZ and Metformin deliberately because they had already been reported as being active against intracellular Mtb and we wished to place our data in the context of existing literature.  These studies were referenced extensively in the text.

(5) Manuscript organisation: It will be very helpful to rearrange figures and supplementary figures.

We will re-organize the figures in the manuscript revision as per the reviewer’s recommendation, and the recommendations of reviewer #1.

We will address the other concerns raised by reviewer #2 in the recommendations to authors during revision of the manuscript. 

Reviewer #3 (Public review):

Summary:

This study provides significant insights into how host metabolism, specifically lipids, influences the pathogenesis of Mycobacterium tuberculosis (Mtb). It builds on existing knowledge about Mtb's reliance on host lipids and emphasizes the potential of targeting fatty acid metabolism for therapeutic intervention.

Strengths:

To generate the data, the authors use CRISPR technology to precisely disrupt the genes involved in lipid import (CD36, FATP1), lipid droplet formation (PLIN2), and fatty acid oxidation (CPT1A, CPT2) in mouse primary macrophages. The Mtb Erdman strain is used to infect the macrophage mutants. The study, reveals specific roles of different lipid-related genes. Importantly, results challenge previous assumptions about lipid droplet formation and show that macrophage responses to lipid metabolism impairments are complex and multifaceted. The experiments are well-controlled and the data is convincing.

Overall, this well-written paper makes a meaningful contribution to the field of tuberculosis research, particularly in the context of host-directed therapies (HDTs). It suggests that manipulating macrophage metabolism could be an effective strategy to limit Mtb growth.

Weaknesses:

None noted. The manuscript provides important new knowledge that will lead mpvel to host-directed therapies to control Mtb infections.

Author response:

Reviewer #1 (Public review):

Summary:

This study investigates what happens to the stimulus-driven responses of V4 neurons when an item is held in working memory. Monkeys are trained to perform memory-guided saccades: they must remember the location of a visual cue and then, after a delay, make an eye movement to the remembered location. In addition, a background stimulus (a grating) is presented that varies in contrast and orientation across trials. This stimulus serves to probe the V4 responses, is present throughout the trial, and is task-irrelevant. Using this design, the authors report memory-driven changes in the LFP power spectrum, changes in synchronization between the V4 spikes and the ongoing LFP, and no significant changes in firing rate.

Strengths:

(1) The logic of the experiment is nicely laid out.

(2) The presentation is clear and concise.

(3) The analyses are thorough, careful, and yield unambiguous results.

(4) Together, the recording and inactivation data demonstrate quite convincingly that the signal stored in FEF is communicated to V4 and that, under the current experimental conditions, the impact from FEF manifests as variations in the timing of the stimulus-evoked V4 spikes and not in the intensity of the evoked activity (i.e., firing rate).

Weaknesses:

I think there are two limitations of the study that are important for evaluating the potential functional implications of the data. If these were acknowledged and discussed, it would be easier to situate these results in the broader context of the topic, and their importance would be conveyed more fairly and transparently.

(1) While it may be true that no firing rate modulations were observed in this case, this may have been because the probe stimuli in the task were behaviorally irrelevant; if anything, they might have served as distracters to the monkey's actual task (the MGS). From this perspective, the lack of rate modulation could simply mean that the monkeys were successful in attending the relevant cue and shielding their performance from the potentially distracting effect of the background gratings. Had the visual probes been in some way behaviorally relevant and/or spatially localized (instead of full field), the data might have looked very different.

Any task design involves tradeoffs; if the visual stimulus was behaviorally relevant, then any observed neurophysiological changes would be more confounded by possible attentional effects. We cannot exclude the possibility that a different task or different stimuli would produce different results; we ourselves have reported firing rate enhancements for other types of visual probes during an MGS task (Merrikhi et al. 2017). We have added an acknowledgement of these limitations in the discussion section (lines 311-319). At minimum, our results show a dissociation between the top-down modulation of phase coding, which is enhanced during WM even for these task-irrelevant stimuli, and rate coding. Establishing whether and how this phase coding is related to perception and behavior will be an important direction for future work.

With this in mind, it would be prudent to dial down the tone of the conclusions, which stretch well beyond the current experimental conditions (see recommendations).

We have edited the title (removing the word ‘primarily’) and key sentences throughout to tone down the conclusions, generally to state that the importance of a phase code in WM modulations is *possible* given the observed results, rather than certain (see abstract line 27, introduction lines 58-60, results line 215, conclusion lines 294-295).

(2) Another point worth discussing is that although the FEF delay-period activity corresponds to a remembered location, it can also be interpreted as an attended location, or as a motor plan for the upcoming eye movement. These are overlapping constructs that are difficult to disentangle, but it would be important to mention them given prior studies of attentional or saccade-related modulation in V4. The firing rate modulations reported in some of those cases provide a stark contrast with the findings here, and I again suspect that the differences may be due at least in part to the differing experimental conditions, rather than a drastically different encoding mode or functional linkage between FEF and V4.

We have added a paragraph to the discussion section addressing links to attention and motor planning (lines 301-322), and specifically acknowledging the inherent difficulties of fully dissociating these effects when interpreting our results (lines 311-319).

Reviewer #2 (Public review):

Summary:

It is generally believed that higher-order areas in the prefrontal cortex guide selection during working memory and attention through signals that selectively recruit neuronal populations in sensory areas that encode the relevant feature. In this work, Parto-Dezfouli and colleagues tested how these prefrontal signals influence activity in visual area V4 using a spatial working memory task. They recorded neuronal activity from visual area V4 and found that information about visual features at the behaviorally relevant part of space during the memory period is carried in a spatially selective manner in the timing of spikes relative to a beta oscillation (phase coding) rather than in the average firing rate (rate code). The authors further tested whether there is a causal link between prefrontal input and the phase encoding of visual information during the memory period. They found that indeed inactivation of the frontal eye fields, a prefrontal area known to send spatial signals to V4, decreased beta oscillatory activity in V4 and information about the visual features. The authors went one step further to develop a neural model that replicated the experimental findings and suggested that changes in the average firing rate of individual neurons might be a result of small changes in the exact beta oscillation frequency within V4. These data provide important new insights into the possible mechanisms through which top-down signals can influence activity in hierarchically lower sensory areas and can therefore have a significant impact on the Systems, Cognitive, and Computational Neuroscience fields.

Strengths:

This is a well-written paper with a well-thought-out experimental design. The authors used a smart variation of the memory-guided saccade task to assess how information about the visual features of stimuli is encoded during the memory period. By using a grating of various contrasts and orientations as the background the authors ensured that bottom-up visual input would drive responses in visual area V4 in the delay period, something that is not commonly done in experimental settings in the same task. Moreover, one of the major strengths of the study is the use of different approaches including analysis of electrophysiological data using advanced computational methods of analysis, manipulation of activity through inactivation of the prefrontal cortex to establish causality of top-down signals on local activity signatures (beta oscillations, spike locking and information carried) as well as computational neuronal modeling. This has helped extend an observation into a possible mechanism well supported by the results.

Weaknesses:

Although the authors provide support for their conclusions from different approaches, I found that the selection of some of the analyses and statistical assessments made it harder for the reader to follow the comparison between a rate code and a phase code. Specifically, the authors wish to assess whether stimulus information is carried selectively for the relevant position through a firing rate or a phase code. Results for the rate code are shown in Figures 1B-G and for the phase code are shown in Figure 2. Whereas an F-statistic is shown over time in Figure 1F (and Figure S1) no such analysis is shown for LFP power. Similarly, following FEF inactivation there is no data on how that influences V4 firing rates and information carried by firing rates in the two conditions (for positions inside and outside the V4 RF). In the same vein, no data are shown on how the inactivation affects beta phase coding in the OUT condition.

We plan to incorporate statistical analysis of this point in the revised version.

Moreover, some of the statistical assessments could be carried out differently including all conditions to provide more insight into mechanisms. For example, a two-way ANOVA followed by post hoc tests could be employed to include comparisons across both spatial (IN, OUT) and visual feature conditions (see results in Figures 2D, S4, etc.). Figure 2D suggests that the absence of selectivity in the OUT condition (no significant difference between high and low contrast stimuli) is mainly due to an increase in slope in the OUT condition for the low contrast stimulus compared to that for the same stimulus in the IN condition. If this turns out to be true it would provide important information that the authors should address.

We plan to incorporate statistical analysis of this point in the revised version.

There are also a few conceptual gaps that leave the reader wondering whether the results and conclusion are general enough. Specifically,

(1) the authors used microstimulation in the FEF to determine RFs. It is thus possible that the FEF sites that were inactivated were largely more motor-related. Given that beta oscillations and motor preparatory activity have been found to be correlated and motor sites show increased beta oscillatory activity in the delay period, it is possible that the effect of FEF inactivation on V4 beta oscillations is due to inactivation of the main source of beta activity. Had the authors inactivated sites with a preponderance of visual neurons in the FEF would the results be different?

We do not believe this to be likely based on what is known anatomically and functionally about this circuitry. Anatomically, the projections from FEF to V4 arise primarily from the supragranular layers, not layers which contain the highest proportion of motor activity (Barone et al. 2000, Pouget et al. 2009, Markov et al. 2013). Functionally, based on electrical identification of V4-projecting FEF neurons, we know that FEF to V4 projections are predominantly characterized by delay rather than motor activity (Merrikhi et al. 2017). We have now tried to emphasize these points when we introduce the inactivation experiments (lines 180-182).

Experimentally, the spread of the pharmacological effect with our infusion system is quite large relative to any clustering of visual vs. motor neurons within the FEF, with behavioral consequences of inactivation spreading to cover a substantial portion of the visual hemifield (e.g., Noudoost et al. 2014, Clark et al. 2014), and so our manipulation lacks the spatial resolution to selectively target motor vs. other FEF neurons.

(2) Somewhat related to this point and given the prominence of low-frequency activity in deeper layers of the visual cortex according to some previous studies, it is not clear where the authors' V4 recordings were located. The authors report that they do have data from linear arrays, so it should be possible to address this.

Unfortunately our chamber placement for V4 has produced linear array penetration angles which do not reliably allow identification of cortical layers. We are aware of previous results showing layer-specific effects of attention in V4 (e.g., Pettine et al. 2019, Buffalo et al. 2011), and it would indeed be interesting to determine whether our observed WM-driven changes follow similar patterns. We may be able to analyze a subset of the data with current source density analysis to look for layer-specific effects in the future, but are not able to provide any information at this time.

(3) The authors suggest that a change in the exact frequency of oscillation underlies the increase in firing rate for different stimulus features. However, the shift in frequency is prominent for contrast but not for orientation, something that raises questions about the general applicability of this observation for different visual features.

We plan to incorporate statistical analysis of this point in the revised version.

(4) One of the major points of the study is the primacy of the phase code over the rate code during the delay period. Specifically, here it is shown that information about the visual features of a stimulus carried by the rate code is similar for relevant and irrelevant locations during the delay period. This contrasts with what several studies have shown for attention in which case information carried in firing rates about stimuli in the attended location is enhanced relative to that for stimuli in the unattended location. If we are to understand how top-down signals work in cognitive functions it is inevitable to compare working memory with attention. The possible source of this difference is not clear and is not discussed. The reader is left wondering whether perhaps a different measure or analysis (e.g. a percent explained variance analysis) might reveal differences during the delay period for different visual features across the two spatial conditions.

We have added discussion regarding the relationship of these results to previous findings during attention in the discussion section (lines 301-322).

The use of the memory-guided saccade task has certain disadvantages in the context of this study. Although delay activity is interpreted as memory activity by the authors, it is in principle possible that it reflects preparation for the upcoming saccade, spatial attention (particularly since there is a stimulus in the RF), etc. This could potentially change the conclusion and perspective.

We have added a new discussion paragraph addressing the relationship to attention and motor planning (lines 301-322). We have also moderated the language used to describe our conclusions throughout the manuscript in light of this ambiguity.

For the position outside the V4 RF, there is a decrease in both beta oscillations and the clustering of spikes at a specific phase. It is therefore possible that the decrease in information about the stimuli features is a byproduct of the decrease in beta power and phase locking. Decreased oscillatory activity and phase locking can result in less reliable estimates of phase, which could decrease the mutual information estimates.

We plan to incorporate statistical analysis of this point in the revised version.

The authors propose that coherent oscillations could be the mechanism through which the prefrontal cortex influences beta activity in V4. I assume they mean coherent oscillations between the prefrontal cortex and V4. Given that they do have simultaneous recordings from the two areas they could test this hypothesis on their own data, however, they do not provide any results on that.

This paper only includes inactivation data. We are working on analyzing the simultaneous recording data for a future publication.

The authors make a strong point about the relevance of changes in the oscillation frequency and how this may result in an increase in firing rate although it could also be the reverse - an increase in firing rate leading to an increase in the frequency peak. It is not clear at all how these changes in frequency could come about. A more nuanced discussion based on both experimental and modeling data is necessary to appreciate the source and role (if any) of this observation.

As the reviewer notes, it is difficult to determine whether the frequency changes drive the rate changes, vice versa, or whether both are generated in parallel by a common source. We have adjusted our language to reflect this (lines 277-278). Future modeling work may be able to shed more light on the causal relationships between various neural signatures.

Reviewer #3 (Public review):

Summary:

In this report, the authors test the necessity of prefrontal cortex (specifically, FEF) activity in driving changes in oscillatory power, spike rate, and spike timing of extrastriate visual cortex neurons during a visual-spatial working memory (WM) task. The authors recorded LFP and spikes in V4 while macaques remembered a single spatial location over a delay period during which task-irrelevant background gratings were displayed on the screen with varying orientation and contrast. V4 oscillations (in the beta range) scaled with WM maintenance, and the information encoded by spike timing relative to beta band LFP about the task-irrelevant background orientation depended on remembered location. They also compared recorded signals in V4 with and without muscimol inactivation of FEF, demonstrating the importance of FEF input for WM-induced changes in oscillatory amplitude, phase coding, and information encoded about background orientations. Finally, they built a network model that can account for some of these results. Together, these results show that FEF provides meaningful input to the visual cortex that is used to alter neural activity and that these signals can impact information coding of task-irrelevant information during a WM delay.

Strengths:

(1) Elegant and robust experiment that allows for clear tests for the necessity of FEF activity in WM-induced changes in V4 activity.

(2) Comprehensive and broad analyses of interactions between LFP and spike timing provide compelling evidence for FEF-modulated phase coding of task-irrelevant stimuli at remembered location.

(3) Convincing modeling efforts.

Weaknesses:

(1) 0% contrast background data (standard memory-guided saccade task) are not reported in the manuscript. While these data cannot be used to consider information content of spike rate/time about task-irrelevant background stimuli, this condition is still informative as a 'baseline' (and a more typical example of a WM task).

We plan to incorporate statistical analysis of this point in the revised version.

(2) Throughout the manuscript, the primary measurements of neural coding pertain to task-irrelevant stimuli (the orientation/contrast of the background, which is unrelated to the animal's task to remember a spatial location). The remembered location impacts the coding of these stimulus variables, but it's unclear how this relates to WM representations themselves.

Indeed, here we have focused on how maintaining spatial WM impacts visual processing of incoming sensory information, rather than on how the spatial WM signal itself is represented and maintained. Behaviorally, this impact on visual signals could be related to the effects of the content of WM on perception and reaction times (e.g., Soto et al. 2008, Awh et al. 1998, Teng et al. 2019), but no such link to behavior is shown in our data.

Author response:

The following is the authors’ response to the original reviews.

Public reviews: 

Reviewer #1 (Public Review): 

Summary: 

In this study, Masroor Ahmad Paddar and his/her colleagues explore the noncanonical roles of ATG5 and membrane atg8ylation in regulating retromer assembly and function. They begin by examining the interactomes of ATG5 and expand the scope of these effects to include homeostatic responses to membrane stress and damage. 

Strengths: 

This study provides novel insights into the noncanonical function of ATG8ylation in endosomal cargo sorting process. 

Weaknesses: 

The direct mechanism by which ATG8ylation regulates the retromer remains unsolved. 

We agree with the reviewer.  We do however show how at least one aspect of atg8ylation contributes to the proper retromer function, which occurs via lysosomal membrane maintenance and repair. Understanding the more direct effects on retromer will require a separate study. We now emphasize this in the revised manuscript (p. 18) and point out the limitations of the present work (p. 18): “One of the limitations of our study is that beyond effects of membrane atg8ylation on quality of lysosomal membrane and its homeostasis there could be more direct effects of membrane modification with mATG8s that still need to be understood”.

Reviewer #2 (Public Review): 

Summary:

Padder et al. demonstrate that ATG5 mediates lysosomal repair via the recruitment of the retromer components during LLOMe-induced lysosomal damage and that mAtg8-ylation contributes to retromer-dependent cargo sorting of GLUT1. Although previous studies have suggested that during glucose withdrawal, classical autophagy contributes to retromer-dependent GLUT1 surface trafficking via interactions between LC3A and TBC1D5, the experiments here demonstrate that during basal conditions or lysosomal damage, ATGs that are not involved in mATG8ylation, such as FIP200, are not functionally required for retromer-dependent sorting of GLUT1. Overall, these studies suggest a unique role for ATG5 in the control of retromer function, and that conjugation of ATG8 to single membranes (CASM) is a partial contributor to these phenotypes. 

Strengths: 

(1) Overall, these studies suggest a unique non-autophagic role for ATG5 in the control of retromer function. They also demonstrate that conjugation of ATG8 to single membranes (CASM) is a partial contributor to these phenotypes. Overall, these data point to a new role for ATG5 and CASM-dependent mATG8ylation in lysosomal membrane repair and trafficking. 

(2) Although the studies are overall supportive of the proposed model that the retromer is controlled by CASM-dependent mATG8-ylaytion, it is noteworthy that previous studies of GLUT1 trafficking during glucose withdrawal (Roy et al. Mol Cell, PMID: 28602638) were predominantly conducted in cells lacking ATG5 or ATG7, which would not be able to discriminate between a CASM-dependent vs. canonical autophagy-dependent pathway in the control of GLUT1 sorting. Is the lack of GLUT1 mis-sorting to lysosomes observed in FIP200 and ATG13KO cells also observed during glucose withdrawal? Notably, deficiencies in glycolysis and glucose-dependent growth have been reported in FIP200 deficient fibroblasts (Wei et al. G&D, PMID: 21764854) so there may be differences in regulation dependent on the stress imposed on a cell. 

We thank the reviewer for the overall assessment of the strengths of the study.  We have discussed in the manuscript the elegant study by Roy et al., PMID 28602683. To accommodate reviewer’s comment, we have additionally emphasized in the text that our study is focused on basal conditions and conditions that perturb endolysosomal compartments. We agree with the reviewer that under metabolic stress conditions (such as glucose limitation) more complex pathways may be engaged and have acknowledged that in the discussion. We have now included this in the limitations of the study (p. 18): “Another limitation of our study is that we have focused on basal conditions or conditions causing lysosomal damage, whereas metabolic stress including glucose excess or limitation with its multitude of metabolic effects have not been addressed”.

Weaknesses: 

(1) Additional controls are needed to clarify the role of CASM in the control of retromer function. Because the manuscript proposes both CASM-dependent and independent pathways in the ATG5 mediated regulation of the retromer, it is important to provide robust evidence that CASM is required for retromer-dependent GLUT1 sorting to the plasma membrane vs. lysosome. The experiments with monensin in Fig. 7C-E are consistent with but not unequivocally corroborative of a role for CASM. 

We fully agree with the reviewer. In fact, our data with bafilomycin A1 treatment causing GLUT1 miss-sorting show that it is the perturbance of lysosomes  and not CASM per se that leads to mis-sorting of GLUT1 (Fig. 7D,E). Note that it has been shown (PMIDs: 28296541, 25484071 and 37796195) that although bafilomycin A1 deacidifies lysosomes it does not induce but instead inhibits CASM. This is because bafilomycin A1 causes dissociation of V1 and V0 sectors of V-ATPase, unlike other CASM-inducing agents which promote V1 V0 association. Complementing this, our data with ATG2AB DKO and ESCRT VPS37A KO (Fig. 8A-F) indicate that the repair of lysosomes is important to keep the retromer machinery functional (as illustrated in Fig. 8G). This may be one of the effector mechanisms downstream of membrane atg8ylation in general and hence also downstream of CASM. We have revised Fig. 7 title to read “Lysosomal perturbations cause GLUT1 mis-sorting” and have explained these relationships in the text (p. 12-13): “Since bafilomycin A1 does not induce CASM but disturbs luminal pH, we conclude that it is the less acidic luminal pH of the endolysosomal organelles, and not CASM, that is sufficient to interfere with the proper sorting of GLUT1.”

Based on the results shown with ATG16KO in Fig 4A-D, rescue experiments of these 16KO cells with WT vs. C-terminal WD40 mutant versions of ATG16 will specifically assess the requirement for CASM and potentially provide more rigorous support for the conclusions drawn. 

We have carried out complementation with ATG16L1 WT and its E230 mutant (devoid of WD40 repeats but still capable of canonical autophagy) and placed these data in Fig. 7 (panels I and J) as recommended by the reviewer. This is now described on p. 13 (To additionally test this notion, we compared ATG16L1 full length (ATG16L1FL) and ATG16L1E230 (Rai et al., PMID 30403914) for complementation of the GLUT1 sorting defect in ATG16L1 KO cells (Fig. 7I,J). ATG16L1E230 [Rai, 2019, 30403914] lacks the key domain to carry out CASM via binding to VATPase 29,30 31-33 but retains capacity to carry out atg8ylation.  Both ATG16L1FL and ATG16L1E230 complemented mis-sorting of GLUT1 (Fig. 7I,J). Collectively, these data indicate that it is not absence of CASM/VAIL but absence of membrane atg8ylation in general that promotes GLUT1 mis-sorting.).

(2) Also, the role of TBC1D5 should be further clarified. In Fig S7, are there any changes in the interactions between TBC1D5 and VPS35 in response to LLOMe or other agents utilized to induce CASM? 

We thank the reviewer for pointing this out. We do have data with VPS35 in co-IPs shown in Fig. S7.  There is no change in the amounts of VPS35 or TBC1D5 in GFP-LC3A co-IPs. We now include in Fig. S7 (new panel D) a graph with quantification in the revised manuscript and emphasize this point (p. 12): “However, under CASM-inducing conditions, no changes were detected (Fig. S7B-D) in interactions between TBC1D5 and LC3A or in levels of VPS35 in LC3A co-IP, a proxy for LC3A-TBC1D5-VPS29/retromer association. This suggests that CASM-inducing treatments and additionally bafilomycin A1 do not affect the status of the TBC1D5-Rab7 system”.        

Does TBC1D5 loss-of-function modulate the numbers of GLUT1 and Gal3 puncta observed in ATG5 deficient cells in response to LLOMe? 

We agree that TBC1D5 is an interesting aspect. However, because TBC1D5 does not change its interactions in the experiments in our study, we consider this topic (i.e. whether TBC1D5 phenocopies VPS35 and ATG5 KOs in its effects on Gal3) to be beyond the scope of the present work. We underscore that LLOMe (lysosomal damage) mis-sorts GLUT1 even without any genetic intervention (e.g., in WT cells in the absence of ATG5 KO; Fig. 7). Thus, in our opinion the effects of TBC1D5 inactivation may be a moot point.  

(3) Finally, the studies here are motivated by experiments in Fig. S1 (as well as other studies from the Deretic and Stallings labs) suggesting unique autophagy-independent functions for ATG5 in myeloid cells and neutrophils in susceptibility to Mycobacterium tuberculosis infection. However, it is curious that no attempt is made to relate the mechanistic data regarding the retromer or GLUT1 receptor mis-sorting back to the infectious models. Do myeloid cells or neutrophils lacking ATG5 have deficiencies in glucose uptake or GLUT1 cell surface levels? 

Reviewer’s point is well taken. Glucose uptake, its metabolism, and diabetes underly resurgence in TB in certain populations and are important factors in a range of other diseases. This was alluded to in our discussion (lines 461-469). However, these are complex topics for future studies. We have now expanded this section of the discussion (p. 18): “In the context of tuberculosis, diabetes, which includes glucose dysregulation, is associated with increased incidence of active disease and adverse outcomes” (Dheda et al., ,PMID: 26377143; Dooley, et al., PMID:19926034).

Reviewer #3 (Public Review): 

In this manuscript, Padder et al. used APEX2 proximity labeling to find an interaction between ATG5 and the core components of the Retromer complex, VPS26, VPS29, and VPS35. Further studies revealed that ATG5 KO inhibited the trafficking of GLUT1 to the plasma membrane. They also found that other autophagy genes involved in membrane atg8ylation affected GLUT1 sorting. However, knocking out other essential autophagy genes such as ATG13 and FIP200 did not affect GLUT1 sorting. These findings suggest that ATG5 participates in the function of the Retromer in a noncanonical autophagy manner. Overall, the methods and techniques employed by the authors largely support their conclusions. These findings are intriguing and significant, enriching our understanding of the non-autophagic functions of autophagy proteins and the sorting of GLUT1.

Nevertheless, there are several issues that the authors need to address to further clarify their conclusions. 

(1) The authors confirmed the interaction between Atg5 and the Retromer complex through Co-IP experiments. Is the interaction between Atg5 and the Retromer direct? If it is direct, which Retromer complex protein regulates the interaction with Atg5? Additionally, does ATG5 K130R mutant enhance its interaction with the Retromer? 

AlphaFold modeling in the initial submission of our study to eLife (absent from the current version) suggested the possibility of a direct interaction between ATG5 and VPS35 with ATG12—ATG5 complex facing outwards, in which case K130R would not matter. However, mutational experiments in putative contact residues did not alter association in co-IPs. So either ATG5 interacts with other retromer subunits or more likely is in a larger protein complex containing retromer. It will take a separate study to dissect associations and find direct interaction partners. 

(2) To more directly elucidate how ATG5 regulates Retromer function by interacting with the Retromer and participates in the trafficking of GLUT1 to the plasma membrane, the authors should identify which region or crucial amino acid residues of ATG5 regulate its interaction with the Retromer. Additionally, they should test whether mutations in ATG5 that disrupt its interaction with the Retromer affect Retromer function (such as participating in the trafficking of GLUT1 to the plasma membrane) and whether they affect Atg8ylation. They also need to assess whether these mutations influence canonical autophagy and lysosomal sensitivity to damage. 

Please see the response to point 1.

Recommendations for the authors.

Reviewer #1 (Recommendations For The Authors): 

While most data are solid and convincing, the following questions need to be addressed before publication: 

Major Concerns: 

(1) Examining only one cargo (GLUT1) is insufficient to reflect the retromer's function comprehensively. At least two additional cargoes should be analyzed to observe the phenotypes more accurately. 

We agree that having another retromer cargo (in addition to GLUT1) would be of interest. We point out that our data also show mis-sorting of SNX27 to lysosomes (Fig. 3H, quantifications in Fig. 3I).  SNX27 in turn sorts nearly 80 ion channels, signaling receptors, and other nutrient transporters. Which of the 80 cargos to prioritize and check (the expectation is that all 80 might be missorted given that they need SNX27)?  We have instead tested MPR, a SNX27-independent cargo. We now include data on effects of ATG5 knockout on CI-MPR (Fig. S9A-F). This is described in the text (p. 14; “Effect of ATG5 knockout on MPR sorting

We tested whether ATG5 affects cation-independent mannose 6-phosphate receptor (CI-MPR). For this, we employed the previously developed methods (Fig. S9A) of monitoring retrograde trafficking of CI-MPR from the plasma membrane to the TGN 70,118-121. In the majority of such studies, CI-MPR antibody is allowed to bind to the extracellular domain of CI-MPR at the plasma membrane and its localization dynamics following endocytosis serves as a proxy for trafficking of CI-MPR. We used ATG5 KOs in HeLa and Huh7 cells and quantified by HCM retrograde trafficking to TGN of antibody-labeled CI-MPR at the cell surface, after being taken up by endocytosis and allowed to undergo intracellular sorting, followed by fixation and staining with TGN46 antibody. There was a minor but statistically significant reduction in CIMPR overlap with TGN46 in HeLaATG5-KO that was comparable to the reduction in HeLa cells when

VPS35 was depleted by CRISPR (HeLaVPS35-KO) (Fig. S9B,C). Morphologically, endocytosed Ab-CI-

MPR appeared dispersed in both HeLaATG5-KO and HeLaVPS35-KO cells relative to HeLaWT cells (Fig. S9D). Similar HCM results were obtained with Huh7 cells (WT vs. ATG5KO; Fig. S9E,F). We interpret these data as evidence of indirect action of ATG5 KO on CI-MPR sorting via membrane homeostasis, although we cannot exclude a direct sorting role via retromer. We favor the former interpretation based on the strength of the effect and the controversial nature of retromer engagement in sorting of CI-MPR (57,70,75,98,120).”)

(2) The evidence from Alphafold predictions is weak. The direct interaction of ATG5 with retromer subunits should be tested. 

Please see the above response to Reviewer 3.

In addition, does retromer also interact with ATG16L1 similarly to the phenomenon in VAIL? 

We fully agree with the reviewer that finding the direct interacting partners between retromer and membrane atg8ylation machinery is an important direction as in our opinion it would expand the repertoire of E3 ligases and its adaptors. However, given the complexity and variety of possibilities, we believe that this is a topic for a future study.  

(3) In Line 166, Figures 2C and 2D, the Gal3 phenotype does not seem to be well complemented by VPS35. 

We have adjusted the text to acknowledge incomplete complementation (p.7). 

(4) In Figures 3 and 4, the authors show that KO of membrane atg8ylation machineries and ATG8-Hexa KO affects the localization of retromer cargo GLUT1 and SNX27. However, the mechanism by which membrane ATG8ylation affects retromer remains unresolved.

Additionally, are other retromer subunits' locations are also affected, if so, how are they impacted? At least a speculative explanation should be provided. 

Following reviewers request, we now state on p. 19 that “one of the limitations of our study is that beyond effects of membrane atg8ylation on quality of lysosomal membrane and its homeostasis there could be more direct effects of membrane modification with mATG8s on retromer that still need to be understood”.

(5) In Figure 3, endogenous IP results are required to examine the interaction of ATG5 with retromer if suitable retromer antibodies for IP are available. 

Endogenous IPs are given in Fig. 1. We have modified text on p. 8 to clarify this.

(6) In Figure 4, ATG8 Hexa KO, and triple KO of LC3s or GABARAPs all increase the localization of GLUT1 on lysosomes. It seems redundant for ATG8 family proteins here.

Can any individual member of the ATG8 family rescue this phenotype? 

If the intent of such complementation analysis is to identify a specific mATG8 responsible for the observed effects, this is already pre-empted by the fact that TKOs also have a similar effect as HEXA mutants (i.e. loss of at least two of mATG8s is enough to cause the phenotype). We now discuss this in the text (p. 10): “Thus, at least two mATG8s, each one from two different mATG8 subclasses (LC3s and GABARAPs) or the entire membrane atg8ylation machinery was engaged in and required for proper GLUT-1 sorting”.  

(7) In Figure 5, knockdown of ATG5 in FIP200 KO cells inhibited GLUT1 sorting from endosomes, leading to its trafficking to lysosomes. However, it is known that very little remnant ATG5 in ATG5 KD cells is enough to support ATG8 lipidation. Therefore, it is essential to repeat this experiment using ATG5/FIP200 double KO or ATG5 KO combined with an autophagy inhibitor. 

We point out to this limitation in the text (p. 11): “….we knocked down ATG5 in FIP200 KO cells (Fig. S5D) and found that GLUT1 puncta and GLUT1+LAMP2+ profiles increased even in the FIP200 KO background with the effects nearing those of VPS35 knockout (Figs. 5D-F and S5C), with the difference between VPS35 KO and ATG5 KD attributable to any residual ATG5 levels in cells subjected to siRNA knockdowns”.

(8) In Figure 7, the authors show that the induction of CASM inhibited GLUT1 sorting from endosomes. However, ATG5 KO, which abolishes membrane ATG8ylation, also inhibits GLUT1 sorting. This seems paradoxical and requires a reasonable explanation or discussion. 

We understand reviewer’s comment. The answer to this paradox is that it is actually the lysosomal damage that causes GLUT1 mis-sorting and not CASM. Membrane atg8ylation, such as CASM and probably other processes given that involvement of both ATG2 and ESCRTs (Fig. 8) counteracts the damage and works in the direction of restoring/maintaining proper retromer-dependent sorting. This is now explained better in the text, and have revised the title of Fig. 7 to read “Lysosomal damage causes GLUT1 mis-sorting”. Our data with bafilomycin A1 show that it is the perturbance of lysosomes (not CASM per se) that leads to mis-sorting of GLUT1 (Fig. 7D,E), and our data with ATG2AB DKO and ESCRT (VPS37A) KO (Fig. 8A-F) indicate that repair of lysosomes is important to keep the retromer working machinery functional (as illustrated in Fig. 8G), which may be one of the effector mechanisms downstream of membrane atg8ylation  in general (and hence also of CASM).  

(9) The immuno-staining results for Figures 7F and 7G are lacking. 

We now provide the requested images.

(10) In Figure 8D, the quality of the image for VPS37 KO cells treated with LLOME is not sufficient to show increased colocalization between GLUT1 and LAMP2. 

We now provide a different example image. We note that these are epiflorescent HCM images  

Minor Concerns: 

(1) It would be better to distinguish the function of the membrane ATG8ylation machinery (i.e., ATG5) from the function of membrane ATG8ylation in the description. No ATG8ylation-deficient mutants were used in this study. 

We have used atg8ylation mutants (e.g. KOs in ATG3, ATG5, ATG7, and ATG16L1). We now emphasize this better in the text (p. 10). 

(2) In Figure 2D, a green box appears there by incident. 

This has been fixed.

(3) In Figure 3A, the conjugate for ATG5-ATG12 is absent in the gel for IB: ATG5.

The ATG5 antibody used in Fig. 3A recognizes primarily the conjugated form of ATG5. This is now clarified in the figure legend. 

(4) Figure 5G is missing in the manuscript. 

Fig 5G is now mentioned in the text. Thank you.

(5) The gRNA sequence information for FIP200 KO is missing in the Methods section. 

Reference(s) to the already published gRNA sequence are in the manuscript. 

(6) Suggest moving the last paragraph in Result section to Discussion section. 

We kept this single-paragraph section in Results as it contains actual data.

Reviewer #2 (Recommendations For The Authors): 

(1) It is unclear why the rescue of VPS35KO cells in Fig 1C-D is so modest. 

Complementation data depend on transfection efficiency and some variability is to be expected.

Reviewer #3 (Recommendations For The Authors): 

(1) Figures 2A, 2C, 2E, and 2G lack scale bars. Figure 2D has a small square above the y axis. 

Relative scale bars are now included. 

(2) Figures S3B, S3D, and S3F lack scale bars. 

Relative scale bars are now included.

Author response:

We thank the Editor and Reviewers for their work on our manuscript, and are happy to receive their positive comments, as well as their questions and suggestions. We are currently revising the manuscript and are planning to de-emphasize Brownian recovery as a simple yet biologically irrelevant benchmark and include comparisons with other biologically inspired strategies suggested by the reviewers. As for sharing the code and data: we completely agree: dataset 1 is already public and we will share the other dataset as well as the code. In a nutshell, we will be addressing the referee’s suggestions as follows:

(1)   As Referee 1 points out, even if the algorithm does not require a map of space, the agent is still required to tell apart North, East, South and West relative to the wind direction which is implicitly assumed known. We will better clarify the spatial encoding required to implement these strategies.

(2)   Referee 1 remarks that the learned recovery strategy works best and suggests to give it a more prominent role and better characterize it. We agree that what is done in the void state is definitely key and more work is needed to understand it. In the revised manuscript, we are planning to further substantiate the statistics of the learned recovery by repeating training several times and comparing several trajectories. Note that this strategy is much more flexible than the others and could potentially mix aspects of recovery to aspects of exploitation: we defer a more in-depth analysis that disentangles these two aspects elsewhere.

(3)   Referee 1 asks whether an optimal, minimal representation of the olfactory states exists. Q learning defines the olfactory states prior to training and does not allow to systematically optimize odor representation for the task. Given the odor features, we can however discretize them in more or less olfactory states. We expect that decreasing the number of olfactory states provides less positional information and potentially degrades performance, although loss in performance may be overshadowed by noise or by efficient recovery. We are planning to re-train our model with a smaller numer of non-void states and will provide the comparison. The number of void states does not need further testing: we chose 50 void states because it matches the time agents typically remain in the void and indeed achieves very high performance (less than 50 void states results in no convergence and more than 50 introduces states that are rarely visited)

(4)   Both reviewers correctly remark that Brownian motion is not biologically relevant. We will make sure to further clarify that this is a rather simple --but biologically irrelevant-- benchmark. We are planning to include results with both circling and zigzaging as biologically inspired recovery strategies.

(5)   We agree with reviewer 2 that animal locomotion does not look like a series of discrete displacements on a checkerboard. However, to overcome this limitation, one has to first focus on a specific system to define actions in a way that best adheres to a species’ motor controls. Second, these actions are likely continuous, which makes reinforcement learning notoriously more complex. While we agree that more realistic models are definitely needed for a comparison with real systems, this remains outside the scope of the current work.

(6)   We agree with the referees and editor that it is important to publish the code and data alongside with the manuscript. It was already planned and we will make sure to share the links within the revised version of the manuscript.

Author response:

The following is the authors’ response to the current reviews.

Reviewer #1 (Public review):

Summary:

The study by Nelson et al. is focused on formation of the Drosophila Posterior Signaling Center (PSC) which ultimately acts as a niche to support hematopoietic stem cells of the lymph gland (LG). Using a combination of genetics and live imaging, the authors show that PSC cells migrate as a tight collective and associate with multiple tissues during a trajectory that positions them at the posterior of the LG.

This is an important study that identifies Slit-Robo signaling as a regulator of PSC morphogenesis, and highlights the complex relationship of interacting cell types - PSC, visceral mesoderm (VM) and cardioblasts (CBs) - in coordinated development of these three tissues during organ development. However, one point requiring clarification is the idea that PSC cells exhibit a collective cell migration; it is not clear that the cells are migrating rather than being pushed to a more dorsal position through dorsal closure and/or other similar large scale embryo movement. This does not detract from the very interesting analysis of PSC morphogenesis as presented.

This Public Review by Reviewer #1 is identical to their original Public Review, thus we are unsure whether Reviewer #1 assessed the revised version of our manuscript, and whether they read our responses to their original Public Review. Below we summarize our original responses to the weaknesses listed for the first version of our manuscript.

Strengths:

• Using expression of Hid or Grim to ablate associated tissues, they find evidence that the VM and CB of the dorsal vessel affect PSC migration/morphology whereas the alary muscles do not. Slit is expressed by both VM and CBs, and therefore Slit-Robo signaling was investigated as PSCs express Robo.

• Using a combination of approaches, the authors convincingly demonstrate that Slit expression in the CBs and VM acts to support PSC positioning. A strength is the ability to knockdown slit levels in particular tissue types using the Gal4 system and RNAi.

• Although in the analysis of robo mutants, the PSC positioning phenotype is weaker in the individual mutants (robo1 and robo2) with only the double mutant (robo1,robo2) exhibiting a phenotype comparable to the slit RNAi. The authors make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs, because PSCs show a phenotype even when CBs do not (Fig 4G).

• New insight into dorsal vessel formation by VM is presented in Fig 4A,B, as loss of the VM can affect dorsal vessel morphogenesis. This result additionally points to the VM as important.

Weaknesses:

• The authors are cautioned to temper the result that Slit-Robo signaling is intrinsic to PSC since loss of robo may affect other cell types (besides CBs and PSCs) to indirectly affect PSC migration/morphogenesis. In fact, in the robo2, robo1 mutant, the VM appears to be incorrectly positioned (Fig. 4G).

We maintain our conclusion, and, we point out that the Reviewer stated, “The authors make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs”. We already added a statement to the Discussion reminding the reader of the possibility of secondary defects (“Finally, it is possible that PSC cells do not intrinsically require Robo activation, but rather CB-independent PSC mis-positioning in sli or robo mutants could be a secondary defect caused by compromised Slit-Robo signaling in some other tissue.”).

• If possible, the authors should use RNAi to knockdown Robo1 and Robo2 levels specifically in the PSCs if a Gal4 is available; might Antp.Gal4 (Fig 1K) be useful? Even if knockdown is achieved in PSCs+CBs, this would be a better/complementary experiment to support the approach outlined in Fig 4D.

As described in our first response, use of Antp-GAL4 with RNAi would be no better than a whole animal double Robo mutant.

• Movies are hard to interpret, as it seems unclear that the PSCs actively migrate rather than being pushed/moved indirectly due to association with VM and CBs/dorsal vessel.

Vm does not directly contact the PSC, so the Vm cannot be physically pushing the PSC. In their original review, Reviewer #3 expressed similar concerns (Weaknesses #1 and #2), and upon their review of our revised manuscript they determined we addressed these concerns.

Reviewer #2 (Public review):

The paper by Nelson KA, et al. explored the collective migration, coalescence and positioning of the posterior signaling center (PSC) cells in Drosophila embryo. With live imaging, the authors observed the dynamic progress of PSC migration. Throughout this process, visceral mesoderm (VM), alary muscles (Ams) and cardioblasts (CBs) are in proximity of PSC. Genetic ablation of these tissues reveals the requirement for VM and CBs, but not AMs in this process. Genetic manipulations further demonstrated that Slit-Robo signaling was critical during PSC migration and positioning. While the genetic mechanisms of positioning the PSC were explored in much detail, including using live imaging, the functional consequence of mispositioning or (partial) absence of PSC cells has not been addressed, but would much increase the relevance of their findings. A few additional issues need to be addressed as well in this otherwise well-done study.

Previous major points:

(1) The only readout in their experiments is the relative correctness of PSC positioning. Importantly, what is the functional consequence if PSC is not properly positioned? This would be particularly important with robo-sli manipulations, where the PSC is present but some cells are misplaced. What is the consequence? Are the LGs affected, like specification of their cell types, structure and function? To address this for at least the robo-slit requirement in the PSC, it may be important to manipulate them directly in the PSC with a split Gal4 system, using Antp and Odd promoters.

We state in our original response that exploring the functional consequences of PSC mis-positioning was outside the scope of this study. Given that the necessary cis-regulatory modules have not been identified at Antp or Odd, creating a split-GAL4 with ‘Antp and Odd promoters’ cannot be accomplished in a reasonable time frame, as we previously detailed in our original response.

(2) The densely, parallel aligned fibers in the lower part of Figure 1J seemed to be visceral mesoderm, but further up (dorsally) that may be epidermis. It is possible that the PSC migrate together with the epidermis? This should be addressed.

This was directly addressed by the additional data included in our revision. When epidermal closure is stalled, the PSC is able to migrate past the stalled leading edge, closer to the midline.

(3) Although the authors described the standards of assessing PSC positioning as "normal" or "abnormal", it is rather subtle at times and variable in the mutant or KD/OE examples. The criteria should be more clearly delineated and analyzed double-blind, also since this is the only readout. Further examples of abnormal positioning in supplementary figures would also help.

We addressed this comment in detail in our original response. Briefly, double-blinding was oftentimes not possible due to the obviousness of the genotype in the image. The criteria we outline for normal PSC positioning is as comprehensive as possible given the subtlety variability of mis-positioning phenotypes. Two of the authors independently analyzed the relatively large sets of samples and arrived at the same conclusions.

(4) Discussion is very lengthy and should shortened.

We shortened the Discussion in the revised version.

Comments on revised version:

Although the authors have responded to my concerns as they deemed suitable, these concerns still stand for the revised version.

Given our responses above and the lack of detail in this comment, we are unsure why the Reviewer is still concerned.

Reviewer #3 (Public review):

Summary:

This work is a detailed and thorough analysis of the morphogenesis of the posterior signaling center (PSC), a hematopoietic niche in the Drosophila larva. Live imaging is performed from the stage of PSC determination until the appearance of a compact lymph gland and PSC in the stage 16 embryo. This analysis is combined with genetic studies that clarify the involvement of adjacent tissue, including the visceral mesoderm, alary muscle, and cardioblasts/dorsal vessel. Lastly, the Slit/Robo signaling system is clearly implicated in the normal formation of the PSC.

Strengths:

The data are clearly presented and well documented, and fully support the conclusions drawn from the different experiments.

The authors have addressed all of my previous comments, in particular concerning the role of epidermal cell rearrangements during dorsal closure as a possible force acting on the movement of PSC cells. The authors have clarified their definition of "collective migration" as it applies to the movement of PSC. The revised paper will make an important contribution to our understanding of the mechanisms driving morphogenesis.

We are appreciative of the time spent by the Reviewer reading our responses and assessing the revision.

---------

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study by Nelson et al. is focused on the formation of the Drosophila Posterior Signaling Center (PSC) which ultimately acts as a niche to support hematopoietic stem cells of the lymph gland (LG). Using a combination of genetics and live imaging, the authors show that PSC cells migrate as a tight collective and associate with multiple tissues during a trajectory that positions them at the posterior of the LG.

This is an important study that identifies Slit-Robo signaling as a regulator of PSC morphogenesis, and highlights the complex relationship of interacting cell types - PSC, visceral mesoderm (VM), and cardioblasts (CBs) - in the coordinated development of these three tissues during organ development. However, one point requiring clarification is the idea that PSC cells exhibit a collective cell migration; it is not clear that the cells are migrating rather than being pushed to a more dorsal position through dorsal closure and/or other similar large-scale embryo movement. This does not detract from the very interesting analysis of PSC morphogenesis as presented.

Since each referee asked for clarification concerning collective cell migration, we present a combined response further below, placed after the comments from Reviewer #3.

Strengths:

(1) Using the expression of Hid or Grim to ablate associated tissues, they find evidence that the VM and CB of the dorsal vessel affect PSC migration/morphology whereas the alary muscles do not. Slit is expressed by both VM and CBs, and therefore Slit-Robo signaling was investigated as PSCs express Robo.

(2) Using a combination of approaches, the authors convincingly demonstrate that Slit expression in the CBs and VM acts to support PSC positioning. A strength is the ability to knockdown slit levels in particular tissue types using the Gal4 system and RNAi.

(3) Although in the analysis of robo mutants, the PSC positioning phenotype is weaker in the individual mutants (robo1 and robo2) with only the double mutant (robo1,robo2) exhibiting a phenotype comparable to the slit RNAi. The authors make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs because PSCs show a phenotype even when CBs do not (Figure 4G).

(4) New insight into dorsal vessel formation by VM is presented in Figure 4A, B, as loss of the VM can affect dorsal vessel morphogenesis. This result additionally points to the VM as important.

Weaknesses:

(1) The authors are cautioned to temper the result that Slit-Robo signaling is intrinsic to PSC since the loss of robo may affect other cell types (besides CBs and PSCs) to indirectly affect PSC migration/morphogenesis. In fact, in the robo2, robo1 mutant, the VM appears to be incorrectly positioned (Figure 4G).

We have reexamined our wording in the relevant Results section and, given that this referee agrees that we, “make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs because PSCs show a phenotype even when CBs do not (Figure 4G)”, it was not clear how we might temper our conclusions more. Given that PSC cells express Robo1 and Robo2, and that the Vm does not contact the PSC, our ‘reasonable argument’ appears fair and parsimonious. Since we agree with the referee that a reader should be made as aware as possible of alternatives, we will add a comment to the Discussion, reminding the reader of the possibility of a secondary defect.

(2) If possible, the authors should use RNAi to knockdown Robo1 and Robo2 levels specifically in the PSCs if a Gal4 is available; might Antp.Gal4 (Fig 1K) be useful? Even if knockdown is achieved in PSCs+CBs, this would be a better/complementary experiment to support the approach outlined in Figure 4D.

While we agree that PSC-specific knockdown of Robo1 and Robo2 simultaneously would be ideal, this is not possible. First, the most-effective UAS-RNAi transgenes (that is, those in a Valium 20 backbone) are both integrated at the same chromosomal position; these cannot be simultaneously crossed with a GAL4 transgenic line to attempt double knock down. Additionally, as with all RNAi approaches that must rely on efficient knockdown over the rapid embryonic period, even having facile access to the above does not ensure the RNAi approach will cause as effective depletion as the genetic null condition that we use. Second, as the referee concedes, there is no embryonic PSC-specific GAL4. The proposed use of Antp-GAL4 would cause knockdown in many tissues (PSC, CB, Vm, epidermis and amnioserosa). This would lead to a reservation similar to that caused by our use of the straight genetic double mutant, as regards potential indirect requirement for Robo function.

(3) Movies are hard to interpret, as it seems unclear that the PSCs actively migrate rather than being pushed/moved indirectly due to association with VM and CBs/dorsal vessel.

First, the Vm does not directly contact the PSC, so it cannot be pushing the PSC dorsally. We will re-examine our text to be certain to make this clear. Second, in our analysis of bin mutants, which lack Vm, LGs and PSCs are able to reach the dorsal midline region in the absence of Vm. Finally, please see our response to Reviewer #3, point 2, for why we maintain that PSC cells are “migrating” even though some PSC cells are attached to CBs.

Reviewer #2 (Public Review):

The paper by Nelson KA, et al. explored the collective migration, coalescence, and positioning of the posterior signaling center (PSC) cells in Drosophila embryo. With live imaging, the authors observed the dynamic progress of PSC migration. Throughout this process, visceral mesoderm (VM), alary muscles (Ams), and cardioblasts (CBs) are in proximity to PSC. Genetic ablation of these tissues reveals the requirement for VM and CBs, but not AMs in this process. Genetic manipulations further demonstrated that Slit-Robo signaling was critical during PSC migration and positioning. While the genetic mechanisms of positioning the PSC were explored in much detail, including using live imaging, the functional consequence of mispositioning or (partial) absence of PSC cells has not been addressed, but would much increase the relevance of their findings. A few additional issues need to be addressed as well in this otherwise well-done study.

Major points:

(1) The only readout in their experiments is the relative correctness of PSC positioning. Importantly, what is the functional consequence if PSC is not properly positioned? This would be particularly important with robo-sli manipulations, where the PSC is present but some cells are misplaced. What is the consequence? Are the LGs affected, like the specification of their cell types, structure, and function? To address this for at least the robo-slit requirement in the PSC, it may be important to manipulate them directly in the PSC with a split Gal4 system, using Antp and Odd promoters.

We agree that the functional consequence of PSC mis-positioning is important and a relevant question to eventually address. However, virtually all markers and reagents used to assess the effect of the PSC on progenitor cells and their differentiated descendants are restricted to analyses carried out on the third larval instar - some three days after the experiments reported here. Most of the manipulated conditions in our work are no longer viable at this phase and, thus, addressing the functional consequences of a malformed PSC will require the field to develop new tools. 

As we noted in the Introduction, the consistency with which the wildtype PSC forms as a coalesced collective at the posterior of the LG strongly suggests importance of its specific positioning and shape, as has now been found for other niches (citations in manuscript). Additionally, in the Discussion we mention the existence of a gap junction-dependent calcium signaling network in the PSC that is important for progenitor maintenance. Without continuity of this network amongst all PSC cells (under conditions of PSC mis-positioning), we strongly anticipate that the balance of progenitors to differentiated hemocytes will be mis-managed, either constitutively, and / or under immune challenge conditions. 

Finally, to our knowledge, the tools do not exist to build a “split Gal4 system using Antp and Odd promoters”. The expression pattern observed using the genomic Antp-GAL4 line must be driven by endogenous enhancers–none of which have been defined by the field, and thus cannot be used in constructing second order drivers. Similarly, for odd skipped, in the embryo the extant Odd-GAL4 driver expresses only in the epidermis, with no expression in the embryonic LG. Thus, the cis regulatory element controlling Odd expression in the embryonic LG is unknown. In the future, the discovery of an embryonic PSC-specific driver will aid in addressing the specific functional consequences of PSC mis-positioning.

(2) The densely, parallel aligned fibers in the part of Figure 1J seemed to be visceral mesoderm, but further up (dorsally) that may be epidermis. It is possible that the PSC migrate together with the epidermis? This should be addressed.

See response to Reviewer #3.

(3) Although the authors described the standards of assessing PSC positioning as "normal" or "abnormal", it is rather subtle at times and variable in the mutant or KD/OE examples. The criteria should be more clearly delineated and analyzed double-blind, also since this is the only readout. Further examples of abnormal positioning in supplementary figures would also help.

We appreciate the Reviewer’s concern and acknowledge that the phenotypes we observed were indeed variable, and, at times subtle. As we show and discuss in the paper, our results revealed that the signaling requirements for proper PSC positioning are complex; this was favorably commented upon by Reviewer #1 (“...highlights the complex relationship of interacting cell types - PSC, visceral mesoderm (VM), and cardioblasts (CBs) - in the coordinated development of these three tissues during organ development.…”). We suspect the phenotypic variability is attributable to any number of biological differences such as heterogeneity of PSC cells and an accompanying difference in the timing of their competence to receive and respond to Slit-Robo signaling, the timing of release of Slit from CBs and Vm, number of cells in a given PSC, which PSC cells in the cluster respond to too little or too much signaling, and/or typical variability between organisms. Furthermore, PSC positioning analyses were conducted by two of the authors, who independently came to the same conclusions. For many of the manipulations double blinding was not possible since the genotype of the embryo was discernible due to the obvious phenotype of the manipulated tissue.

(4) The Discussion is very lengthy and should shortened.

We will re-examine the prose and emphasize more conciseness, while maintaining clarity for the reader.

Reviewer #3 (Public Review):

Summary:

This work is a detailed and thorough analysis of the morphogenesis of the posterior signaling center (PSC), a hematopoietic niche in the Drosophila larva. Live imaging is performed from the stage of PSC determination until the appearance of a compact lymph gland and PSC in the stage 16 embryo. This analysis is combined with genetic studies that clarify the involvement of adjacent tissue, including the visceral mesoderm, alary muscle, and cardioblasts/dorsal vessels. Lastly, the Slit/Robo signaling system is clearly implicated in the normal formation of the PSC.

Strengths:

The data are clearly presented, well documented, and fully support the conclusions drawn from the different experiments. The manuscript differs in character from the mainstay of "big data" papers (for example, no sets of single-cell RNAseq data of, for instance, PSC cells with more or less Slit input, are offered), but what it lacks in this regard, it makes up in carefully planned and executed visualizations and genetic manipulations.

Weaknesses:

A few suggestions concerning improvement of the way the story is told and contextualized.

(1) The minute cluster of PSC progenitors (5 or so cells per side) is embedded (as known before and shown nicely in this study) in other "migrating" cell pools, like the cardioblasts, pericardial cells, lymph gland progenitors, alary muscle progenitors. These all appear to move more or less synchronously. What should also be mentioned is another tissue, the dorsal epidermis, which also "moves" (better: stretches?) towards the dorsal midline during dorsal closure. Would it be reasonable to speculate (based on previously published data) that without the force of dorsal closure, operating in the epidermis, at least the lateral>medial component of the "migration" of the PSC (and neighboring tissues) would be missing? If dorsal closure is blocked, do essential components of PSC and lymph gland morphogenesis (except for the coming-together of the left and right halves) still occur? Are there any published data on this?

Each of the Reviewers is interested in our response to this very relevant question, and, thus, we will address the issue en bloc here. First, we will add a Supplementary Figure showing that LG and CBs are still able to progress medially towards the dorsal midline when dorsal closure stalls.  This rules out any major effect for the most prominent “large-scale embryo cell sheet movement” in positioning the PSC. Second, published work by Haack et. al. and Balaghi et. al. shows that CBs and leading edge epidermal cells are independently migratory, and we will add this context to the manuscript for the reader.

(2) Along similar lines: the process of PSC formation is characterized as "migration". To be fair: the authors bring up the possibility that some of the phenotypes they observe could be "passive"/secondary: "Thus, it became important to test whether all PSC phenotypes might be 'passive', explained by PSC attachment to a malforming dorsal vessel. Alternatively, the PSC defects could reflect a requirement for Robo activation directly in PSC cells." And the issue is resolved satisfactorily. But more generally, "cell migration" implies active displacement (by cytoskeletal forces) of cells relative to a substrate or to their neighbors (like for example migration of hemocytes). This to me doesn't seem really clearly to happen here for the dorsal mesodermal structures. Couldn't one rather characterize the assembly of PSC, lymph gland, pericardial cells, and dorsal vessel in terms of differential adhesion, on top of a more general adhesion of cells to each other and the epidermis, and then dorsal closure as a driving force for cell displacement? The authors should bring in the published literature to provide a background that does (or does not) justify the term "migration".

Before addressing this specifically, we remind readers of our response above that states the rationale ruling out large, embryo-scale movements, such as epidermal dorsal closure, in driving PSC positioning. So, how are PSC cells arriving at their reproducible position? This manuscript reports the first live-imaging of the PSC as it comes to be positioned in the embryo. We interpret these movies to suggest strongly that these cells are a ‘collective’ that migrates. Neither the data, nor we, are asserting that each PSC cell is ‘individually’ migrating to its final position. Rather, our data suggest that the PSC migrates as a collective. The most paradigmatic example of directed, collective cell migration, is of Drosophila ovarian border cells. That cell cluster is surrounded at all times by other cells (nurse cells, in that case), and for the collective to traverse through the tissue, the process requires constant remodeling of associations amongst the migrating cells in the collective (the border cells), as well as between cells in the collective and those outside of it (the nurse cells). In fact, the nurse cells are considered the substrate upon which border cells migrate. Note also that in collective border cell migration cells within the collective can switch neighbors, suggesting dynamic changes to cell associations and adhesions. 

In our analysis, the PSC cells exhibit qualities reminiscent of the border cells, and thus we infer that the PSC constitutes a migratory cell collective.  We also show in Figure 1H that PSC cells exhibit cellular extensions, and thus have a very active, intrinsic actin-based cytoskeleton. In fact, in Figure 1I, we point out that PSC cells shift position within the collective, which is not only a direct feature of migration, but also occurs within the border cell collective as that collective migrates. Additionally, the fact that the lateral-most PSC cells shift position in the collective while remaining a part of the collective–and they do this while executing net directional movement–makes a strong argument that the PSC is migratory, as no cell types other than PSCs are contacting the surfaces of those shifting PSC cells. Lastly, the Reviewer’s supposition that, rather than migration, dorsal mesoderm structures form via “differential adhesion, on top of a more general adhesion of cells to each other” is, actually, precisely an inherent aspect of collective cell migration as summarized above for the ovarian border collective.

In our resubmission we will adjust text citing the existing literature to better put into context the reasoning for why PSC formation based on our data is an example of collective cell migration.

(3) That brings up the mechanistic centerpiece of this story, the Slit/Robo system. First: I suggest adding more detailed data from the study by Morin-Poulard et al 2016, in the Introduction, since these authors had already implicated Slit-Robo in PSC function and offered a concrete molecular mechanism: "vascular cells produce Slit that activates Robo receptors in the PSC. Robo activation controls proliferation and clustering of PSC cells by regulating Myc, and small GTPase and DE-cadherin activity, respectively". As stated in the Discussion: the mechanism of Slit/Robo action on the PSC in the embryo is likely different, since DE-cadherin is not expressed in the embryonic PSC; however, it maybe not be THAT different: it could also act on adhesion between PSC cells themselves and their neighbors. What are other adhesion proteins that appear in the late lateral mesodermal structures?

Could DN-cadherin or Fasciclins be involved?

We agree with the Reviewer that Slit-Robo signaling likely acts in part on the PSC by affecting PSC cell adhesion to each other and/or to CBs (lines 428-435). As stated in the Discussion, we do not observe Fasciclin III expression in the PSC until late stages when the PSC has already been positioned, suggesting that Fasciclin III is not an active player in PSC formation. Assessing whether the PSC expresses any other of the suite of potential cell adhesion molecules such as DN-Cadherin or other Fasciclins, and then study their potential involvement in the Slit-Robo pathway in PSC cells, would be part of a follow-up study.  

Recommendations for the authors:

Reviewing Editor Comments:

The authors are encouraged to address several key issues and provide more explicit clarification when interpreting the behavior of the PSC cells as "migration." It is recommended that the authors engage with all reviewers' comments and refine the text based on the feedback they find valuable.

Reviewer #1 (Recommendations For The Authors):

Major concerns:

(1) Is it possible to assay robo1 and/or robo1 RNAi in a tissue-specific manner to further explore an intrinsic role in the PSC? Might the VM indirectly affect PSCs in a CB-independent manner? How does this affect the interpretation of results in Figure 4.

See also our response to Reviewer #1, Public review weaknesses #2.

Though we agree with the Reviewer that this is the better experiment to test for an intrinsic role for Robo in the PSC, this experiment is not possible at this time. As we noted in the manuscript, we do not yet have an embryonic PSC-specific GAL4, though we have been putting efforts towards identifying/developing such a tool. The Antp-GAL4 driver we used in this study will drive not only in both PSCs and CBs, but also in Vm, epidermis, and amnioserosa, as well as other tissues. The other available embryonic PSC drivers are not specific to the PSC and will drive expression in CBs and Vm, at minimum. This, combined with the reality that RNAi can be ineffective in embryonic tissues, resulted in our use of whole organism mutants to best address this question. 

We acknowledge that it is possible the Vm indirectly effects the PSC in a CB-independent manner in the double Robo mutant, and we added a statement to the Discussion reiterating this point. However, because the PSC expresses Robo1 and Robo2, we maintain that the simplest interpretation of the results in Figure 4 is that PSC cells require intrinsic Robo signaling. And, as we state in the manuscript, it is possible that Slit signals directly from Vm to Robo on the PSC.

(2) As this is the first study to be presenting PSC formation as involving collective cell migration, can the authors provide experimental evidence and rationale for this categorization?

We have added our rationale to the Results section in the revision.

See also our response to Reviewer #3, Public review weakness #2.

(3) The Slit staining presented in Fig 3 W', Z' should be quantified. Furthermore, what is the VM phenotype when Robo1 is overexpressed? Is there a VM-specific phenotype and could this indirect effect cause the PSC to misform/mismigrate?

We didn’t quantify Slit levels in the Vm-specific Robo overexpression condition because there was a visually striking difference compared to controls (increased intensity and specific localization to Vm membranes), and the manipulation resulted in a PSC phenotype. Thus, the evidence we show appears sufficient to strongly suggest that our genetic manipulation resulted in successful trapping of Slit on the Vm.

As to a Vm phenotype when Robo1 is overexpressed Vm-specifically: we know Vm is present, but we haven’t performed an in-depth phenotypic analysis. In the manuscript we show that this manipulation at least affects organization of PSC-adjacent CBs, which we go on to show is correlated with mis-positioned PSCs. Thus, the PSC phenotype in this condition is not solely due to a Vm-specific phenotype.

Minor concerns/suggestions:

(1) I might have missed it but where are the Movies referenced in the text? Are legends provided for the videos? It is important that this is included in the final version (or more clearly presented if I missed it).

We thank you the Reviewer for pointing this out; we now direct the reader to the movies at appropriate places within the text.

(2) In Figure 5, it might be helpful to add a third column to A in which the PSCs are pseudo-colored and thus highlighted because it is difficult to discern the white (not pink) PSCs...

We appreciate the suggestion and now include these panels as Figure 5A’’ in the revision.

(3) If I am following correctly, the lost PSC cells in Figure 5 don't move. Doesn't this suggest that what is critical is that the PSCs attach to the VM and/or CBs, and not necessarily that they are an actively migrating cell type? They "move" but might be passively carried.

See also the response to Reviewer #3, Public reviews weaknesses #2.

The Reviewer is correct that the PSC cells in Fig. 5 don’t move very much, but we interpret this differently from the Reviewer. After detachment of the cells in question they undergo dramatic shape changes, indicating active cytoskeletal remodeling, so the molecular machinery needed for migration appears to remain intact. Thus, we suggest that this observation actually emphasizes our finding that collectivity is needed for the migration. Given the consistency of PSC coalescence/collectivity and the intricate regulation that controls it, we believe it to be an integral part of PSC identity. When PSC cells become detached, they likely lose an aspect of their identity. In various manipulations we’ve noted instances of severely dispersed PSC cells expressing very low levels of identity markers Antp or Odd. Cells in such cases are likely compromised for their function, and this can include, for example, whether they can properly sense cues for migration.

Reviewer #2 (Recommendations For The Authors):

Minor points:

(1) The expression pattern of Antp-Gal4 > myrGFP in the whole embryo should be shown to better demonstrate the overlap with Odd. How does it compare with Antp-Gal4 > CD8::GFP?

We do not understand the question posed. We are not suggesting that Antp and Odd overlap in all cells, nor even many cells. It has been demonstrated by the field that co-expression among mesodermal cells, in the position where LG cells are specified, is a marker for the PSC. We have not thoroughly investigated all reporter lines for the GAL4 drivers used by the field.

(2) Does Tincdelta4-Gal4 not at all express in the PSC? This should be verified.

This question appears to refer to depletion of Slit by RNAi or cell killing driven by tinCΔ4-GAL4. TinCΔ4-GAL4 is expressed in CBs and in precisely 1 embryonic PSC cell. First, Slit isn’t expressed by any PSC cells to our eye, so any PSC mis-positioning observed upon tinCΔ4>Sli RNAi implicates CB involvement in PSC positioning. In designing tests for CB involvement, we were unable to identify any mutant known to lack CBs (or have fewer CBs) that didn’t also affect specification of the LG/PSC. The cell killing approach seemed best.  It is possible that, in this scenario, perhaps ablation of a single, key PSC cell could affect final positioning of the other PSCs, but we think that less likely than a role for CBs. We also retain our original conclusion due to the fact that we often find mis-positioned PSC cells adjacent to mis-positioned CBs, including in the panel representing the CB ablation experiment, Figure 2S.  

(3) Line 212: The data provide evidence that Vm is necessary, but clearly not sufficient, as CBs are also necessary.

We see how this wording was misleading and have adjusted the text accordingly.

(4) The CBs are not visible in Figure 3B.

We are unsure what the Reviewer is referring to, as we are certain that the signal between the blue outlines is indeed Slit expression in CBs.

Reviewer #3 (Recommendations For The Authors):

One minor mistake (I believe): in line 229 it should say "3C and 3D"

We have corrected this error.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews

Reviewer #1 (Public Review): 

(1) Although the theory is based on memory, it also is based on spatially-selective cells.

Not all cells in the hippocampus fulfill the criteria of place/HD/border/grid cells, and place a role in memory. E.g., Tonegawa, Buszaki labs' work does not focus on only those cells, and there are certainly a lot of non-pure spatial cells in monkeys (Martinez-Trujillo) and humans (iEEG). Does the author mainly focus on saying that "spatial cells" are memory, but do not account for non-spatial memory cells? This seems to be an incomplete account of memory - which is fine, but the way the model is set up suggests that *all* memory is, place (what/where), and non-spatial attributes ("grid") - but cells that don't fulfil these criteria in MTL (Diehl et al., 2017, Neuron; non-grid cells; Schaeffer et al., 2022, ICML; Luo et al., 2024, bioRxiv) certainly contribute to memory, and even navigation. This is also related to the question of whether these cell definitions matter at all (Luo et al., 2024). The authors note "However, this memory conjunction view of the MTL must be reconciled with the rodent electrophysiology finding that most cells in MTL appear to have receptive fields related to some aspect of spatial navigation (Boccara et al., 2010; Grieves & Jeffery, 2017). The paucity of non-spatial cells in MTL could be explained if grid cells have been mischaracterized as spatial." Is the author mainly talking about rodent work?

There is a new section in the introduction that deals with these issues, titled ‘Why Model the Rodent Navigation Literature with a Memory Model?’ That section reads:

“Spatial navigation is inherently a memory problem – learning the spatial arrangement of a new enclosure requires memory for the conjunction of what and where. This has long been realized and in the introduction to ‘Hippocampus as a Cognitive Map’, O’Keefe and Nadel (1978) wrote “We shall argue that the hippocampus is the core of a neural memory system providing an objective spatial framework within which the items and events of an organism's experience are located and interrelated” (emphasis added). Furthermore, in the last chapter of their book, they extended cognitive map theory to human memory for non-spatial characteristics. However, in the decades since the development of cognitive map theory, the rodent spatial navigation and human memory literatures have progressed somewhat independently.

The ideas proposed in this model are an attempt to reunify these literatures by returning to the original claim that spatial navigation is inherently a memory problem. The goal of the current study is to explain the rodent spatial navigation literature using a memory model that has the potential to also explain the human memory literature. In contrast, most grid cell models (Bellmund et al., 2016; Bush et al., 2015; Castro & Aguiar, 2014; Hasselmo, 2009; Mhatre et al., 2012; Solstad et al., 2006; Sorscher et al., 2023; Stepanyuk, 2015; Widloski & Fiete, 2014) are domain specific models of spatial navigation and as such, they do not lend themselves to explanations of human memory. Thus, the reason to prefer this model is parsimony. Rather than needing to develop a theory of memory that is separate from a theory of spatial navigation, it might be possible to address both literatures with a unified account.

This study does not attempt to falsify other theories of grid cells. Instead, this model reaches a radically different interpretation regarding the function of grid cells; an interpretation that emerges from viewing spatial navigation as a memory problem. All other grid cell models assume that an entorhinal grid cell displaying a spatially arranged grid of firing fields serves the function of spatial coding (i.e., spatial grid cells exist to support a spatial metric). In contrast, the proposed memory model of grid cells assumes that the hexagonal tiling reflects the need to keep memories separate from each other to minimize confusion and confabulation – the grid pattern is the byproduct of pattern separation between memories rather than the basis of a spatial code. 

It is now understood that grid-like firing fields can occur for non-spatial twodimensional spaces. For instance, human entorhinal cortex exhibits grid-like responses to video morph trajectories in a two-dimensional bird neck-length versus bird leg-length space (Constantinescu et al., 2016). As a general theory of learning and memory, the proposed memory model of grid cells is easily extended to explain these results (e.g., relabeling the border cell inputs in the model as neck-length and leg-length inputs). However, there are other grid cell models that can explain both spatial grid cells as well as non-spatial grid-like responses (Mok & Love, 2019; Rodríguez-Domínguez & Caplan, 2019; Stachenfeld et al., 2017; Wei et al., 2015). Similar to this memory model of grid cells, these models are also positioned to explain both the rodent spatial navigation and human memory literatures. Nevertheless, there is a key difference between this model and other grid cell models that generalize to non-spatial representations. Specifically, these other models assume that grid cells exhibiting spatial receptive fields serve the function of identifying positions in the environment (i.e., their function is spatial). As such, these models do not explain why most of the input to rodent hippocampus appears to be spatial (Boccara et al., 2010; Diehl et al., 2017; Grieves & Jeffery, 2017). This memory model of grid cells provides an answer to the apparent paucity of nonspatial cell types in rodent MTL by proposing that grid cells with spatial receptive fields have been misclassified as spatial (they are what cells rather than where cells) and that place cells are fundamentally memory cells that conjoin what and where.”

(2) Related to the last point, how about non-grid multi-field mEC cells? In theory, these also should be the same; but the author only presents perfect-look grid cells. In empirical work, clearly, this is not the case, and many mEC cells are multi-field non-grid cells (Diehl et al., 2017). Does the model find these cells? Do they play a different role? As noted by the author "Because the non-spatial attributes are constant throughout the two-dimensional surface, this results in an array of discrete memory locations that are approximately hexagonal (as explained in the Model Methods, an "online" memory consolidation process employing pattern separation rapidly turns an approximately hexagonal array into one that is precisely hexagonal). " If they are indeed all precisely hexagonal, does that mean the model doesn't have non-grid spatial cells? 

Grid cells with irregular firing fields are now considered in the discussion with the following paragraphs

“According to this model, hexagonally arranged grid cells should be the exception rather than the rule when considering more naturalistic environments. In a more ecologically valid situation, such as with landmarks, varied sounds, food sources, threats, and interactions with conspecifics, there may still be remembered locations were events occurred or remembered properties can be found, but because the non-spatial properties are non-uniform in the environment, the arrangement of memory feedback will be irregular, reflecting the varied nature of the environment. This may explain the finding that even in a situation where there are regular hexagonal grid cells, there are often irregular non-grid cells that have a reliable multi-location firing field, but the arrangement of the firing fields is irregular (Diehl et al., 2017). For instance, even when navigating in an enclosure that has uniform properties as dictated by experimental procedures, they may be other properties that were not well-controlled (e.g., a view of exterior lighting in some locations but not others), and these uncontrolled properties may produce an irregular grid (i.e., because the uncontrolled properties are reliably associated with some locations but not others, hippocampal memory feedback triggers retrieval of those properties in the associations locations).

In this memory model, there are other situations in which an irregular but reliable multilocation grid may occur, even when everything is well controlled. In the reported simulations, when the hippocampal place cells were based on variation in X/Y (as defined by Border cells), nothing else changed as a function of location, and the model rapidly produced a precise hexagonal arrangement of hippocampal place cell memories. When head direction was included (i.e., real-world variation in X, Y, and head direction), the model still produced a hexagonal arrangement as per face-centered cubic packing of memories, but this precise arrangement was slower to emerge, with place cells continuing to shift their positions until the borders of the enclosure were sufficiently well learned from multiple viewpoints. If there is real-world variation in four or more dimensions, as is likely the case in a more ecologically valid situation, it will be even harder for place cell memories to settle on a precise regular lattice. Furthermore, in the case of four dimensions, mathematicians studying the “sphere packing problem” recently concluded that densest packing is irregular (Campos et al., 2023). This may explain why the multifield grid cells for freely flying bats have a systematic minimum distance between firing fields, but their arrangement is globally irregular (Ginosar et al., 2021). Assuming that the memories encoded by a bat include not just the three real-world dimensions of variation, but also head direction, the grid will likely be irregular even under optimal conditions of laboratory control.”

(3) Theoretical reasons for why the model is put together this way, and why grid cells must be coding a non-spatial attribute: Is this account more data-driven (fits the data so formulated this way), or is it theoretical - there is a reason why place, border, grid cells are formulated to be like this. For example, is it an efficient way to code these variables? It can be both, like how the BVC model makes theoretical sense that you can use boundaries to determine a specific location (and so place cell), but also works (creates realistic place cells). 

The motivation for this model is now articulated in the new section, quoted above, titled ‘Why Model the Rodent Navigation Literature with a Memory Model?’ Regarding the assumption that border cells provide a spatial metric, this assumption is made for the same reasons as in the BVC model. Regarding this, the text said: “These assumptions regarding border cells are based on the boundary vector cell (BVC) model of Barry et al. (2006). As in the BVC model, combinations of border cells encode where each memory occurred in the realworld X/Y plane.”. A new sentence is added to model methods, stating: “This assumption is made because border cells provide an efficient representation of Euclidean space (e.g., if the animal knows how far it is from different walls of the enclosure, this already available information can be used to calculate location).”

But in this case, the purpose of grid cell coding a non-spatial attribute, and having some kind of system where it doesn't fire at all locations seems a little arbitrary. If it's not encoding a spatial attribute, it doesn't have to have a spatial field. For example, it could fire in the whole arena - which some cells do (and don't pass the criteria of spatial cells as they are not spatially "selective" to another location, related to above).  

Some cells have a constant high firing rate, but they are the exception rather than the rule. More typically, cells habituate in the presence of ongoing excitatory drive and by doing so become sensitive to fluctuations in excitatory drive. Habituation is advantageous both in terms of metabolic cost and in terms of function (i.e., sensitivity to change). This is now explained in the following paragraph:

“In theory, a cell representing a non-spatial attribute found at all locations of an enclosure (aka, a grid cell in the context of this model), could fire constantly within the enclosure. However, in practice, cells habituate and rapidly reduce their firing rate by an order of magnitude when their preferred stimulus is presented without cessation (Abbott et al., 1997; Tsodyks & Markram, 1997). After habituation, the firing rate of the cell fluctuates with minor variation in the strength of the excitatory drive. In other words, habituation allows the cell to become sensitive to changes in the excitatory drive (Huber & O’Reilly, 2003). Thus, if there is stronger top-down memory feedback in some locations as compared to others, the cell will fire at a higher rate in those remembered locations rather than in all locations even though the attribute is found at all locations. In brief when faced with constant excitatory drive, the cell accommodates, and becomes sensitive to change in the magnitude of the excitatory drive. In the model simulation, this dynamic adaptation is captured by supposing that cells fire 5% of the time on-average across the simulation, regardless of their excitatory inputs.”

(4) Why are grid cells given such a large role for encoding non-spatial attributes? If anything, shouldn't it be lateral EC or perirhinal cortex? Of course, they both could, but there is less reason to think this, at least for rodent mEC.  

This is a good point and the following paragraph has been added to the introduction to explain that lateral EC is likely part of the explanation. But even when including lateral EC, it still appears that most of the input to hippocampus is spatial.

“One possible answer to the apparent lack of non-spatial cells in MTL is to highlight the role of the lateral entorhinal cortex (LEC) as the source of non-spatial what information for memory encoding (Deshmukh & Knierim, 2011). LEC can be contrasted with mEC, which appears to only provide where information (Boccara et al., 2010a; Diehl et al., 2017). Although it is generally true that LEC is involved in non-spatial processing, there is evidence that LEC provides some forms of spatial information (Knierim et al., 2014). The kind of non-spatial information provided by LEC appears to be in relation to objects (Connor & Knierim, 2017; Wilson et al., 2013). However, in a typical rodent spatial navigation study there are no objects within the enclosure. Thus, although the distinction between mEC and LEC is likely part of the explanation, it is still the case that rodent entorhinal input to hippocampus appears to heavily favor spatial information.”

(5) Clarification: why do place cells and grid cells differ in terms of stability in the model? Place cells are not stable initially but grid cells come out immediately. They seem directly connected so a bit unclear why; especially if place cell feedback leads to grid cell fields. There is an explanation in the text - based on grid cells coding the on-average memories, but these should be based on place cell inputs as well. So how is it that place fields are unstable then grid fields do not move at all? I wonder if a set of images or videos (gifs) showing the differences in spatial learning would be nice and clarify this point.  

In this revision, I provide a new video focused on learning of place cell memories that include head direction. This second video is in relation to the results reported in Figure 9. The short answer is that the grid fields for the non-spatial cell are based on the average across several view-dependent memories (i.e., across several place cells that have head direction sensitivity) and the average is reliable even if the place cells are unstable. The text of this explanation now reads:

“Why was the grid immediately apparent for the non-spatial attribute cell whereas the grid took considerable prior experience for the head direction cells? The answer relates to memory consolidation and the shifting nature of the hippocampal place cells. Head direction cells only produced a reliable grid once the hippocampal place cells (aka, memory cells) assumed stable locations. During the first few sessions, the hippocampal place cells were shifting their positions owing to pattern separation and consolidation. But once the place cells stabilized, they provided reliable top-down memory feedback to the head direction cells in some places but not others, thus producing a reliable grid arrangement to the firing maps of the head direction cells. In other words, for the head direction cells, the grid only appeared once the place cells stabilized. This slow stabilization of place fields is a known property (Bostock et al., 1991; Frank et al., 2004).

In the simulation, the place cells did not stabilize until a sufficient number of place cells were created (Figure 9C). Specifically, these additional memories were located immediately outside the enclosure, around all borders (Figure 9D). These “outside the box” memories served to constrain the interior place cells, locking them in position despite ongoing consolidation. This dynamic can be seen in a movie showing a representative simulation. The movie shows the positions of the head direction sensitive place cells during initial learning, and then during additional sessions of prior experience as the movie speeds up (see link in Figure 9 capture).

Why did the non-spatial grid cell (k) produce a grid immediately, before the place cells stabilized? As discussed in relation to Figure 8, the non-spatial grid cell is the projection through the 3D volume of real-world coordinates that includes X, Y, and head direction. Each grid field of a non-spatial grid cell reflects feedback from several place cells that each have a different head direction sensitivity (see for instance the allocentric pairs of memories illustrated in Figure 8C and 8D). Thus, each grid field is the average across several memories that entail different viewpoints and this averaging across memories provides stability even if the individual memories are not yet stable. This average of unstable memories produces a blurry sort of grid pattern without any prior experience.

A final piece of the puzzle relies on the same mechanism that caused the grid pattern to align with the borders as reported in the results of Figures 6 and 7. Specifically, there are some “sticky” locations with ongoing consolidation because the connection weights are bounded. Because weights cannot go below their minimum or above their maximum, it is slightly more difficult for consolidation to push or pull connection weights over the peak value or under the minimum value of the tuning curve. Thus, the place cells tend to linger in locations that correspond to the peak or trough of a border cell. There are multiple peak and trough locations but for the parameter values in this simulation, the grid pattern seen in Figure 9C shows the set of peak/trough locations that satisfy the desired spacing between memories. Thus, the average across memories shows a reliable grid field at these locations even though the memories are unstable.”

(6) Other predictions. Clearly, the model makes many interesting (and quite specific!) predictions. But does it make some known simple predictions? 

• More place cells at rewarded (or more visited) locations. Some empirical researchers seem to think this is not as obvious as it seems (e.g., Duvellle et al., 2019; JoN; Nyberg et al., 2021, Neuron Review).  

• Grid cell field moves toward reward (Butler et al., 2019; Boccera et al., 2019).  

• Grid cells deform in trapezoid (Krupic et al., 2015) and change in environments like mazes (Derikman et al., 2014).  

Thank you for these suggestions and I have added the following paragraph to the discussion:

“In terms of the animal’s internal state, all locations in the enclosure may be viewed as equally aversive and unrewarding, which is a memorable characteristic of the enclosure. Reward, or lack thereof, is arguably one of the most important nonspatial characteristics and application of this model to reward might explain the existence of goal-related activity in place cells (Hok et al., 2007; although see Duvelle et al., 2019), reflecting the need to remember rewarding locations for goal directed behavior. Furthermore, if place cell memories for a rewarding location activate entorhinal grid cells, this may explain the finding that grid cells remap in an enclosure with a rewarded location such that firing fields are attracted to that location (Boccara et al., 2019; Butler et al., 2019). Studies that introduce reward into the enclosure are an important first step in terms of examining what happens to grid cells when the animal is placed in a more varied environment.”

Regarding the changes in shape of the environment, this was discussed in the section of the paper that reads “As seen in Figure 12, because all but one of the place cells was exterior when the simulated animal was constrained to a narrow passage, the hippocampal place cell memories were no longer arranged in a hexagonal grid. This disruption of the grid array for narrow passages might explain the finding that the grid pattern (of grid cells) is disrupted in the thin corner of a trapezoid (Krupic et al., 2015) and disrupted when a previously open enclosure is converted to a hairpin maze by insertion of additional walls within the enclosure (Derdikman et al., 2009).” This particular section of the paper now appears in the Appendix and Figure 12 is now Appendix Figure 2.

Reviewer #2 (Public Review): 

The manuscript describes a new framework for thinking about the place and grid cell system in the hippocampus and entorhinal cortex in which these cells are fundamentally involved in supporting non-spatial information coding. If this framework were shown to be correct, it could have high impact because it would suggest a completely new way of thinking about the mammalian memory system in which this system is non-spatial. Although this idea is intriguing and thought-provoking, a very significant caveat is that the paper does not provide evidence that specifically supports its framework and rules out the alternate interpretations. Thus, although the work provides interesting new ideas, it leaves the reader with more questions than answers because it does not rule out any earlier ideas. 

Basically, the strongest claim in the paper, that grid cells are inherently non-spatial, cannot be specifically evaluated versus existing frameworks on the basis of the evidence that is shown here. If, for example, the author had provided behavioral experiments showing that human memory encoding/retrieval performance shifts in relation to the predictions of the model following changes in the environment, it would have been potentially exciting because it could potentially support the author's reconceptualization of this system. But in its current form, the paper merely shows that a new type of model is capable of explaining the existing findings. There is not adequate data or results to show that the new model is a significantly better fit to the data compared to earlier models, which limits the impact of the work. In fact, there are some key data points in which the earlier models seem to better fit the data.  

Overall, I would be more convinced that the findings from the paper are impactful if the author showed specific animal memory behavioral results that were only supported by their memory model but not by a purely spatial model. Perhaps the author could run new experiments to show that there are specific patterns of human or animal behavior that are only explained by their memory model and not by earlier models. But in its current form, I cannot rule out the existing frameworks and I believe some of the claims in this regard are overstated. 

As previously detailed in Box 1 and as explained in the text in several places, the model provides an explanation of several findings that remain unexplained by other theories (see “Results Uniquely Explained by the Memory Model”). But more generally this is a good point, and the initial draft failed to fully articulate why a researcher might choose this model to guide future empirical investigations. A new section in the introduction that deals with these issues, titled ‘Why Model the Rodent Navigation Literature with a Memory Model?’ That section reads:

“Spatial navigation is inherently a memory problem – learning the spatial arrangement of a new enclosure requires memory for the conjunction of what and where. This has long been realized and in the introduction to ‘Hippocampus as a Cognitive Map’, O’Keefe and Nadel (1978) wrote “We shall argue that the hippocampus is the core of a neural memory system providing an objective spatial framework within which the items and events of an organism's experience are located and interrelated” (emphasis added). Furthermore, in the last chapter of their book, they extended cognitive map theory to human memory for non-spatial characteristics. However, in the decades since the development of cognitive map theory, the rodent spatial navigation and human memory literatures have progressed somewhat independently.

The ideas proposed in this model are an attempt to reunify these literatures by returning to the original claim that spatial navigation is inherently a memory problem. The goal of the current study is to explain the rodent spatial navigation literature using a memory model that has the potential to also explain the human memory literature. In contrast, most grid cell models (Bellmund et al., 2016; Bush et al., 2015; Castro & Aguiar, 2014; Hasselmo, 2009; Mhatre et al., 2012; Solstad et al., 2006; Sorscher et al., 2023; Stepanyuk, 2015; Widloski & Fiete, 2014) are domain specific models of spatial navigation and as such, they do not lend themselves to explanations of human memory. Thus, the reason to prefer this model is parsimony. Rather than needing to develop a theory of memory that is separate from a theory of spatial navigation, it might be possible to address both literatures with a unified account.

This study does not attempt to falsify other theories of grid cells. Instead, this model reaches a radically different interpretation regarding the function of grid cells; an interpretation that emerges from viewing spatial navigation as a memory problem. All other grid cell models assume that an entorhinal grid cell displaying a spatially arranged grid of firing fields serves the function of spatial coding (i.e., spatial grid cells exist to support a spatial metric). In contrast, the proposed memory model of grid cells assumes that the hexagonal tiling reflects the need to keep memories separate from each other to minimize confusion and confabulation – the grid pattern is the byproduct of pattern separation between memories rather than the basis of a spatial code. 

It is now understood that grid-like firing fields can occur for non-spatial twodimensional spaces. For instance, human entorhinal cortex exhibits grid-like responses to video morph trajectories in a two-dimensional bird neck-length versus bird leg-length space (Constantinescu et al., 2016). As a general theory of learning and memory, the proposed memory model of grid cells is easily extended to explain these results (e.g., relabeling the border cell inputs in the model as neck-length and leg-length inputs). However, there are other grid cell models that can explain both spatial grid cells as well as non-spatial grid-like responses (Mok & Love, 2019; Rodríguez-Domínguez & Caplan, 2019; Stachenfeld et al., 2017; Wei et al., 2015). Similar to this memory model of grid cells, these models are also positioned to explain both the rodent spatial navigation and human memory literatures. Nevertheless, there is a key difference between this model and other grid cell models that generalize to non-spatial representations. Specifically, these other models assume that grid cells exhibiting spatial receptive fields serve the function of identifying positions in the environment (i.e., their function is spatial). As such, these models do not explain why most of the input to rodent hippocampus appears to be spatial (Boccara et al., 2010; Diehl et al., 2017; Grieves & Jeffery, 2017). This memory model of grid cells provides an answer to the apparent paucity of nonspatial cell types in rodent MTL by proposing that grid cells with spatial receptive fields have been misclassified as spatial (they are what cells rather than where cells) and that place cells are fundamentally memory cells that conjoin what and where.”

- The paper does not fully take into account all the findings regarding grid cells, some of which very clearly show spatial processing in this system. For example, findings on grid-bydirection cells (e.g., Sargolini et al. 2006) would seem to suggest that the entorhinal grid system is very specifically spatial and related to path integration. Why would grid-bydirection cells be present and intertwined with grid cells in the author's memory-related reconceptualization? It seems to me that the existence of grid-by-direction cells is strong evidence that at least part of this network is specifically spatial.

Head by direction grid cells were a key part of the reported results. These grid cells naturally arise in the model as the animal forms memories (aka, hippocampal place cells) that conjoin location (as defined by border cells), head direction at the time of memory formation, and one or more non-spatial properties found at that location. In this revision, I have attempted to better explain how including head direction in hippocampal memories naturally gives rise to these cell types. The introduction to the head direction module simulations now reads:

“According to this memory model of spatial navigation, place cells are the conjunction of location, as defined by border cells, and one or more properties that are remembered to exist at that location. Such memories could, for instance, allow an animal to remember the location of a food cache (Payne et al., 2021). The next set of simulations investigates behavior of the model when one of the to-be-remembered properties is head direction at the time when the memory was formed (e.g., the direction of a pathway leading to a food cache). Indicating that head direction is an important part of place cell representations, early work on place cells in mazes found strong sensitivity to head direction, such that the place field is found in one direction of travel but not the other (McNaughton et al., 1983; Muller et al., 1994). Place cells can exhibit a less extreme version of head direction sensitivity in open field recordings (Rubin et al., 2014), but the nature of the sensitivity is more complicated, depending on location of the animal relative to the place field center (Jercog et al., 2019).

It is possible that some place cell memories do not receive head direction input, as was the case for the simulations reported in Figures 6/7 – in those simulations, place cells were entirely insensitive to head direction, owing to a lack of input from head direction cells. However, removal of head direction input to hippocampus affects place cell responses (Calton et al., 2003) and grid cell responses (Winter et al., 2015), suggesting that head direction is a key component of the circuit. Furthermore, if place cells represent episodic memories, it seems natural that they should include head direction (i.e., viewpoint at the time of memory formation).

In the simulations reported next, head direction is simply another property that is conjoined in a hippocampal place cell memory. In this case, a head direction cell should become a head direction conjunctive grid cell (i.e., a grid cell, but only when the animal is heading in a particular direction), owing to memory feedback from the hexagonal array of hippocampal place cell memories. When including head direction, the real-world dimensions of variation are across three dimensions (X, Y, and head direction) rather than two, and consolidation will cause the place cells to arrange in a three-dimensional volume. The simulation reported below demonstrates that this situation provides a “grid module”.”

- I am also concerned that the paper does not do enough to address findings regarding how the elliptical shape of grid fields shifts when boundaries of an environment compress in one direction or change shape/angles (Lever et al., & Krupic et al). Those studies show compression in grid fields based on boundary position, and I don't see how the authors' model would explain these findings.  

This finding was covered in the original submission: “For instance, perhaps one egocentric/allocentric pair of mEC grid modules is based on head direction (viewpoint) in remembered positions relative to the enclosure borders whereas a different egocentric/allocentric pair is based on head direction in remembered positions relative to landmarks exterior to the enclosure. This might explain why a deformation of the enclosure (moving in one of the walls to form a rectangle rather than a square) caused some of the grid modules but not others to undergo a deformation of the grid pattern in response to the deformation of the enclosure wall (see also Barry et al., 2007). More specifically, if there is one set of non-orthogonal dimensions for enclosure borders and the movement of one wall is too modest as to cause avoid global remapping, this would deform the grid modules based the enclosure border cells. At the same time, if other grid modules are based on exterior properties (e.g., perhaps border cells in relation to the experimental room rather than the enclosure), then those grid modules would be unperturbed by moving the enclosure wall.”

I apologize for being unclear in describing how the model might explain this result. The paragraph has been rewritten and now reads:

“Consider the possibility that one mEC grid modules is based on head direction (viewpoint) in remembered positions relative to the enclosure borders (e.g., learning the properties of the enclosure, such as the metal surface) while a different grid module is based on head direction in remembered positions relative to landmarks exterior to the enclosure (e.g., learning the properties of the experimental room, such as the sound of electronics that the animal is subject to at all locations). This might explain why a deformation of the enclosure (moving one of the walls to form a rectangle rather than a square) caused some of the grid modules but not others to undergo a deformation of the grid pattern in response to the deformation of the enclosure wall (see also Barry et al., 2007). More specifically, suppose that the movement of one wall is modest and after moving the wall, the animal views the enclosure as being the same enclosure, albeit slightly modified (e.g., when a home is partially renovated, it is still considered the same home). In this case, the set of non-orthogonal dimensions associated with enclosure borders would still be associated with the now-changed borders and any memories in reference to this border-determined space would adjust their positions accordingly in real-world coordinates (i.e., the place cells would subtly shift their positions owing to this deformation of the borders, producing a corresponding deformation of the grid). At the same time, there may be other sets of memories that are in relation to dimensions exterior to the enclosure. Because these exterior properties are unchanged, any place cells and grid cells associated with the exterior-oriented memories would be unchanged by moving the enclosure wall.”

- Are findings regarding speed modulation of grid cells problematic for the paper's memory results? 

- A further issue is that the paper does not seem to adequately address developmental findings related to the timecourses of the emergence of different cell types. In their simulation, researchers demonstrate the immediate emergence of grid fields in a novel environment, while noting that the stabilization of place cell positions takes time. However, these simulation findings contradict previous empirical developmental studies (Langston et al., 2010). Those studies showed that head direction cells show the earliest development of spatial response, followed by the appearance of place cells at a similar developmental stage. In contrast, grid cells emerge later in this developmental sequence. The gradual improvement in spatial stability in firing patterns likely plays a crucial role in the developmental trajectory of grid cells. Contrary to the model simulation, grid cells emerge later than place cells and head direction cells, yet they also hold significance in spatial mapping. 

- The model simulations suggest that certain grid patterns are acquired more gradually than others. For instance, egocentric grid cells require the stabilization of place cell memories amidst ongoing consolidation, while allocentric grid cells tend to reflect average place field positions. However, these findings seemingly conflict with empirical studies, particularly those on the conjunctive representation of distance and direction in the earliest grid cells. Previous studies show no significant differences were found in grid cells and grid cells with directional correlates across these age groups, relative to adults (Wills et al., 2012). This indicates that the combined representation of distance and direction in single mEC cells is present from the earliest ages at which grid cells emerge. 

These are good points and they have been addressed in a new section of the introduction titled ‘The Scope of the Proposed Model’. That section reads:

“The reported simulations explain why most mEC cell types in the rodent literature appear to be spatial (Boccara et al., 2010; Diehl et al., 2017; Grieves & Jeffery, 2017). Assuming that rodents can form non-spatial memories, rodent hippocampus must receive non-spatial input from entorhinal cortex. These simulations suggest that characterization of the rodent mEC cortex as primarily spatial might be incorrect if most grid cells (except perhaps head direction conjunctive grid cells) have been mischaracterized as spatial. Other literatures with other species find non-spatial representations in MTL (Gulli et al., 2020; Quiroga et al., 2005; Wixted et al., 2014) and non-spatial hippocampal memory encoding has been found in rodents (Liu et al., 2012; McEchron & Disterhoft, 1999). The proposed memory model is compatible with these results – the ideas contained in this model could be applied to nonspatial memory representations. However, surveys of cell types in rodent entorhinal cortex seem to indicate that most cells are spatial (Boccara et al., 2010; Diehl et al., 2017; Grieves & Jeffery, 2017). How can the rodent hippocampus encode nonspatial memories if most of its input is spatial? The goal of the reported simulations is to explain the apparent paucity of non-spatial cells in rodent entorhinal cortex by proposing that grid cells have been misclassified as spatial (see also Luo et al., 2024).

Given the simplicity of the proposed model, there are important findings that the model cannot address -- it is not that the model makes the wrong predictions but rather that it makes no predictions. The role of running speed (Kraus et al., 2015) is one such variable for which the model makes no predictions. Similarly, because the model is a rate-coded model rather than a model of oscillating spiking neurons, it makes no predictions regarding theta oscillations (Buzsáki & Moser, 2013). The model is an account of learning and memory for an adult animal, and it makes no predictions regarding the developmental (Langston et al., 2010; Muessig et al., 2015; Wills et al., 2012) or evolutionary (Rodrıguez et al., 2002) time course of different cell types. This model contains several purely spatial representations such as border cells, head direction cells, and head direction conjunctive grid cells and it may be that these purely spatial cell types emerged first, followed by the evolution and/or development of non-spatial cell types. However, this does not invalidate the model. Instead, this is a model for an adult animal that has both episodic memory capabilities and spatial navigation capabilities, irrespective of the order in which these capabilities emerged.

This model has the potential to explain context effects in memory (Godden & Baddeley, 1975; Gulli et al., 2020; Howard et al., 2005). According to this model, different grid cells represent different non-spatial characteristics and place cells represent the combination of these “context” factors and location. In the simulation, just one grid cell is simulated but the same results would emerge when simulating hundreds of different non-spatial inputs provided that all of the simulated non-spatial inputs exist throughout the recording session. However, there is evidence that hippocampus can explicitly represent the passage of time (Eichenbaum, 2014), and time is assuredly an important factor in defining episodic memory (Bright et al., 2020). Thus, although the current model addresses unique combinations of what and where, it is left to future work to incorporate representations of when in the memory model.”

Reviewer #3 (Public Review): 

A crucial assumption of the model is that the content of experience must be constant in space. It's difficult to imagine a real-world example that satisfies this assumption. Odors and sounds are used as examples. While they are often more spatially diffuse than an objects on the ground, odors and sounds have sources that are readily detectable. Animals can easily navigate to a food source or to a vocalizing conspecific. This assumption is especially problematic because it predicts that all grid cells should become silent when their preferred non-spatial attribute (e.g. a specific odor) is missing. I'm not aware of any experimental data showing that grid cells become silent. On the contrary, grid cells are known to remain active across all contexts that have been tested, including across sleep/wake states. Unlike place cells, grid cells do not seem to turn off. Since grid cells are active in all contexts, their preferred attribute must also be present in all contexts, and therefore they would not convey any information about the specific content of an experience.  

These are good points and in this revision I have attempted to explain that there is a great deal of contextual similarity across all recording sessions. One paragraph in the discussion now reads

“In a typical rodent spatial navigation study, the non-spatial attributes are wellcontrolled, existing at all locations regardless of the enclosure used during testing (hence, a grid cell in one enclosure will be a grid cell in a different enclosure). Because labs adopt standard procedures, the surfaces, odors (e.g., from cleaning), external lighting, time of day, human handler, electronic apparatus, hunger/thirst state, etc. might be the same for all recording sessions. Additionally, the animal is not allowed to interact with other animals during recording and this isolation may be an unusual and highly salient property of all recording sessions. Notably, the animal is always attached to wires during recording. The internal state of the animal (fear, aloneness, the noise of electronics, etc.) is likely similar across all recording situations and attributes of this internal state are likely represented in the hippocampus and entorhinal input to hippocampus. According to this model, hippocampal place cells are “marking” all locations in the enclosure as places where these things tend to happen.”

The proposed novelty of this theory is that other models all assume that grid cells encode space. This isn't quite true of models based on continuous attractor networks, the discussion of which is notably absent. More specifically, these models focus on the importance of intrinsic dynamics within the entorhinal cortex in generating the grid pattern. While this firing pattern is aligned to space during navigation and therefore can be used as a representation of that space, the neural dynamics are preserved even during sleep. Similarly, it is because the grid pattern does not strictly encode physical space that gridlike signals are also observed in relation to other two-dimensional continuous variables. 

These models were briefly discussed in the general discussion section and in this revision they are further discussed in the introduction in a new section, titled ‘Why Model the Rodent Navigation Literature with a Memory Model?’ That section reads:

“Spatial navigation is inherently a memory problem – learning the spatial arrangement of a new enclosure requires memory for the conjunction of what and where. This has long been realized and in the introduction to ‘Hippocampus as a Cognitive Map’, O’Keefe and Nadel (1978) wrote “We shall argue that the hippocampus is the core of a neural memory system providing an objective spatial framework within which the items and events of an organism's experience are located and interrelated” (emphasis added). Furthermore, in the last chapter of their book, they extended cognitive map theory to human memory for non-spatial characteristics. However, in the decades since the development of cognitive map theory, the rodent spatial navigation and human memory literatures have progressed somewhat independently.

The ideas proposed in this model are an attempt to reunify these literatures by returning to the original claim that spatial navigation is inherently a memory problem. The goal of the current study is to explain the rodent spatial navigation literature using a memory model that has the potential to also explain the human memory literature. In contrast, most grid cell models (Bellmund et al., 2016; Bush et al., 2015; Castro & Aguiar, 2014; Hasselmo, 2009; Mhatre et al., 2012; Solstad et al., 2006; Sorscher et al., 2023; Stepanyuk, 2015; Widloski & Fiete, 2014) are domain specific models of spatial navigation and as such, they do not lend themselves to explanations of human memory. Thus, the reason to prefer this model is parsimony. Rather than needing to develop a theory of memory that is separate from a theory of spatial navigation, it might be possible to address both literatures with a unified account.

This study does not attempt to falsify other theories of grid cells. Instead, this model reaches a radically different interpretation regarding the function of grid cells; an interpretation that emerges from viewing spatial navigation as a memory problem. All other grid cell models assume that an entorhinal grid cell displaying a spatially arranged grid of firing fields serves the function of spatial coding (i.e., spatial grid cells exist to support a spatial metric). In contrast, the proposed memory model of grid cells assumes that the hexagonal tiling reflects the need to keep memories separate from each other to minimize confusion and confabulation – the grid pattern is the byproduct of pattern separation between memories rather than the basis of a spatial code. 

It is now understood that grid-like firing fields can occur for non-spatial two dimensional spaces. For instance, human entorhinal cortex exhibits grid-like responses to video morph trajectories in a two-dimensional bird neck-length versus bird leg-length space (Constantinescu et al., 2016). As a general theory of learning and memory, the proposed memory model of grid cells is easily extended to explain these results (e.g., relabeling the border cell inputs in the model as neck-length and leg-length inputs). However, there are other grid cell models that can explain both spatial grid cells as well as non-spatial grid-like responses (Mok & Love, 2019; Rodríguez-Domínguez & Caplan, 2019; Stachenfeld et al., 2017; Wei et al., 2015). Similar to this memory model of grid cells, these models are also positioned to explain both the rodent spatial navigation and human memory literatures. Nevertheless, there is a key difference between this model and other grid cell models that generalize to non-spatial representations. Specifically, these other models assume that grid cells exhibiting spatial receptive fields serve the function of identifying positions in the environment (i.e., their function is spatial). As such, these models do not explain why most of the input to rodent hippocampus appears to be spatial (Boccara et al., 2010; Diehl et al., 2017; Grieves & Jeffery, 2017). This memory model of grid cells provides an answer to the apparent paucity of nonspatial cell types in rodent MTL by proposing that grid cells with spatial receptive fields have been misclassified as spatial (they are what cells rather than where cells) and that place cells are fundamentally memory cells that conjoin what and where.”

The use of border cells or boundary vector cells as the main (or only) source of spatial information in the hippocampus is not well supported by experimental data. Border cells in the entorhinal cortex are not active in the center of an environment. Boundary-vector cells can fire farther away from the walls but are not found in the entorhinal cortex. They are located in the subiculum, a major output of the hippocampus. While the entorhinalhippocampal circuit is a loop, the route from boundary-vector cells to place cells is much less clear than from grid cells. Moreover, both border cells and boundary-vector cells (which are conflated in this paper) comprise a small population of neurons compared to grid cells.

AUTHOR RESPONSE: The model can be built without assuming between-border cells (early simulations with the model did not make this assumption). Regarding this issue, the text reads “Unlike the BVC model, the boundary cell representation is sparsely populated using a basis set of three cells for each of the three dimensions (i.e., 9 cells in total), such that for each of the three non-orthogonal orientations, one cell captures one border, another the opposite border, and the third cell captures positions between the opposing borders (Solstad et al., 2008). However, this is not a core assumption, and it is possible to configure the model with border cell configurations that contain two opponent border cells per dimension, without needing to assume that any cells prefer positions between the borders (with the current parameters, the model predicts there will be two border cells for each between-border cell). Similarly, it is possible to configure the model with more than 3 cells for each dimension (i.e., multiple cells representing positions between the borders).” The Solstad paper found a few cells that responded in positions between borders, but perhaps not as many as 1 out of 3 cells, such as this particular model simulation predicts. If the paucity of between-border cells is a crucial data point, the model can be reconfigured with opponent-border cells without any between border cells. The reason that 3 border cells were used rather than 2 opponent border cells was for simplicity. Because 3 head direction cells were used to capture the face-centered cubic packing of memories, the simulation also used 3 border cells per dimensions to allow a common linear sum metric when conjoining dimensions to form memories. If the border dimensions used 2 cells while head direction used 3 cells, a dimensional weighting scheme would be needed to allow this mixing of “apples and oranges” in terms of distances in the 3D space that includes head direction.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Specific questions/clarifications:  

(1) Assumption of population-based vs single unit link to biological cells: At the start, the author assumes that each unit here can be associated with a population: "the simulated activation values can be thought of as proportional to the average firing rate of an ensemble of neurons with similar inputs and outputs (O'Reilly & Munakata, 2000)." But is a 'grid cell' found here a single cell or an average of many cells? Does this mean the model assumes many cells that have different fields that are averaged, which become a grid-like unit in the model? But in biology, these are single cells? Or does it mean a grid response is an average of the place cell inputs? 

I apologize for being unclear about this. The grid cells in the model are equivalent to real single cells except that the simulation uses a ratecoded cell rather than a spiking cell. The averaging that was mentioned in the paper is across identically behaving spiking cells rather than across cells with different grid field arrangements. To better explain this, I have added the following text:

“For instance, consider a set of several thousand spiking grid cells that are identical in terms of their firing fields. At any moment, some of these identically-behaving cells will produce an action potential while others do not (i.e., the cells are not perfectly synchronized), but a snapshot of their behavior can be extracted by calculating average firing rate across the ensemble. The simulated cells in the model represent this average firing rate of identically-behaving ensembles of spiking neurons.” 

This is a mathematical short-cut to avoid simulating many spiking neurons. Because this model was compared to real spike rate maps, this real-valued average firing rate is down-sampled to produce spikes by finding the locations that produced the top 5% of real-valued activation values across the simulation.

(2) It is not clear to me why they are circular border cells/basis sets.  

In the initial submission, there was a brief paragraph describing this assumption. In this revision, that paragraph has been expanded and modified for greater clarity. It now reads:

“Because head direction is necessarily a circular dimension, it was assumed that all dimensions are circular (a circular dimension is approximately linear for nearby locations). This assumption of circular dimensions was made to keep the model relatively simple, making it easier to combine dimensions and allowing application of the same processes for all dimensions. For instance, the model requires a weight normalization process to ensure that the pattern of weights for each dimension corresponds to a possible input value along that dimension. However, the normalization for a linear dimension is necessarily different than for a circular dimension. Because the neural tuning functions were assumed to be sine waves, normalization requires that the sum of squared weights add up to a constant value. For a linear dimension, this sum of squares rule only applies to the subset of cells that are relevant to a particular value along the dimension whereas for a circular dimension, this sum of squares rule is over the entire set of cells that represent the dimension (i.e., weight normalization is easier to implement with circular dimensions). Although all dimensions were assumed to be circular for reasons of mathematical convenience and parsimony, circular dimensions may relate to the finding that human observers have difficultly re-orienting themselves in a room depending on the degree of rotational symmetry of the room (Kelly et al., 2008). In addition, this simplifying assumption allows the model to capture the finding that the population of grid cells lies on a torus (Gardner et al., 2022), although I note that the model was developed before this result was known.”

(3) Why is it 3 components? I realise that the number doesn't matter too much, but I believe more is better, so is it just for simplicity? 

In this revision, additional text has been added to explain this assumption: “To keep the model simple, the same number of cells was assumed for all dimensions and all dimensions were assumed to be circular (head direction is necessarily circular and because one dimension needed to be circular, all dimensions were assumed to be circular). Three cells per dimensions was chosen because this provides a sparse population code of each dimension, with few border cells responding between borders, with few border cells responding between borders, while allowing three separate phases of grid cells within a grid cell module (in the model, a grid cell module arises from combination of a third dimension, such as head direction, with the real-world X/Y dimensions defined by border cells).”

As a reminder, the text explaining the sparse coding of border cells reads: “However, this is not a core assumption, and it is possible to configure the model with border cell configurations that contain two opponent border cells per dimension, without needing to assume that any cells prefer positions between the borders (with the current parameters, the model predicts there will be two border cells for each between-border cell). Similarly, it is possible to configure the model with more than 3 cells for each dimension (i.e., multiple cells representing positions between the borders).”

The model can work with just two opponent cells or with more than three cells per basis set. In different simulations, I have explored these possibilities. Three was chosen because it is a convenient way to highlight the face-centered cubic packing of memories that tends to occur (FCP produces 3 alternating layers of hexagonally arranged firing fields). Thus, each of the three head direction cells captures a different layer of the FCP arrangement. A more realistic simulation might combine 6 different head direction cells tiling the head direction dimension with opponent border cells (just 2 cells for each border dimensions). Such a combination would produce responses at borders, but no responses between borders and, at the same time, the head direction cells would still reveal the FCP arrangement. However, it is not easy to find the right parameters for such a mix-and-match simulation in which different dimensions have different numbers of tuning functions (e.g., some dimensions having 2 cells while others have 3 or 6 and some dimensions being linear while others are circular). When all of the dimensions are of the same type, the simple sum that arises from multiplying the input by the weight values gives rise to Euclidean distance (see Figure 3B). With a mix-and-match model of different dimension-types, it should be possible to adjust the sum to nevertheless produce a monotonic function with Euclidean distance although I leave this to future work. To keep things simple, I assumed that all dimensions are of the same type (circular, with 3 cells per dimension).  

(4) Confusion due to the border cells/box was unclear to me. "If the period of the circular border cells was the same as the width of the box, then a memory pushed outside the box on one side would appear on the opposite side of the box, in which case the partial grid field on one side should match up with its remainder on the other side. This would entail complete confusion between opposite sides of the box, and the representation of the box would be a torus (donut-shaped) rather than a flat two-dimensional surface. To reduce confusion ..." Is this confusion of the model? Of the animal?  

This would be confusion of the animal (e.g., a memory field overlapping with one border would also appear at the opposite border in the corresponding location). At one point in model development, I made the assumption that one side of the box wraps to the other side, and I asked Trygve Solstad to run some analyses of real data to see if cells actually wrap around in this manner. He did not find any evidence of this, and so I decided to include outsidethe-box representational area which, as it turned out, allowed the model to capture other behaviors as detailed in the paper.

This section of the paper now reads:

“The cosine tuning curves of the simulated border cells represent distance from the border on both sides of the border (i.e., firing rate increases as the animal approaches the border from either the inside or the outside of the enclosure). Experimental procedures do not allow the animal to experience locations immediately outside the enclosure, but these locations remain an important part of the hypothetic representation, particularly when considering the modification of memories through consolidation (i.e., a memory created inside the enclosure might be moved to a location outside the enclosure). This symmetry about the border cell’s preferred location is needed to maintain an unbiased representation, with a constant sum of squares for the border cell inputs (see methods section). Rather than using linear dimensions, all dimensions were assumed to be circular to keep the model relatively simple. This assumption was made because head direction is necessarily a circular dimension and by having all dimensions be circular, it is easy to combine dimensions in a consistent manner to produce multidimensional hippocampal place cell memories. Thus, the border cells define a torus (or more accurately a three-torus) of possible locations. This provides a hypothetical space of locations that could be represented.

In light of the assumption to represent border cells with a circular dimension, when a memory is pushed outside the East wall of the enclosure, it would necessarily be moved to the West wall of the enclosure if the period of the circular dimension was equal to the width of the enclosure. If this were true, then the partial grid field on one side of the enclosure would match up with its remainder on the other side. Such a situation would cause the animal to become completely confused regarding opposite sides of the enclosure (a location on the West wall would be indistinguishable from the corresponding location on the East wall). To reduce confusion between opposite sides of the enclosure, the width of the enclosure in which the animal navigated (Figure 5) was assumed to be half as wide as the full period of the border cells. In other words, although the space of possible representations was a three-torus, it was assumed that the real-world twodimensional enclosure encompassed a section of the torus (e.g., a square piece of tape stuck onto the surface of a donut). The torus is better thought of as “playing field” in which different sizes and shapes of enclosure can be represented (i.e., different sizes and shapes of tape placed on the donut). Furthermore, this assumption provides representational space that is outside the box without such locations wrapping around to the opposite side of the box.”

(5) Figure 3 - This result seems to be related to whether you use Euclidean or city-block distance. If you use Euclidean distances in two dimensions wouldn't this work out fine?  

Euclidean distance was the metric used in the analysis of the two-dimensional simulation, but this did not work out. To make this clear, I have changed the label on the x-axes to read “Euclidean distance” for both the two- and three-dimensional simulations. The two-dimensional simulation produced city block behavior rather than Euclidean behavior because memory retrieval is the sum of the two dimensions, as is standard in neural networks, rather than the Euclidian distance formula, which would require that memory retrieval be the square root of the sum of squares of the two dimensions. One way to address this problem with the two-dimensional simulation would be to use a specific Euclidean-mimicking activation function rather than a simple sum of dimensions. The very first model I developed used such an activation function as applied to opponent border cells with just two dimensions (so 4 cells in total – left/right and top/down). This produced Euclidean behavior, but the activation function was implausible and did not generalize to simulations that also included head direction. In contrast, with three non-orthogonal dimensions, the simple sum of dimensions is approximately Euclidean.

(6) Final sentence of the Discussion: "However, unlike the present model, these models still assume that entorhinal grid cells represent space rather than a non-spatial attribute." I am not sure if the authors of the cited papers will agree with this. They consider the spatial cases, but most argue they can treat non-spatial features as well. What the author might mean is that they assume non-spatial features are in some metric space that, in a way, is spatial. However, I am not sure if the author would argue that non-spatial features cannot be encoded metrically (e.g., Euclidean distance based on the similarity of odours). 

In this section, when referring to “entorhinal grid cells” I was specifically referring to traditional grid cells in a rodent spatial navigation experiment. I did not mean to imply that these other theories cannot explain nonspatial grid fields, such as in the two-dimensional bird space grid cells found with humans. The way in which the proposed memory model and these other models differ is in terms of what they assume regarding the function of grid cells that exhibit spatial grid fields. In this revision, I have changed this text to read:

“These models can capture some of the grid cell results presented in the current simulations, including extension to non-spatial grid-like responses (e.g., grid field that cover a two-dimensional neck/leg length bird space). Furthermore, these models may be able to explain memory phenomena similar to the model proposed in this study. However, unlike the proposed model, these models assume that the function of entorhinal grid cells that exhibit spatial X/Y grid fields during navigation is to represent space. In contrast, the memory model proposed in this study assume that the function of spatial X/Y grid cells is to represent a non-spatial attribute; the only reason they exhibit a spatial X/Y grid is because memories of that non-spatial attribute are arranged in a hexagonal grid owing to the uncluttered/unvarying nature of the enclosure. Thus, these model do not explain why most of the input to rodent hippocampus appears to be spatial (Boccara et al., 2010b; Diehl et al., 2017; Grieves & Jeffery, 2017) whereas the proposed model can explain this situation as reflecting the miss-classification of grid cells with a spatial arrangement as providing spatial input to hippocampus.”

(7) It would be interesting to see videos/gifs of the model learning, and an idea of how many steps of trials it takes (is it capturing real-time rodent cell firing whilst foraging, or is it more abstracted, taking more trials). 

The short answer is “yes”, the model is capturing real-time rodent cell firing while foraging. This is particularly true when simulating place cell memories in the absence of head direction information, as was shown in a video provided in the initial submission in relation to Figure 4. In this revision, I have provided a second video of learning when simulating place cell memories that include head direction. This second video is in relation to the results reported in Figure 9. This shows that even when learning a three-dimensional real-world space (X, Y, and head direction), the model rapidly produces an on-average hexagonal arrangement of place cells memories owing to the slight tendency of the place cell memories to linger in some locations as compared to others during consolidation. More specifically, they are more likely to linger in the locations that are the intersections of the peaks and/or troughs of the border cells and it is this tendency that supports the immediate appearance of grid cells. However, because the place cell memories are still shifting, head direction conjunctive grid cells are slower to emerge (the head direction conjunctive grid cells require stabilization of the place cells). The video then speeds up the learning process to so how place cells eventually stabilize after sufficient learning of the borders of the enclosure from different head/view directions.

(8) One question is whether all the results have to be presented in the main text. It was difficult to see which key predictions fit the data and do so better than a spatial/navigation account. 

Thank you for this suggestion. To make the paper more readable and easier for different readers with different interests to choose different aspects of the results to read, the second half of the results have been put in an appendix. More specifically, the second half of the results concerned place cells rather than grid cells. Thus, in this revision, the main text concerns grid cell results and the appendix concerns place cell results.

Reviewer #3 (Recommendations For The Authors):  

The title could usefully be shortened to focus on the main argument that observed firing patterns could be consistent with mapping memories instead of space. It's a stretch to argue that memory is the primary role when no such data is presented (i.e., there is no comparison of competing models). 

This is a good point (I do not present evidence that conclusively indicates the function of MTL). This original title was chosen to make clear how this account is a radical departure from other accounts of grid cells. The revised title highlights that: 1) a memory model can also explain rodent single cell recording data during navigation; and 2) grid cell may not be non-spatial. The revised title is: “A Memory Model of Rodent Spatial Navigation: Place Cells are Memories Arranged in a Grid and Grid Cells are Non-spatial”

When arguing that the main role of the hippocampus is memory, I strongly suggest engaging with the work of people like Howard Eichenbaum who spent the better part of their career arguing the same (e.g. DOI:10.1152/jn.00005.2017.)  

Thank you for pointing out this important oversight. Early in introduction, I now write: “The proposal that hippocampus represents the multimodal conjunctions that define an episode is not new (Marr et al., 1991; Sutherland & Rudy, 1989) and neither is the proposal that hippocampal memory supports spatial/navigation ability (Eichenbaum, 2017). This view of the hippocampus is consistent with “feature in place” results (O’Keefe & Krupic, 2021) in which hippocampal cells respond to the conjunction of a non-spatial attribute affixed to a specific location, rather than responding more generically to any instance of a non-spatial attribute. In other words, the what/where conjunction is unique. Furthermore, the uniqueness of the what/where conjunction may be the fundamental building block of spatial memory and navigation. In reviewing the hippocampal literature, Howard Eichenbaum (2017) concludes that ‘the hippocampal system is not dedicated to spatial cognition and navigation, but organizes experiences in memory, for which spatial mapping and navigation are both a metaphor for and a prominent application of relational memory organization.’”

With a focus on episodic memory, there should be a mention of the temporal component of memory. While it may rightfully be beyond the scope of this model, it's confusing to omit time completely from the discussion. 

This issue and several others are now addressed in a new section in the introduction titled ‘The Scope of the Proposed Model’. That section reads:

“The reported simulations explain why most mEC cell types in the rodent literature appear to be spatial (Boccara et al., 2010; Diehl et al., 2017; Grieves & Jeffery, 2017). Assuming that rodents can form non-spatial memories, rodent hippocampus must receive non-spatial input from entorhinal cortex. These simulations suggest that characterization of the rodent mEC cortex as primarily spatial might be incorrect if most grid cells (except perhaps head direction conjunctive grid cells) have been mischaracterized as spatial. Other literatures with other species find non-spatial representations in MTL (Gulli et al., 2020; Quiroga et al., 2005; Wixted et al., 2014) and non-spatial hippocampal memory encoding has been found in rodents (Liu et al., 2012; McEchron & Disterhoft, 1999). The proposed memory model is compatible with these results – the ideas contained in this model could be applied to nonspatial memory representations. However, surveys of cell types in rodent entorhinal cortex seem to indicate that most cells are spatial (Boccara et al., 2010; Diehl et al., 2017; Grieves & Jeffery, 2017). How can the rodent hippocampus encode nonspatial memories if most of its input is spatial? The goal of the reported simulations is to explain the apparent paucity of non-spatial cells in rodent entorhinal cortex by proposing that grid cells have been misclassified as spatial (see also Luo et al., 2024).

Given the simplicity of the proposed model, there are important findings that the model cannot address -- it is not that the model makes the wrong predictions but rather that it makes no predictions. The role of running speed (Kraus et al., 2015) is one such variable for which the model makes no predictions. Similarly, because the model is a rate-coded model rather than a model of oscillating spiking neurons, it makes no predictions regarding theta oscillations (Buzsáki & Moser, 2013). The model is an account of learning and memory for an adult animal, and it makes no predictions regarding the developmental (Langston et al., 2010; Muessig et al., 2015; Wills et al., 2012) or evolutionary (Rodrıguez et al., 2002) time course of different cell types. This model contains several purely spatial representations such as border cells, head direction cells, and head direction conjunctive grid cells and it may be that these purely spatial cell types emerged first, followed by the evolution and/or development of non-spatial cell types. However, this does not invalidate the model. Instead, this is a model for an adult animal that has both episodic memory capabilities and spatial navigation capabilities, irrespective of the order in which these capabilities emerged.

This model has the potential to explain context effects in memory (Godden & Baddeley, 1975; Gulli et al., 2020; Howard et al., 2005). According to this model, different grid cells represent different non-spatial characteristics and place cells represent the combination of these “context” factors and location. In the simulation, just one grid cell is simulated but the same results would emerge when simulating hundreds of different non-spatial inputs provided that all of the simulated non-spatial inputs exist throughout the recording session. However, there is evidence that hippocampus can explicitly represent the passage of time (Eichenbaum, 2014), and time is assuredly an important factor in defining episodic memory (Bright et al., 2020). Thus, although the current model addresses unique combinations of what and where, it is left to future work to incorporate representations of when in the memory model.”

I recommend explaining the motivation of the theory in more detail in the introduction. It reads as "what if it's like this?" It would be helpful to instead highlight the limitations of current theories and argue why this theory is either a better fit for the data or is logically simpler. 

This issue and several others are now addressed in the new section in the introduction titled ‘Why Model the Rodent Navigation Literature with a Memory Model?’, which I quoted above in response to the public reviews.

It's worth considering shortening the results section to include only those that most convincingly support the main claim. The manuscript is quite long and appears to lack focus at times. 

Thank you for this suggestion. To make the paper more readable and easier for different readers with different interests to choose different aspects of the results to read, the second half of the results have been put in an appendix. More specifically, the second half of the results concerned place cells rather than grid cells. Thus, in this revision, the main text concerns grid cell results and the appendix concerns place cell results.

The discussion of path dependence on the formation of the grid pattern is important but only briefly discussed. It may be useful to add simulations testing whether different paths (not random walks) produce distorted grid patterns. 

The short answer is that the path doesn’t affect things in general. The consolidation rule ensures equally spaced memories even if, for instance, one side of the enclosure is explored much more than the other side. As just one example, I have run simulations with a radial arm maze and even though the animal is constrained to only run on the maze arms. The memories still arrange hexagonally as memories become pushed outside the arms. Rather than adding additional simulations to study, I now briefly describe this in the model methods:

“Of note, the ability of the model to produce grid cell responses does not depend on this decision to simulate an animal taking a random walk – the same results emerge if the animal is more systematic in its path. All that matters for producing grid cell responses is that the animal visits all locations and that the animal takes on different head directions for the same location in the case of simulations that also include head direction as an input to hippocampal place cells.”

I struggle to understand in Figure 3 why retrieval strength ought to scale monotonically with Euclidean distance, and why that justifies a more complex model (three non-orthogonal dimensions). 

The introduction to this section now reads: “Animals can plan novel straight line paths to reach a known position and evidence suggests they do so by learning Euclidean representations of space (Cheng & Gallistel, 2014; Normand & Boesch, 2009; Wilkie, 1989). Thus, it was assumed that hippocampal place cells represent positions in Euclidean space (as opposed to non-Euclidean space, such a occurs with a city-block metric).”

p.17 "although the representational space is a torus (or more specifically a three-torus), it is assumed that the real-world two-dimensional surface is only a section of the torus (e.g., a square piece of tape stuck onto the surface of a donut)." I fail to understand how the realworld surface is only a part of the torus. In the existing theoretical and experimental work on toroidal topology of grid cell activity, the torus represents a very small fraction of the real world, and repeating activity on the toroidal manifold is a crucial feature of how it maps 2D space in a regular manner. Why then here do you want the torus to be larger than the realworld? 

This section has been rewritten to better explain these assumptions. The relevant paragraphs now read:

“The cosine tuning curves of the simulated border cells represent distance from the border on both sides of the border (i.e., firing rate increases as the animal approaches the border from either the inside or the outside of the enclosure). Experimental procedures do not allow the animal to experience locations immediately outside the enclosure, but these locations remain an important part of the hypothetic representation, particularly when considering the modification of memories through consolidation (i.e., a memory created inside the enclosure might be moved to a location outside the enclosure). This symmetry about the border cell’s preferred location is needed to maintain an unbiased representation, with a constant sum of squares for the border cell inputs (see methods section). Rather than using linear dimensions, all dimensions were assumed to be circular to keep the model relatively simple. This assumption was made because head direction is necessarily a circular dimension and by having all dimensions be circular, it is easy to combine dimensions in a consistent manner to produce multidimensional hippocampal place cell memories. Thus, the border cells define a torus (or more accurately a three-torus) of possible locations. This provides a hypothetical space of locations that could be represented.

In light of the assumption to represent border cells with a circular dimension, when a memory is pushed outside the East wall of the enclosure, it would necessarily be moved to the West wall of the enclosure if the period of the circular dimension was equal to the width of the enclosure. If this were true, then the partial grid field on one side of the enclosure would match up with its remainder on the other side. Such a situation would cause the animal to become completely confused regarding opposite sides of the enclosure (a location on the West wall would be indistinguishable from the corresponding location on the East wall). To reduce confusion between opposite sides of the enclosure, the width of the enclosure in which the animal navigated (Figure 5) was assumed to be half as wide as the full period of the border cells. In other words, although the space of possible representations was a three-torus, it was assumed that the real-world twodimensional enclosure encompassed a section of the torus (e.g., a square piece of tape stuck onto the surface of a donut). The torus is better thought of as “playing field” in which different sizes and shapes of enclosure can be represented (i.e., different sizes and shapes of tape placed on the donut). Furthermore, this assumption provides representational space that is outside the box without such locations wrapping around to the opposite side of the box.”

p.28 "More specifically, egocentric grid cells (e.g., head direction conjunctive grid cells) require stabilization of the place cell memories in the face of ongoing consolidation whereas allocentric grid cells reflect on-average place field positions." and p.32 "if place cells represent episodic memories, it seems natural that they should include head direction (an egocentric viewpoint)." But the head direction signal is not egocentric, it is allocentric. I'm unsure whether this is a typo or a potentially more serious conceptual misunderstanding. 

Any reference to egocentric has been removed in this revision. In the initial submission, when I used egocentric, I was referring to memories that depended on the head direction of the animal at the time of memory formation. I was using “egocentric” in relation to whether the memory was related to the animal’s personal bodily experience at the time of memory formation. But I concede that this is confusing since the ego/allo distinction is typically used to differentiate angular directions that are relative to the person (left/right) versus earth (East/West). Instead, throughout the manuscript I now refer to these as view-dependent memories since head direction would entail having a different view of the environment at the time of memory formation. I still refer to the stacking of multiple view-dependent memories on the same X/Y location as being the development of an allocentric representation however, since this can be thought of as one way to learn a cognitive map of the enclosure that is view independent.

p.37 "But if the border cells had changed their alignment with the new enclosure (e.g., if the E border dimension aligned with the North-South borders), then the place cells would have appeared to undergo global remapping as their positions rotated by 90 degrees and the grid pattern would have also rotated." But this would not be interpreted as global remapping by standard analyses of place and grid cell responses. A coherent rotation of firing patterns is not interpreted as remapping. 

This sentence now reads: “But if the border cells had changed their alignment with the new enclosure (e.g., if the E border dimension aligned with the North-South borders), then the place cells would remain in their same positions relative to the now-rotated borders (i.e., no remapping relative to the enclosure) and the corresponding grid cells would also retain their same alignment relative to the enclosure.”

p.37 "this is more accurately described as partial remapping (nearly all place fields were unaffected)." If nearly all place fields were unaffected, this should be interpreted as a stable map. Partial remapping is a mix of stability, rate remapping, and global remapping within a population of place cells. 

This sentence has been removed.

p.40 "The dependence of grid cell responses on memory may help explain why grid cells have been found for bats crawling on a two-dimensional surface (Yartsev et al., 2011), but three-dimensional grid cells have never been observed for flying bats." This is not true. Ginosar et al. (2021) observed 3D grid cells in flying bats.  

Thank you for highlighting this issue. In the initial submission I was using “grid cell” to mean a cell that produced a precise hexagonal grid, which is not the case for the 3D grid cells in bats. In this revision, I now discuss grid cell that produce irregular grid fields, writing:

“According to this model, hexagonally arranged grid cells should be the exception rather than the rule when considering more naturalistic environments. In a more ecologically valid situation, such as with landmarks, varied sounds, food sources, threats, and interactions with conspecifics, there may still be remembered locations were events occurred or remembered properties can be found, but because the non-spatial properties are non-uniform in the environment, the arrangement of memory feedback will be irregular, reflecting the varied nature of the environment. This may explain the finding that even in a situation where there are regular hexagonal grid cells, there are often irregular non-grid cells that have a reliable multi-location firing field, but the arrangement of the firing fields is irregular (Diehl et al., 2017). For instance, even when navigating in an enclosure that has uniform properties as dictated by experimental procedures, they may be other properties that were not well-controlled (e.g., a view of exterior lighting in some locations but not others), and these uncontrolled properties may produce an irregular grid (i.e., because the uncontrolled properties are reliably associated with some locations but not others, hippocampal memory feedback triggers retrieval of those properties in the associations locations).

In this memory model, there are other situations in which an irregular but reliable multi-location grid may occur, even when everything is well controlled. In the reported simulations, when the hippocampal place cells were based on variation in X/Y (as defined by Border cells), nothing else changed as a function of location, and the model rapidly produced a precise hexagonal arrangement of hippocampal place cell memories. When head direction was included (i.e., real-world variation in X, Y, and head direction), the model still produced a hexagonal arrangement as per face centered cubic packing of memories, but this precise arrangement was slower to emerge, with place cells continuing to shift their positions until the borders of the enclosure were sufficiently well learned from multiple viewpoints. If there is realworld variation in four or more dimensions, as is likely the case in a more ecologically valid situation, it will be even harder for place cell memories to settle on a precise regular lattice. Furthermore, in the case of four dimensions, mathematicians studying the “sphere packing problem” recently concluded that densest packing is irregular (Campos et al., 2023). This may explain why the multifield grid cells for freely flying bats have a systematic minimum distance between firing fields, but their arrangement is globally irregular (Ginosar et al., 2021). Assuming that the memories encoded by a bat include not just the three realworld dimensions of variation, but also head direction, the grid will likely be irregular even under optimal conditions of laboratory control.”

Multiple typos are found on page 25, end of paragraph 3: "More specifically, if there is one set of non-orthogonal dimensions for enclosure borders and the movement of one wall is too modest as to cause avoid global remapping, this would deform the grid modules based the enclosure border cells."

As detailed above in the response the public reviews, this paragraph has been rewritten.

Author Response:

Reviewer #1 (Public Review):

Summary:

The study by Gupta et al. investigates the role of mast cells (MCs) in tuberculosis (TB) by examining their accumulation in the lungs of M. tuberculosis-infected individuals, non-human primates, and mice. The authors suggest that MCs expressing chymase and tryptase contribute to the pathology of TB and influence bacterial burden, with MC-deficient mice showing reduced lung bacterial load and pathology.

Strengths:

(1) The study addresses an important and novel topic, exploring the potential role of mast cells in TB pathology.

(2) It incorporates data from multiple models, including human, non-human primates, and mice, providing a broad perspective on MC involvement in TB.

(3) The finding that MC-deficient mice exhibit reduced lung bacterial burden is an interesting and potentially significant observation.

Weaknesses:

(1) The evidence is inconsistent across models, leading to divergent conclusions that weaken the overall impact of the study.

The strength of the study is the use of multiple models including mouse, non-human primate as well as human samples. The conclusions have now been refined to reflect the complexity of the disease and the use of multiple models.

(2) Key claims, such as MC-mediated cytokine responses and conversion of MC subtypes in granulomas, are not well-supported by the data presented.

To address the reviewer’s comments, we will carry out further experimentation to strengthen the link between MC subtypes and cytokine responses.

(3) Several figures are either contradictory or lack clarity, and important discrepancies, such as the differences between mouse and human data, are not adequately discussed.

We will further clarify the figures and streamline the discussions between the different models used in the study.

(4) Certain data and conclusions require further clarification or supporting evidence to be fully convincing.

We will either provide clarification or supporting evidence for some of the key conclusions in the paper.

Reviewer #2 (Public review):

Summary:

The submitted manuscript aims to characterize the role of mast cells in TB granuloma. The manuscript reports heterogeneity in mast cell populations present within the granulomas of tuberculosis patients. With the help of previously published scRNAseq data, the authors identify transcriptional signatures associated with distinct subpopulations.

Strengths:

(1) The authors have carried out a sufficient literature review to establish the background and significance of their study.

(2) The manuscript utilizes a mast cell-deficient mouse model, which demonstrates improved lung pathology during Mtb infection, suggesting mast cells as a potential novel target for developing host-directed therapies (HDT) against tuberculosis.

Weaknesses:

(1) The manuscript requires significant improvement, particularly in the clarity of the experimental design, as well as in the interpretation and discussion of the results. Enhanced focus on these areas will provide better coherence and understanding for the readers.

The strength of the study is the use of multiple models including mouse, non-human primate as well as human samples. The conclusions have now been refined to reflect the complexity of the disease and the use of multiple models.

(2) Throughout the manuscript, the authors have mislabelled the legends for WT B6 mice and mast cell-deficient mice. As a result, the discussion and claims made in relation to the data do not align with the corresponding graphs (Figure 1B, 3, 4, and S2). This discrepancy undermines the accuracy of the conclusions drawn from the results.

We apologize for the discrepancy which will be corrected in the revised manuscript

(3) The results discussed in the paper do not add a significant novel aspect to the field of tuberculosis, as the majority of the results discussed in Figure 1-2 are already known and are a re-validation of previous literature.

This is the first study which has used mouse, NHP and human TB samples from Mtb infection to characterize and validate the role of MC in TB. We believe the current study provides significant novel insights into the role of MC in TB.

(4) The claims made in the manuscript are only partially supported by the presented data. Additional extensive experiments are necessary to strengthen the findings and enhance the overall scientific contribution of the work.

We will either provide clarification or supporting evidence for some of the key conclusions in the paper.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, BOUTRY et al examined a cnidarian Hydra model system where spontaneous tumors manifest in laboratory settings, and lineages featuring vertically transmitted neoplastic cells (via host budding) have been sustained for over 15 years. They observed that hydras harboring long-term transmissible tumors exhibit an unexpected augmentation in tentacle count. In addition, the presence of extra tentacles, enhancing the host's foraging efficiency, correlated with an elevated budding rate, thereby promoting tumor transmission vertically. This study provided evidence that tumors, akin to parasitic entities, can also exert control over their hosts.<br /> Strengths:

The manuscript is well-written, and the phenotype is intriguing.

Weaknesses:

The quality of this manuscript could be improved if more evidence were to be provided regarding the beneficial versus detrimental effects of the tumors.

We thank the reviewer for taking the time to examine our work carefully and for their highly relevant comments and precise suggestions. We have incorporated these suggestions, which greatly improved the clarity of our manuscript concerning the beneficial and detrimental effects of tumors. Specifically, we have added a new analysis and rephrased the results section, as well as the corresponding sentences in the discussion, to enhance clarity.

Additionally, regarding the impact of tumor size on the development of supernumerary tentacles, we have included as suggested a new analysis that was previously only available in the supplementary materials of the earlier version. This addresses the reviewer's question and significantly enhances the quality of our paper.

We have thanked the two referees in the Acknowledgements section of our article.

Reviewer #2 (Public Review):

Background and Summary:

This study addresses the intriguing question of whether and how tumors can develop in the freshwater polyp hydra and how they influence the fitness of the animals. Hydra is notable for its significant morphogenetic plasticity and nearly unlimited capacity for regeneration. While its growth through asexual reproduction (budding) and the associated processes of pattern formation have been extensively studied at the cellular level, the occurrence of tumors was only recently described in two strains of Hydra oligactis (Domazet-Lošo et al, 2014). In that research, an arrest in the differentiation of female germ cells led to an accumulation of germline cells that failed to develop into eggs. In hydra, fertile egg cells typically incorporate nurse cells, which originate from large interstitial stem cells (ISCs) restricted to the germline, through apoptosis. However, this increase in apoptosis activity is absent in "germline tumors," and germline ISCs instead form slowly growing patches that do not compromise tissue integrity. Despite the upregulation of certain genes associated with mammalian neoplasms (such as tpt1 and p23) in this tissue, determining whether this differentiation arrest and the resulting egg patches truly constitute neoplasms remains a challenge.

The authors have recently published two papers on the ecological and evolutionary aspects of hydra tumor formation (Boutry et al 2022, 2023), which is also the focus of this manuscript. They transplanted tissues derived from animals with germline tumors to wildtype animals and analyzed their growth patterns, specifically the number of tentacles in the host tissue. They observed that such tissues induced the growth of additional tentacles compared to tissues without germline tumors. The authors conclude that this growth pattern (increased number of tentacles) is correlated with "reducing the burden on the host by (over-)compensating for the reproductive costs of tumors" and claim that "transmissible tumors in hydra have evolved strategies to manipulate the phenotype of their host". While it might be stimulating to add a fresh view from other disciplines (here, ecological and evolutionary aspects), the authors completely ignore the current knowledge of the underlying cell biology of the processes they analyze.

Strengths:

The study focuses on intriguing questions. Whether and how tumors can develop in the freshwater polyp hydra, and how they influence the fitness of the animals?

Weaknesses:

Concept of germline tumors.

The conceptual foundation of their experiments on germline tumors was the study of Domazet-Lošo et al (2014) introducing the concept of germline tumors in hydra (see above). While this is an intriguing hypothesis, there has been little advancement in comprehending the molecular mechanisms underlying tumor formation in hydra beyond this initial investigation. Germline tumors in hydra do not fully meet the typical criteria for neoplasms observed in mammalian tissues. More importantly, a similar phenotype was already reported by the work of Paul Brien and described as "crise gametique" (Brien, 1966, Biologie de la reproduction animale - Blastogenèse, Gamétogenèse, Sexualisation, ed. Masson & Cie, Paris). This phenomenon of gametic crisis is unique to Hydra oligactis, a stenotherm, cold-adapted cosmopolitan species. In this species, gametogenesis severely impacts the vitality of the polyps, often leading to complete exhaustion and death (Tardent, 1974). Animals can only be rescued during the initial phase of the cold-induced sexual period (see also the research of Littlefield (1984, 1985, 1986, 1991). The observed arrest in differentiation arrest in germline tumors might represent an epigenetically established consequence of surviving gametogenesis. Regrettably, this important work was not mentioned by the authors or by Domazet-Lošo et al. (2014), highlighting a notable gap in the recognition of basic research in this area that might challenge the hydra tumor hypothesis.

"Super-nummary" tentacles in graft experiments.

The authors describe that after grafting tissue from animals with germline tumors to wild-type animals, the number of tentacles in the host tissue increased when the donor tissue had germline tumors. A maximum effect of four additional tentacles was found with donor strain H. oligactis robusta and three additional tentacles with donor strain H.oligactis St Petersburg. In general, H.oligactis wild-type host strains had fewer tentacles than H.oligactis St Petersburg strains. This is consistent with the results of Domazet-Lošo et al (2014) who showed that the number of tentacles increased in the strains with germline tumors. What conclusions can be drawn from these experiments? 

The authors might want to conclude that transmissible tumors in Hydra have developed strategies to manipulate the phenotype of their host. But there is no evidence for this, as essential controls are missing. It is known that the size of hydra polyps is proportion-regulated, i.e. the number of tentacles varies with the size and number of (epithelial) cells. Such controls are missing in the experiments. There is also a lack of controls from wild-type animals in gametogenesis: it is very likely that grafts with wild-type animals with egg spots of comparable size as the germline tumors (see above) will result in similar numbers of tentacles in host tissue.

We thank the reviewer for their thoughtful comments. While we appreciate the concerns raised, we maintain that the evidence provided by Domazet-Lošo et al. (2014, Nature Communications) supports the relevance of this model, including the suggested comparisons with the expression profiles of individuals undergoing induced sexual reproduction. Our study focuses primarily on the impact of these tumors on the host phenotype rather than their origin. Tumors are defined as accumulations of abnormally proliferating cells. This includes the definition provided by the referee, which describes “apoptosis activity as absent in 'germline tumors,' with germline ISCs forming slowly growing patches.” Compromise of tissue integrity is not a criterion for defining neoplasms, and many benign neoplasms do not meet this criterion. We are interested in continuing this discussion with the referee to better understand the expected evidence and agree that histological nomenclature could be improved. While further investigation into the cell biology of these tumors would be valuable, this is currently beyond the scope of our article but is being pursued in separate research.

We also appreciate the points raised regarding the definition of germline tumors and the reference to the pioneering work of Paul Brien. However, in that publication, the concept of gametic crisis in H. oligactis describes reproductive exhaustion leading to death, rather than abnormal cell proliferation indicative of a tumor-like phenotype. This distinction likely explains why this specific paper was not cited previously.

Our study builds on prior research using the same model (e.g., Domazet-Lošo et al. 2014; Boutry et al. 2023) and describes observations across different hydra strains from various locations worldwide (not just two), all conducted under stable warm temperatures that are not conducive to sexual development. These investigations reveal a phenomenon distinct from the senescence observed post-reproduction in H. oligactis. The phenotype we describe, characterized by an accumulation of cells in the ectoderm, aligns with studies referenced by the reviewer from leading groups in hydra research, known for their expertise in hydra cellular biology. We have relied on these studies after carefully reviewing their results and receiving training from these experts. Furthermore, our team is focused on eco-evolutionary topics and does not aim to specialize in cellular biology, as other teams are already dedicated to that field.

We also thank the reviewer for their comments on the relevance of our findings and the missing controls. However, we have noted that the reviewer may have misunderstood our experimental design and results.

Firstly, it appears that the reviewer based their critique mainly on the initial sentences of our Results section (illustrated in Figure 2), which outline the donor groups used in our study rather than presenting the results of the grafting experiments. This description alone is insufficient for drawing conclusions, which is why we conducted further analyses using these donor groups grafted onto different recipients. The maximum effects mentioned by the reviewer (+10 tentacles with St. Petersburg tumoral tissue and +8 tentacles with Robusta tumoral tissue, Results Section 2) represent only a part of our study. We encourage the reviewer to focus on the model analyses presented in Results Section 2, which directly relate to the grafting experiments and provide a more comprehensive evaluation of our results and conclusions. These analyses include comparisons between transmissible tumors and spontaneous tumors, offering deeper insights into their effects on tentacle development.

In our methods (as depicted in Figure 3), we explicitly compared different types of tumorous tissue from various donors, distinguishing between spontaneous and transmissible tumors. Although we avoid labeling spontaneous tumors as "controls" to prevent confusion with healthy tissue controls, they serve as controls to the “treatment” that involves transmissible tumors, and thus are appropriate comparisons for assessing the size effect suggested by the reviewer. Spontaneous and transmissible tumors share similar size and cellular characteristics but differ significantly in the number of tentacles their hosts possess. Furthermore, we refer the reviewer to a relevant study (Ngo et al. 2021) that found no increase in tentacle numbers with larger polyps of healthy tissue. This reference has been included in the revised discussion (line 309 to 312), which now also addresses the potential effect of body size with additional explanations.

Regarding the suggestion to include controls from animals undergoing gametogenesis, we did not find evidence in the literature indicating an increase in tentacle numbers during this process in hydra. If such studies exist, we kindly request the complete references so we can include them in our discussion. Additionally, as noted in Brien's work, Hydra oligactis undergoing gametogenesis are known to either die or experience significant degeneration afterward. Transplanting tissue from dead or dying (and reproducing) hydras poses technical challenges and raises questions about whether any observed effects result from incomplete gametogenesis, the onset of senescence, or both. While these questions are intriguing, they fall outside the scope of our article.

In conclusion, we appreciate the opportunity to address these points and reaffirm that our study offers valuable insights into the evolutionary dynamics of interactions between transmissible tumor tissues and host phenotypes in hydra. We remain open to further discussion and welcome any additional feedback to enhance the clarity and robustness of our manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) If the fitness of hydra is altered in those with spontaneous tumors is the increased number of tentacles associated with those with transmitted tumors able to rescue this phenotype?

We thank the reviewer for reformulating our results. Indeed, fitness can be restored and even improved in tumorous polyps harboring supernumerary tentacles. This phenomenon, which we referred to as compensation and over-compensation in Section 3 and Figure 4, was initially discussed only in the discussion section. To improve the clarity of our manuscript, we have now specified this in the Conclusion (lines 345 to 347 and some minor rewording in the same paragraph) in the Results section (lines 284 to 286).

(2) Does the size of the tumor predict the number of tentacles formed?

We agree that this would be a valuable complementary analysis. We have conducted an analysis considering the qualitative size of the tumors (based on visual categories) and the number of tentacles, which is now included in our paper (lines 160-161; lines 193 to 198; lines 253 to 259; lines 314 - 322).

(3) Considering the mentioned association of body size with tentacle numbers for hydra, is a change in size a phenotype associated with transmitted tumors, and is such a phenotype transmittable. 

All tumorous individuals, regardless of their tumor type, exhibit a swollen body. We have added a sentence in the introduction to clarify this point (line 62).

(4) Is there anything unique about the Rob population that would explain their mass mortality following transplantation? For instance, their resistance to spontaneous tumor formation? Similarly, is there a difference in transplantation success based on the type of tissue transplanted? The authors could address this point in the discussion.

It is a very old lineage described nearly 80 years ago. It is unknown whether natural populations of Robusta exist, and no reports of any male individuals have been documented. We have added a sentence in the Materials and Methods section to clarify this information (lines 98 to 102).

(5) What downsides are known about the transmittable tumors in hydra and how present are they in the grafted individuals? Are other physiological aspects such as mobility, regeneration, or sexual reproduction hindered?

Transmissible tumors have been associated with increased vulnerability to predation and alterations in life history traits, including a higher budding rate and decreased sexual reproduction. While we were unable to measure behavioral traits in this study of our grafted individuals, this is an intriguing avenue for further research. We have included this perspective in the discussion section as a concluding remark (lines 375 to 382). Thanks a lot for the suggestion of this conclusion.

(6) It is important to explore the mechanisms behind the phenotypic variation conferred by the types of tumors, whether of different lineage or transmissibility. For this purpose, RNA-Seq on the recipients seems like a good starting point.

Thanks for this suggestion, we've reworded the sentence about this perspective in our discussion to be more precise (line 320).

Boutry, Justine, Marie Buysse, Sophie Tissot, Chantal Cazevielle, Rodrigo Hamede, Antoine M. Dujon, Beata Ujvari, et al. 2023. « Spontaneously Occurring Tumors in Different Wild-Derived Strains of Hydra ». Scientific Reports 13 (1): 7449. https://doi.org/10.1038/s41598-023-34656-0.

Domazet-Lošo, Tomislav, Alexander Klimovich, Boris Anokhin, Friederike Anton-Erxleben, Mailin J. Hamm, Christina Lange, et Thomas C. G. Bosch. 2014. « Naturally occurring tumours in the basal metazoan {Hydra} ». Nat Commun 5 (1): 4222. https://doi.org/10.1038/ncomms5222.

Ngo, Kha Sach, Berta R-Almási, Zoltán Barta, et Jácint Tökölyi. 2021. « Experimental Manipulation of Body Size Alters Life History in Hydra ». Ecology Letters 24 (4): 728‑38. https://doi.org/10.1111/ele.13698.

Author response:

The following is the authors’ response to the previous reviews.

This important study provides proof of principle that C. elegans models can be used to accelerate the discovery of candidate treatments for human Mendelian diseases by detailed high-throughput phenotyping of strains harboring mutations in orthologs of human disease genes. The data are compelling and support an approach that enables the potential rapid repurposing of FDA-approved drugs to treat rare diseases for which there are currently no effective treatments. The authors should provide a clearer explanation of how the statistical analyses were performed, as well as a link to a GitHub repository to clarify how figures and tables in the manuscript were generated from the phenotypic data.

We have amended our description of the statistical analysis in the materials and methods section of the manuscript. We have also updated the GitHub repository link to a dedicated repository for this study, this contains all of the code needed to generated all the figures made from the phenotypic data provided. Additionally, we have updated the Zenodo repository to contain both the code and datasets within the same file.

We have also updated the GitHub repository link to a dedicated repository for this manuscript, that contains all of the code needed to generate all figures from the phenotypic data provided. Additionally, we have updated the Zenodo repository link to contain both the code and datasets within the same folder structure. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have responded to previous review to improve the presentation of the work. The paper more than meets publication standards.

No response required.

Reviewer #2 (Recommendations for the authors):

The authors have addressed all of my questions and concerns. I'm happy to see this updated paper of record.

No response required.

Reviewer #3 (Recommendations for the authors):

Regarding the interactive heatmap

The html version and the panel in Figure 2C appear not to coincide visually. Maybe the features are ordered in a different way?

The html version of Figure 2C is for the entire feature set extract per strain and not the condensed Tierpsy256 set shown in the panel figure. We have now remade this figure to show this reduced feature set (aligning with what is shown in Figure 2C) and included both versions of the interactive heatmaps as static html files within the same repository.

Regarding data accessibility overall

More generally, the html file does not address my initial concern about the accessibility of the data to non-experts. Making the full dataset available was a necessary first step, but the hermetic nature of its format and the lack of a simple way to query the data remains an issue for me that limits the usefulness of this data to the broadest audience.

We agree, but unfortunately do not currently have the resources to build a public-facing database to facilitate this.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The work by Chuong et al. provides important new insights into the contribution of different molecular mechanisms in the dynamics of CNV formation. It will be of interest to anyone curious about genome architecture and evolution from yeast biologists to cancer researchers studying genome rearrangements.

Thank you for recognizing the broad significance of our study.

Strengths:

Their results are especially striking in that the "simplest" mechanism of GAP1 amplification-non-allelic homologous recombination between the flanking Ty-LTR elements is not the most common route taken by the cells, emphasizing the importance of experimentally testing what might seem on the surface to be obvious answers. One of the important developments of their work is the use of their neural network simulation-based inference (nnSBI) model to derive rates of amplicon formation and their fitness effects.

We agree with this assessment as the results of our study challenge our intuition that the simplest path to structural variation is the most likely and reveals the great diversity in mechanisms that can lead to large scale changes in the genome.

Weaknesses:

The manuscript reads as though two different people wrote two different sections of the manuscript - an experimental evolutionist and a computational scientist. If the goal is to reach both groups of readers, there needs to be more explanation of both types of work. I found the computational sections to be particularly dense but even the experimental sections need clearer explanations and more specific examples of the rearrangements found. I will point out these areas in the detailed remarks to the authors. While I have no reason to question their conclusions, I couldn't independently verify the results that ODIRA was the majority mechanism since the sequence of amplified clones was not made available during the review. I've encouraged the authors to include specific, detailed sequence information for both ODIRA events as well as the specific clones where GAP1 was amplified but the flanking gene GFP was not.

We have revised the manuscript to expand explanations of both the experimental and computational aspects of our study and to provide additional information for the reader. In doing so, we have edited the text to improve readability. We have made all raw data publicly available through the NCBI short read archive (SRA) and are hosting all sequence data for easy visualization in JBrowse using a public server.

Reviewer #2 (Public Review):

Summary:

This study examines how local DNA features around the amino acid permease gene GAP1 influence adaptation to glutamine-limited conditions through changes in GAP1 Copy Number Variation (CNV). The study is well motivated by the observation of numerous CNVs documented in many organisms, but difficulty in distinguishing the mechanisms by which they are formed, and whether or how local genomic elements influence their formation. The main finding is convincing and is that a nearby Autonomous Replicating Sequence (ARS) influences the formation of GAP1 CNVs and this is consistent with a predominate mechanism of Origin Dependent Inverted Repeat Amplification (ODIRA). These results along with finding and characterizing other mechanisms of GAP1 CNV formation will be of general interest to those studying CNVs in natural systems, experimental evolution, and in tumor evolution. While the results are limited to a single CNV of interest (GAP1), the carefully controlled experimental design and quantification of CNV formation will provide a useful guide to studying other CNVs and CNVs in other organisms.

Thank you for this positive assessment of our study.

Strengths:

The study was designed to examine the effects of two flanking genomic features next to GAP1 on CNV formation and adaptation during experimental evolution. This was accomplished by removing two Long Terminal Repeats (LTRs), removing a downstream ARS, and removing both LTRs and the ARS. Although there was some heterogeneity among replicates, later shown to include the size and breakpoints of the CNV and the presence of an unmarked CNV, both marker-assisted tracking of CNV formation and modeling of CNV rate and fitness effects showed that deletion of the ARS caused a clear difference compared to the control and the LTR deletion.

The consequence of deletion of local features (LTR and ARS) was quantified by genome sequencing of adaptive clones to identify the CNV size, copy number and infer the mechanism of CNV formation. This greatly added value to the study as it showed that i) ODIRA was the most common mechanism but ODIRA is enhanced by a local ARS, ii) non-allelic homologous recombination (NAHR) is also used but depends on LTRs, and iii) de novo insertion of transposable elements mediate NAHR in strains with both ARS and LTR deletions. Together, these results show how local features influence the mechanism of CNV formation, but also how alternative mechanisms can substitute when primary ones are unavailable.

We agree with this assessment.

Weaknesses:

The CNV mutation rate and its effect on fitness are hard to disentangle. The frequency of the amplified GFP provides information about mutation rate differences as well as fitness differences. The data and analysis show that each evolved population has multiple GAP1 CNV lineages within it, with some being unmarked by GFP. Thus, estimates of CNV fitness are more of a composite view of all CNV amplifications increasing in frequency during adaptation. Another unknown but potential complication is whether the local (ARS, LTR) deletions influence GAP1 expression and thus the fitness gain of GAP1 CNVs. The neural network simulation-based inference does a good job at estimating both mutation rates and fitness effects, while also accounting for unmarked CNVs. However, the model does not account for the population heterogeneity of CNVs and their fitness effects. Despite these limitations of distinguishing mutation rate and fitness differences, the authors' conclusions are well supported in that the LTR and ARS deletions have a clear impact on the CNV-mediated evolutionary outcome and the mechanism of CNV formation.

While it is true that the inferred mutation rate and fitness effect are negatively correlated, as in other studies (Gitschlag et al., 2023; Caspi et al., 2023; Avecilla et al., 2022), our modeling approach does generate an estimate of each parameter that is best explained by the data. By reporting the confidence intervals (i.e. the 95% HDI) we define the set of parameter values that are consistent with the data. It is true that our model doesn't explicitly account for population heterogeneity; rather, following Hegreness et al. (2006), we employ a single effective fitness effect and mutation rate for all GAP1 CNVs. It is interesting to consider whether the ARS and LTR affect GAP1 expression; however, we have no evidence that this is the case.

Reviewer #3 (Public Review):

Summary:

The authors represent an elegant and detailed investigation into the role of cis-elements, and therefore the underlying mechanisms, in gene dosage increase. Their most significant finding is that in their system copy number increase frequently occurs by what they call replication errors that result from the origin of replication firing.

The authors somewhat quantitatively determine the effect of the presence of a proximal origin of replication or LTR on the different CNV scenarios.

Strengths:

(1) A clever and elegant experimental design.

(2) A quantitative determination of the effect of a proximal origin of replication or LTR on the different CNV scenarios. Measuring directly the contribution of two competing elements.

(3) ODIRA can occur by firing of a distal ARS element.

(4) Re-insertion of Ty elements is interesting.

We agree that these are interesting and novel findings from our study.

Weaknesses:

(1) Overall, the research does not considerably advance the current knowledge. The research does not investigate what the maximum distance between ARS for ODIRA is to occur. This is an important point since ODIRA was previously described. A considerable contribution to the field would be to understand under what conditions ODIRA wins NAHR.

We agree that these are important questions and they are ones that we are pursuing in future studies.

(2) The title and some sentences in the abstract give a wrong impression of the generality and the novelty of the observations presented. Below are some examples of much earlier work that dealt with mechanisms of CNV and got different conclusions. The Lobachev lab (Cell 2006) published a different scenario years ago, with a very different mechanism (hair-pin capped breaks). The Argueso lab found something different (NAHR) (Genetics 2013).

In fact, the CUP1 system presents a good example of this point. The Houseley group showed a complex replication transcription-based mechanism (NAR 2022, cited), the Argueso group showed Ty-based amplification and the Resnick group showed aneuploidy-based amplification. While aneuploidy is a minor factor here the numerous works in Candida albicans, Cryptococcus neoformans, and Yeast suggest otherwise (Selmecki et al Science 2006, Yona et al PNAS 2013, Yang et al Microbiology Spectrum 2021).

As the reviewer points out there have been several important published studies investigating mechanisms by which structural variation is generated. It is important to note that we are explicitly looking at CNVs in the context of adaptive evolution and the role of genomic features that enable different mechanisms of CNV formation. To emphasize this point, we have changed the title of our manuscript to “Template switching during DNA replication is a prevalent source of adaptive gene amplification”. Aneuploidy is indeed a mechanism of adaptive gene amplification in our current and previously reported studies. We have expanded our discussion to place our study in the context of previous studies reporting mechanisms of gene amplification.

(3) The authors added a mathematical model to their experimental data. For me, it was very difficult to understand the contribution of the model to the research. I anticipated, for example, that the model would make predictions that would be tested experimentally. For example, " ARSΔ and ALLΔ are predicted to be almost eliminated by generation 116, as the average predicted WT proportion is 0.998 and 0.999" But to my understanding without testing the model.

In our previous publication (Avecilla et al. 2022, PLoS Biology) we experimentally validated the use of nnSBI to infer evolutionary parameters. In this study, we have extended our modeling framework to quantify differences between genotypes, which was not previously possible. Our results reveal that the local ARS has a key role in the overall supply rate of CNVs at this locus.

Recommendations for the authors:

We have addressed all public reviews and recommendations.

Reviewer #1 (Recommendations For The Authors):

Specific comments about the work are covered in the order of appearance in the text or Figures. I apologize in advance for the number of comments. They are made out of curiosity, enthusiasm for the research, and a desire to help highlight the most interesting aspects of this work.

We are grateful for the thoughtful comments that have helped us to significantly improve our manuscript.

(1) I would appreciate the inclusion of several references to the work on the ODIRA model.

a) Page 3 last paragraph: "(2) DNA replication-based mechanisms (Harel et al., 2015; Hastings, Lupski, et al., 2009; Malhotra & Sebat, 2012; Pös et al., 2021; Zhang, Gu, et al., 2009; Brewer et al., 2011)" (Addition of Brewer et al., 2011).

We have added all suggested references.

b) Page 4 top: (Brewer et al., 2011; Brewer et al., 2015; Martin et al., 2024). (Addition of Brewer et al., 2011).

We have added all suggested references.

c) Page 14 top: "Recent work has proposed that ODIRA CNVs are a major mechanism of CNVs in human genomes (Brewer et al., 2015; Martin et al., 2024; Brewer et al., 2024)." Brewer et al., 2024 focuses specifically on ODIRA and human CNVs. (Addition of Brewer et al., 2024).

We have added all suggested references.

(2) Page 6, third paragraph: I was surprised that a single inoculating strain was used to establish the replicate chemostats because of the possibility of non-independence of the resulting GAP1 CNVs. A nnSBI model was used to correct for this possibility later in the paper. It seems like it could have been avoided by a simple change in protocol to inoculate each chemostat with an independent inoculum. Was there a reason that the replicate chemostats were not conducted as independent events? Establishing the presence of 'founder' GAP1 CNVs without GFP seems rather secondary to the point of the paper (examining the CNVs that arise during evolution) and I would recommend it being moved to the supplement.

As is typical in microbial experimental evolution studies, we aimed to start with genetically identical homogenous populations and observe the emergence and selection of de novo variation. Therefore, we founded independent populations from a single inoculum. However, this study, and our prior work using lineage tracking barcodes, has clearly demonstrated that during the initial growth of the culture used for the inoculum CNVs are generated that contribute to the adaptation dynamics on all derived populations. This unanticipated result now suggests that the reviewer’s suggestion is a valid one - independent populations should be derived from independent inocula and this will be our standard practice in future studies.

We believe that our results, presented in Figure 2, establishing the presence of pre-existing GAP1 CNVs without the GFP are important as it highlights a limitation of the use of CNV reporters of gene copy number that was not previously known. However, we subsequently show that this class of variant - CNVs that are not detected by the reporter system - can be incorporated into our modeling framework enabling estimation of evolutionary parameters, which we believe is an important finding warranting inclusion in the main text.

(3) Page 7 first full paragraph: "Finally, we also observe a significant delay (ANOVA, p = 0.00833) in the generation at which the CNV frequency reaches equilibrium in ARS∆ (~generation 112) compared to WT (pairwise t-test, adjusted p = 0.05) . . .". Is the delay in reaching a plateau in Figure 1E just a consequence of the later appearance of CNVs or do the authors believe there are two separate events responsible for this delay? E.g. if the authors think that the delay in reaching a plateau is related to lower selection coefficients of the CNVs that do arise compared to the CNVs of other strains, then this should be explicitly discussed.

We believe that the delay in reaching equilibrium is a consequence of both a lower CNV formation and reduced selection coefficients. Lower values for the fitness coefficient and formation rate in ARS∆ explain both the delay in CNV appearance and CNV equilibrium as shown by the predicted dynamics (Figure S3B). We have added an explicit discussion of the effect of the ARS on CNV dynamics in paragraph 2 of the Discussion section paragraph 2 starting at line 456.

(4) Page 7: Incorporating pre-existing CNVs into an evolutionary model: The rationale for how you are able to discount the formation rate of GFP-free CNVs (C-) in your model isn't clear to me. How are you able to assume that these C- events don't form after timepoint 0? Why do you assume a starting population of C- events but not a starting population of C+ events?

We explored the possibility of modeling C- (amplifications of GAP1 without amplification of the reporter) during the evolution experiment. However, because the rate at which C- events occurs is slower than the rate at which C+ events occur (GAP1 amplifications with amplification of the reporter) we found that the effect was negligible. Importantly, the simple model is sufficient to describe the observed dynamics and thus we do not include these possible rare events.

(5) Figure 1:

(a) Panel B: Please put the tRNAs on the line diagrams of the four strains. I first interpreted ALLΔ as missing the tRNAs, too.

Thank you for this suggestion. We added tRNAs to all diagrams to provide additional detail about the structure of the GAP1 locus.

(b) Panels C, D, and E: the dark shade of the colored boxplots obscures the individual points. I recommend reducing the opacity of the box or choosing a lighter shade so that the individual points are visible on top of the box. Is the percent increase in CNVs per generation (Panel D) based on the slopes of the curves in panel B? By eye the slopes of ARS∆ and ALL∆ appear at least as steep as those of wild type and LTR∆.

Thank you for this suggestion. We have now made the individual points visible on top of the boxplots in Figures 1C, 1D, and 1E. The lines in Figure 1B show the median value across populations per time point whereas each point in Figure 1D is the slope from linear regression using values from individual populations (data from individual populations are shown in Figure 3C).

(6) Figure 2:

(a) Panel A: Please remind the readers what FSC-A is measuring and label the different groups of cells in each sample. Are we supposed to assume the upper scatter in generation 8 is the pre-existing CNV variants? Are the three species at generation 50 due to 1, 2, and 3 copies of GFP? Is the new species in generation 137 further amplification of the locus? And if so, how many copies does it represent? I find it fascinating that what I assume is the 2-copy CNV (presumably a direct oriented amplicon produced by NAHR) at 50 generations is lost (out-competed by a potential inverted triplication) at later times, but I didn't find any mention of this phenomenon in the text. What do the different mutant strains look like over the same time course? Please supply supplemental figures with the flow cytometry gating and vertically aligned histograms of the GFP signal so that the peaks are more easily compared. And provide this information for each of the altered strains in supplementary materials.

Thank you for these useful suggestions. We have added a gating legend to the figure to clearly indicate the copy-number for each subpopulation. We have edited the caption and main text to explain forward scatter (FSC-A). Raw flow cytometry plots are now provided as Supplementary figure 2 and distributions of cell-size normalized GFP signal are provided in Supplementary figure 3. Although our primary objective with Figure 2A was to show the persistence of the 1-copy GFP population the reviewer is correct that we did not highlight interesting aspects of the CNV dynamics. We have added additional text starting at line 251 to point out these features of the data.

(b) Panel B: It would help to label the different colored boxes inside cells in Figure 2B - it took me a while to identify the white box as an unrelated adaptive mutation elsewhere in the genome. The linear arrangement of these small colored blocks seems to indicate their structural arrangement. Is that the case? And are they inverted or direct amplicons? Perhaps the authors are being agnostic at this point but it would be better if each of the blocks were separate. If there are other mutations that can explain these GFP-non-amplified survivors, were they identified in your whole genome sequencing?

We have now included a complete legend for Figure 2B indicating that the white box reflects other beneficial mutations. We have separated this class of beneficial mutation from the GAP1 and reporter elements to reflect that they are not linked. We did not identify additional beneficial mutations but plan to pursue this question in a future project.

(c) Panel C: Are the two sets of lines mislabeled? One would expect the "reported" CNV proportions to be lower than the total CNV proportions, not the other way around. Maybe the labels "total CNVs" and "reported CNVs" are unclear to me and I am misunderstanding what "reported" refers to. Please clarify.

Thank you for identifying this mistake. The lines were mislabeled and have now been corrected in the revised version.

(7) Figure 3:

(a) A fuller discussion of panels A and B is needed. The results of panel A in particular seem like an excellent opportunity for connecting the computation to the biology. Can the authors speculate on why the ALL∆ strain has a higher CNV formation rate (𝛿c) than the ARS∆ strain? I would think that taking away one means of amplification would decrease CNV formation. Likewise, could the authors discuss why the selection coefficient (sc) for the LTR∆ strain would be the same as for the wild type? Overall, I would like to see more discussion about what these differences in formation rates and selection coefficients could mean for the types of amplicons arising in the chemostats. (In panel B I don't see the shaded area referred to in the figure legend.) A side-by-side comparison of the data in Panel A with the data shown in Supplemental Figure S3A would be instructive..

Thank you for raising these points. We have added substantial text to the manuscript to address these findings. Starting at line 456 we state:

“The lower CNV formation rate in the LTR∆ could be a closer approximation of ODIRA formation rates at this locus as ODIRA CNVs are the predominant CNV mechanism in the LTR∆ strain (Figure 4F). Furthermore, the low formation rates in the LTR∆ relative to WT might suggest that the presence of the flanking long terminal repeats may increase the rate of ODIRA formation through an otherwise unknown combinatorial effect of DNA replication across these flanking LTRs and template switching at the GAP1 locus. ARS∆ has the lowest CNV formation rate and it could be an approximation of the rates of NAHR between flanking LTRs and ODIRA at distal origins. We find that the ALL∆ has a higher CNV formation rate than the ARS∆, even though three elements are deleted instead of one. One explanation for this is that the deletion of the flanking LTRs in ALL∆ gives opportunity for novel transposon insertions and subsequent LTR NAHR. Indeed we find an enrichment of novel transposon-insertions in the ALL∆ (Figure 4F) and subsequent CNV formation through recombination of the Ty1-associated repeats (Figure 4H, ALL∆). Both events, transposon insertion followed by LTR NAHR, would have to occur quickly at a rate that explains our estimated CNV rate in ALL∆. While remarkable, increased transposon activity has been associated with nutrient stress (Curcio & Garfinkel, 1999; Lesage & Todeschini, 2005; Todeschini et al., 2005) and therefore feasible explanation for the CNV rate estimated in the ALL∆. Additionally, ARS∆ clones rely more on LTR NAHR to form CNVs (Figure 4F). The prevalence of ODIRA in ARS∆ and ALL∆ are similar. LTR NAHR usually occurs after double strand breaks at the long terminal repeats to give rise to CNVs (Argueso et al., 2008). Because we use haploid cells, such double strand break and homology-mediated repair would have to occur during S-phase after DNA replication with a sister chromatid repair template to form tandem duplications. Therefore the dependency on LTR NAHR to form CNVs and the spatial (breaks at LTR sequences) and temporal (S-phase) constraints could explain the lower formation rate in ARS∆.”

In addition, we added a discussion of the different selection coefficients estimated and how the simulated competitions help us understand the decreased selection coefficients in the architecture mutants. In newly added text starting at line 479 we state:

“The genomic elements have clear effects on the evolutionary dynamics in simulated competitive fitness experiments. The similar selection coefficients in WT and LTR∆ suggest that CNV clones formed in these background strains are similar. Indeed, the predominant CNV mechanism in both is ODIRA followed by LTR NAHR (Figure 4F). While LTR NAHR is abolished in the LTR∆, it seems that CNVs formed by ODIRA allow adaptation to glutamine-limitation similar to WT. The lower selection coefficients in ARS∆ and ALL∆ suggest that GAP1 CNVs formed in these strains have some cost. In a competition, they would get outcompeted by CNV alleles in the WT and LTR∆ background.”

(b) The data shown in panel C seems redundant to what is shown more clearly in Supplemental Figure S3B. It seems to me the more important comparison to make in panel C would be the overlay of the predicted data to the median proportion of cells obtained from the experimental data (Figure 1B). Also, overlays of the cultures from each strain could be added to S3A. It is difficult to see the variation within each strain when the data from all four strains are superimposed as they are in Figure 3C.

We agree and have edited Figure 3C to incorporate these suggestions and more clearly convey the intra- and interstrain variation.

(8) Figure 4:

(a) Panels A, B, and C are nice summaries and certainly helpful for understanding panel E, but it would be instructive to see some actual rearrangements of the ODIRA events, the NAHR, and the transposon-mediated rearrangements. It isn't clear to me what these last events look like. A figure that shows the specific architecture of example clones for each category would be helpful. I am also having a hard time reconciling ODIRA events with a copy number of 2. Are these rearrangements free isochromosomes with amplification to the telomere or are they secondary rearrangements like those described in Brewer et al., 2024? And what about the non-aneuploid rearrangement that includes the centromere? Is it a dicentric?

We have now added more detailed depictions of CNVs in Figure 4A and provide links to visualize the alignment files. We have added additional discussion starting at line 397 of the non-canonical ODIRA events and putative neochromosome amplicons with reference to Brewer et al 2024. Starting at line 397 we state:

“Surprisingly, we found CNVs with breakpoints consistent with ODIRA that contained only 2 copies of the amplified region, whereas ODIRA typically generates a triplication. In the absence of additional data, we cannot rule out inaccuracy in our read-depth estimates of copy numbers for these clones (ie. they have 3 copies). An alternate explanation is a secondary rearrangement of an original inverted triplication resulting in a duplication (Brewer et al., 2024); however, we did not detect evidence for secondary rearrangements in the sequencing data. A third alternate explanation is that a duplication was formed by hairpin capped double-strand break repair (Narayanan et al., 2006). Notably, we found 3 additional ODIRA clones that end in native telomeres, each of which had amplified 3 copies. In these clones the other breakpoint contains the centromere, indicating the entire right arm of chromosome XI was amplified 3 times via ODIRA, each generating supernumerary chromosomes. Thus,ODIRA can result in amplifications of large genomics regions from segmental amplifications to supernumerary chromosomes.”

(b) In Panel B the violin plots appear to indicate that there are two size categories for amplicons in the ARS∆ strain. Do clones from these different sub-populations share a common CNV architecture?

Thank you for making this point. (Please note that the violin plots are now Figure 4E) We added a short discussion and Supplementary Figure 14. In line 432, we state:

“In ARS∆, we find two CNV length groups (Figure 4E) that correspond with two different CNV mechanisms (Supplementary Figure 14). 100% of smaller CNVs (6-8kb) (Supplementary Figure 14) correspond with a mechanism of NAHR between LTRs flanking the GAP1 gene (Figure 4H, ARS∆, bottom left green points). Larger CNVs (8kb-200kb) (Supplementary Figure 14) correspond with other mechanisms that tend to produce larger CNVs, including ODIRA and NAHR between one local and one distal LTR element (Figure 4H).”

(c) Panels D and E: There is great information in these two panels but I find the color keys confusing. There doesn't seem to be any reason for the strain color key in panel E. I am assuming that the key should go with Panel D. Is there some way to indicate in Panel D which events are in which CNV category? It is cumbersome to find that information from Panel E. Perhaps the color-coding from Panel E could be applied to the row labels in Panel D. Being able to link amplicon to the mechanism of CNV formation is especially important for seeing which ODIRA events contain an origin.

Thank you for this suggestions. We now indicate the mechanism of CNV formation using a consistent color coding in panels G and H (previously panels D and E).

(d) Panel E: I don't understand the two axes in Panel E. If both axes are log scales, why is the origin 0 for the X-axis and 1 for the Y-axis? And why are the focal amplicons (most of which are recombination events between the two LTRs) scattered in both X and Y coordinates? Shouldn't they form a single point? The same for the recombinants with distal LTRs. Also, orange and red (ODIRA and complex CNVs, respectively) are very hard to distinguish. All of these data need to be presented in a spreadsheet identifying each clone's strain ID, chemostat number, GAP1 and GFP copy numbers, sequence across the junction, and their coordinates. The SRA project (PRJNA1016460) for the sequence data was not found in SRA. Will this data be available to easily look at read depth across chromosome XI for all of the sequenced strains - perhaps as .bam files?

Thank you for calling these issues with data visualization to our attention. Indeed, the focal amplifications do form around a single point. We originally had jittered the data to show each individual focal amplification but agree that this is confusing. We now overlay the individual points and have altered opacity to enable visualization of individual values. The suggested table of clone data is provided in Supplementary File 2 and the SRA project is now publicly available. Moreover, we are providing all alignment (.bam) files, split, and discordant read depth profiles for each CNV strain and their corresponding ancestor aligned to our custom reference genomes in a public jbrowse server at:

https://jbrowse.bio.nyu.edu/gresham/?data=data/ee_gap1_arch_muts for WT strains, https://jbrowse.bio.nyu.edu/gresham/LTRKO_clones for LTR∆ strains, https://jbrowse.bio.nyu.edu/gresham/ARSKO_clones for ARS∆ strains, https://jbrowse.bio.nyu.edu/gresham/ALLKO_clones for ALL∆ strains.

(e) Supplementary Table 1 and Supplementary Figure S2: Please indicate which rearrangements (of the 8 reported in Figure S2A) were identified in each of the clones described in the table. If each of the 8 amplicons is identified by a letter, then this information could be added as a column in the table. I am assuming that each of the eight rearrangements was found in more than one chemostat. Showing these data is crucial for establishing the possibility that they were preexisting at the time of chemostat inoculation. The other possibility is that the clones with amplified GAP1 but a single copy of GFP could have been created by a secondary rearrangement in the outgrowth of the clones that originally had amplified both genes to the same extent. What is the structure of these amplicons? Is there a common junction between GAP1 and GFP? I couldn't find these data in the paper. A suggestion for Supplemental Figure S2A - include a zoomed-in inset for the GAP1 GFP region for each of the 8 read-depth plots. It is hard to see the exact location of GFP and GAP1 across all 8 tracks without getting out a ruler. Were these sequences aligned to your custom reference genome or the reference genome without GFP? If they were aligned to the custom reference that includes the GFP reporter, the reader could visually confirm the absence of GFP amplification.

Thank you for these suggestions. We edited Supplementary Table 1 and Supplementary Figure 1A as requested. We now provide the precise CNV breakpoints in the GFP-GAP1 region (supplemental figure 1B) displaying both genome read depth and split read depth tracks. These sequences were aligned to the custom reference containing the GFP reporter, which is now clearer in the figure and caption text in line 1226.

The clones in this figure were sampled from the five different chemostats and we have clarified this in the edited table and text at line 210. We did not detect the same CNV allele in different chemostats and therefore we do not have evidence to support GAP1 amplification without the GFP reporter pre-existing at time of inoculation. We are not able to definitively distinguish whether the amplicons were pre-existing at the time of inoculation or occurred after as we do not have barcoded lineages. We isolated clones carrying this class of amplification from the 1-GFP-copy subfraction late in the experimental evolution (generation 165-182). Given that the alleles appear to differ between populations we think the most parsimonious explanation is that these amplifications occurred after chemostat inoculation but early in the evolution experiment. We explicitly state this in the text starting in line 219.

(9) Page 8-9: I am sorry to say that I can't evaluate the "HDI of posterior distributions". It is out of my competency range. So I am not sure what this analysis is adding to the paper. The same goes for the rest of the supplementary figures.

HDI is a measure of certainty in an estimate, similar to confidence interval. We state this in the text in line 276. With the editing of the text we hope the modeling and its supplementary figures are more clear now.

(10) Page 9 top: Deletion of the ARS appears to lower the fitness of the amplified GAP1 variants. Can the authors speculate on why the ARS deletion would reduce fitness? Did they consult published replication profiles to determine the size of the origin-free gap that could result from the deletion of this mid-S phase origin? Could it explain the delay in the appearance of GAP1 amplicons in the ARS-deletion strains and be responsible for their reduced selection coefficients? Did you examine the growth properties of the starting strain or any of the amplified GAP1 derivatives? Perhaps this consideration could contribute to the discussion. Could there be a bit fuller discussion on the interaction between CNV length differences as shown in Figure 4A and differences in selection coefficient as determined by the nnSBI?

Thank you for raising this point. We have now added text to our discussion of the reduced fitness in ARS∆ in relation to DNA replication starting on line 359:

“ARS1116 is a major origin (McGuffee et al., 2013) and ODIRA CNVs found around this origin corroborate its activity. GAP1 is highly transcribed in glutamine-limited chemostats (Airoldi et al., 2016). Head-on transcription-replication collisions at this locus may be contributing to the higher CNV formation rate in wild type and LTR∆. Elimination of the local ARS could result in less transcription-replication collisions and the slower CNV formation rates estimated. Once formed they get outcompeted by faster-forming CNVs and thus in theory are less fit than CNVs in other strain backgrounds. These simulated competitions further suggest that the ARS is a more important contributor to adaptive evolution mediated by GAP1 CNVs.”

We examined replication profiles in McGuffee et al. Mol Cell. 2013 but could not determine the size of the origin-free gap. ARS1116 and its neighboring ARSs, ARS1118 downstream and ARS1115 upstream are efficient firing origins (Supplement 1 of McGuffee et al. 2013) and therefore the gap is likely to be minimal. The dynamics of the distal firing ARS elements involved in creating ODIRA CNVs might explain the reduced fitness, but further experiments would be required to address this. Regarding growth properties, the growth rate at steady-state in the chemostat is the same as the dilution rate regardless of strain background. Because we had the same dilution rate for each chemostat, the ARS∆ populations would have the same replication rate as the other three strains even if there may be replication rate differences in bulk culture growth. Finally, we found no significant interaction between CNV length and selection coefficients and we state this in line 359.

(11) Page 10: WT competition simulations: It may help to explicitly state that the competition modeling approach was experimentally validated in Avecilla 2022 as opposed to just citing the paper. I found the results much more convincing after reading Avecilla 2022, but I imagine many readers may skip that.

We added a sentence to state that the nnSBI method was experimentally validated in Avecilla et 2022 at line 249.

Reviewer #2 (Recommendations For The Authors):

(1) Figure 2: says reported CNV proportions (dashed). This may be a typo since I think the GFP reported should be solid, not dashed. Also, (C) isn't bold.

Thank you for identifying these mistakes. We have corrected the figure’s caption in line 1157.

(2) "compared to 898/345 clones" Does this refer to transposition/clone? Seems more natural to compare clones with transpositions to a total number of clones. This could be clarified.

We rephrased the sentence (lines 519-520) to clarify that in their study Hays et al. 2023 found 898 novel Ty insertions across 345 nitrogen-evolved clones. As a result of this high rate of transposition, some clones are expected to have multiple Ty insertions.

(3) The methods state that Kan replaces the Nat cassette that was used to make the deletions. It should be made more clear whether Kan is present and where Kan is with respect to GFP and GAP1.

Thank you for pointing this out. To clarify we added the following sentence to the methods starting in line 567:

“The CNV reporter is 3.1 kb and located 1117 nucleotides upstream of the GAP1 coding sequence. It consists of, in the following order, an ACT1 promoter, mCitrine (GFP) coding sequence, ADH1 terminator, and kanamycin cassette under control of a TEF promoter and terminator.”

Additionally in line 571 we clarify the drug resistance of the genomic architecture ∆ strains that are kanamycin(+) and nourseothricin(-).

Reviewer #3 (Recommendations For The Authors):

(1) The major advancement of the manuscript is stated in the title "DNA replication errors are a major source of adaptive gene amplification" First, in my humble opinion the term replication errors is not quite right; the term template switching is more accurate. In that regard, recently a paper was published just on this topic (Martin et al Plos Genetics, 2024).

We have changed the title to “Template-switching during DNA replication is a prevalent source of adaptive gene amplification”. We cite Martin et al Plos Genetics 2024 throughout the main text in lines 93, 126, 159, 502, 555.

(2) I find the statement "We find that 49% of all GAP1 CNVs are mediated by the DNA replication-based mechanism Origin Dependent Inverted Repeat Amplification (ODIRA) regardless of background strain." Somewhat misleading, there were considerable differences between the strains. If I am not mistaken the range was 20-80%.

Thank you for pointing this out. Indeed, the range was 26-80% across the four strains. We updated this sentence in the abstract at line 40, and in the main text at line 141 to clearly state the range.

(3) In their attempt to fill the gap of knowledge regarding the fitness effect of the adaptive CNV the authors use a mathematical model. As an experimental biologist, I found the description lacking. It is hard for me to evaluate the contribution of the model to understanding the results and I think the authors could improve this part.

We have edited the text regarding the modeling and associated results and hope that it is now more clear. The mathematical model describes the experiment in a simplified manner. We use it to predict the outcomes of additional experiments without additional experimental work. For example, we used it to simulate a competition between two strains, predict the total proportion of GAP1 CNVs, and predict the relative genetic diversity.

(4) Experiments the authors may want to consider to increase the novelty of their work:

a) Place the GAP1 gene right in the middle of the two most distant ARS elements and test the mechanism of CNV.

Thank you for this proposed experiment. It is beyond the scope of this paper and will be pursued in future studies.

b) The finding of de-novo Ty element insertion is interesting. What happens if the overdose strain of Jef Boeke is used (Retrotransposon overdose and genome integrity, PNAS 2009) or in contrast, a reverse transcriptase deficient strain?

We agree. Our study has revealed a critical role for novel Ty insertion in mediating CNVs. The suggested experiments as well as using strains that lack Ty sequences will be very interesting to explore in followup studies.

c) The genomic analyses were based on single colony isolates. To my understanding, the CNV events are identified at least partly by split reads. Therefore, each event may have a "signature" that is unique and can be concluded from single reads and not necessarily from the assembled genome. If true, a distinction between the scenarios could be achieved if bulk cultures are sequenced with enough depth. Thus, a truly dynamic and quantitative determination of the different events, rate of appearance, and disappearance can be made.

Thank you for this suggestion, which is a good idea but not currently feasible for several reasons. First, although split reads are a powerful way to detect CNV breakpoints, we have found that even at high coverage (21-153X, median 78.5X), in clonal samples that are rare with only 3-30 split reads (median 14) detected. These observations are from a total of 23 breakpoints across 16 sequenced clones. Thus, when sequencing heterogeneous cultures, in which different CNVs only comprise a fraction of the population, our ability to detect single CNV alleles by split reads and quantify their frequency is limited. Given our observations, with a median of 14 split reads when sequencing to 78.5X genome-wide read coverage it is possible we may be able to detect an individual CNV allele once it makes up (14/78.5) 17% of the population. However, our previous study has shown that there are tens to hundreds of unique CNV alleles initially and thus this would only be feasible at very late timepoints. Second, recurrent CNVs may occur independently at the same exact location, such as LTR NAHR. Thus, unique signatures may not be obtained even if they are independent events. Third, it would be not appropriate to pursue this analysis with our current dataset, as we lack lineage tracking barcodes to validate the results.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

The authors sometimes seem to equivocate on to what extent they view their model as a neural (as opposed to merely behavioral) description. For example, they introduce their paper by citing work that views heterogeneity in strategy as the result of "relatively independent, separable circuits that are conceptualized as supporting distinct strategies, each potentially competing for control." The HMM, of course, also relates to internal states of the animal. Therefore, the reader might come away with the impression that the MoA-HMM is literally trying to model dynamic, competing controllers in the brain (e.g. basal ganglia vs. frontal cortex), as opposed to giving a descriptive account of their emergent behavior. If the former is really the intended interpretation, the authors should say more about how they think the weighting/arbitration mechanism between alternative strategies is implemented, and how it can be modulated over time. If not, they should make this clearer.

The MoA-HMM is meant to be descriptive in identifying behaviorally distinct strategies. Our intention in connecting it with a “mixture-of-strategies” view of the brain is that the results of the MoA-HMM could be indicative of an underlying arbitration process, but not modeling that process per se, that can be used to test neural hypotheses driven by this idea. We’ve added additional clarification in the discussion to highlight this point.

Explicitly, we added the following sentence in the discussion: “For example, while the MoA-HMM itself is a descriptive model of behavior and is not explicitly modeling an underlying arbitration of controllers in the brain, the resulting behavioral states may be indicative of underlying neural processes and help identify times when different neural controllers are prevailing”

Second, while the authors demonstrate that model recovery recapitulates the weight dynamics and action values (Fig. 3), the actual parameters that are recovered are less precise (Fig. 3 Supplement 1). The authors should comment on how this might affect their later inferences from behavioral data. Furthermore, it would be better to quantify using the R^2 score between simulated and recovered, rather than the Pearson correlation (r), which doesn't enforce unity slope and zero intercept (i.e. the line that is plotted), and so will tend to exaggerate the strength of parameter recovery.

In the methods section, we noted that the interaction between parameters can cause the recovery of randomly drawn parameter sets to fail, as seen in Figure 3 Supplement 1. This is because there are parameter regimes (specifically when a softmax temperature is near zero) which causes choices to be random, and therefore other parameters no longer matter. To address this, we included a second supplemental figure, Figure 3 Supplement 2, where we recovered model parameters from data simulated solely from models inferred from the behavioral data. Recovery of these models is much more precise, which credits our later inferences from the behavioral data.

To make this point clearer, we changed the reference to Figure 3 Supplements 1 & 2 to: “(Figure 3 – figure supplement 1 for recovery of randomized parameters with noted limitations, and figure supplement 2 for recovery of models fit to real data)” We additionally added the following to the Figure 3 Supplement 1 caption: “Due to the interaction between different model parameters (e.g. a small 𝛽 weight will affect the recoverability of the agent’s learning rate 𝛼), a number of “failures” can be seen.”

Furthermore, we added an R^2 score that enforces unity slope and zero intercept alongside the Pearson correlation coefficient for more comprehensive metrics of recovery. The R^2 scores are plotted on both Figure 3 Supplements 1 & 2 as “R2”, and the following text was added in both captions: “"r" is the Pearson's correlation coefficient between the simulated and recovered parameters, and "R2" is the coefficient of determination, R2, calculating how well the simulated parameters predict the recovered parameters.”

Finally, the authors are very aware of the difficulties associated with long-timescale (minutes) correlations with neural activity, including both satiety and electrode drift, so they do attempt to control for this using a third-order polynomial as a time regressor as well as interaction terms (Fig. 7 Supplement 1). However, on net there does not appear to be any significant difference between the permutation-corrected CPDs computed for states 2 and 3 across all neurons (Fig. 7D). This stands in contrast to the claim that "the modulation of the reward effect can also be seen between states 2 and 3 - state 2, on average, sees a higher modulation to reward that lasts significantly longer than modulation in state 3," which might be true for the neuron in Fig. 7C, but is never quantified. Thus, while I am convinced state modulation exists for model-based (MBr) outcome value (Fig. 7A-B), I'm not convinced that these more gradual shifts can be isolated by the MoA-HMM model, which is important to keep in mind for anyone looking to apply this model to their own data.

We agree with the reviewers that our initial test of CPD significance was not sufficient to support the claims we made about state differences, especially for Figure 7D. To address this, we updated the significance test and indicators in Figure 7B,D to instead signify when there is a significant difference between state CPDs. This updated test supports a small, but significant difference in early post-outcome reward modulation between states 2 and 3.

We clarified and updated the significance test in the methods with the following text:

“A CPD (for a particular predictor in a particular state in a particular time bin) was considered significant if that CPD computed using the true dataset was greater than 95% of corresponding CPDs (same predictor, same state, same time bin) computed using these permuted sessions. For display, we subtract the average permuted session CPD from the true CPD in order to allow meaningful comparison to 0.

To test whether neural coding of a particular predictor in a particular time bin significantly differed according to HMM state, we used a similar test. For each CPD that was significant according to the above test, we computed the difference between that CPD and the CPD for the same predictor and time bin in the other HMM states. We compare this difference to the corresponding differences in the circularly permuted sessions (same predictor, time bin, and pair of HMM states). We consider this difference to be significant if the difference in the true dataset is greater than 95% of the CPD differences computed from the permuted sessions.”

We updated the significance indicators above the panels in Figure 7B,D (colored points) to refer to significant differences between states, with additional text to the left of each row of points to specify the tested state and which states it is significantly greater than. We updated the figure caption for both B and D to reflect these changes.

We also changed text in the results to focus on significant differences between states. Specifically, we replaced the sentence “Looking at the CPD of expected outcome value split by state (Figure 7B) reveals that the trend from the example neuron is consistent across the population of OFC units, where state 2 shows the greatest CPD.” with the sentence “Looking at the CPD of expected outcome value split by state (Figure 7B) reveals that the trend from the example neuron is consistent across the population of OFC units, where state 2 has a significantly greater CPD than states 1 and 3.”

We also replaced the sentence “Suggestively, the modulation of the reward effect can also be seen between states 2 and 3 – state 2, on average, sees a higher modulation to reward that lasts significantly longer than modulation in state 3.” with the sentence “Additionally, the modulation of the reward effect can also be seen between states 2 and 3 — immediately after outcome, we see a small but significantly higher modulation to reward during state 2 than during state 3.”

Reviewer #2 (Public Review):

There were a lot of typos and some figures were mis-referenced in the text and figure legends.

We apologize for the numerous typos and errors in the text and are grateful for the assistance in identifying many of them. We have taken another thorough pass through the manuscript to address those identified by the reviewer as well as fix additional errors. To reduce redundancy, we’ll address all typoand error-related suggestions from both reviewers here.

● We fixed all Figure 1 references. We additionally reversed the introduction order of the agents in Figure 1 and in the results section “Reinforcement learning in the rat two-step task”, where we introduce both model-free agents before both model-based agents. This is to make the model-based choice agent description (which references the model-free choice agent in the statement “That is, like MFc, this agent tends to repeat or switch choices regardless of reward”) come after introducing the model-free choice agent.

● We fixed all Figure 4 references.

● We fixed all Figure 6 references and fixed the panel references in the figure caption to match the figure labeling: Starting with panel B, the reference to (i) was removed, and the reference to (ii) was updated to C. The previous reference to C was updated to D.

● All line-numbered suggestions were addressed.

● The text “(move to supplement?)” was removed from the methods heading, and the mistaken reference to Q_MBr was fixed.

● We removed all “SR” acronyms from the statistics as it was an artifact from an earlier draft.

● We homogenized notation in Figure 2, replacing all “c” variable references with “y”, as well as homogenized notation of β

● We replaced many uses of the word “action” with the word “choice” for consistency throughout the manuscript.

● We addressed many additional minor errors

Reviewer #1 (Recommendations For The Authors):

(1) Could the authors comment on why the cross-validated accuracy continues to increase, albeit non-significantly, after four states, as opposed to decreasing (as I would naively expect would be the result due to overfitting)?

Due to the large amounts of trials and sessions obtained from each rat (often >100 sessions with >200 trials per session) and the limited number of training iterations (capped at 300 iterations), it is not guaranteed that the cross-validated accuracy would decrease over the range of states we included in Figure 4, especially given that the number of total parameters in the largest model shown (7-states, 95 parameters) is greatly less than the number of observations. Since we’re mainly interested in using this tool to identify interpretable, consistent structure across animals, we did not focus on interpreting the regime of larger models.

(2) It seems like the model was refit multiple times with different priors ("Estimation of Population Prior"), each derived from the previous step of fitting. I'm not very familiar with fitting these kinds of models. Is this standard practice? It gives off the feeling of double-dipping. It would be helpful if the authors could cite some relevant literature here or further justify their choices.

We adopted a “one-step” hierarchical approach, where we estimate the population prior a single time on (nearly) unconstrained model fits, and use it for a second, final round of model fits which were used for analysis. Since the prior is only estimated once, in practice there isn’t risk of converging on an overly constrained prior. This is a somewhat simplified approach motivated by analogy to the first step of EM fit in a hierarchical model, in which population- and subject-level parameters are iteratively re-estimated in terms of one another until convergence (Huys et al., 2012; Daw 2010). We have clarified this approach in the methods with citations by adding the following paragraph:

“Hierarchical modeling gives a better estimate of how model parameters can vary within a population by additionally inferring the population distribution over which individuals are likely drawn (Daw, 2011). This type of modeling, however, is notoriously difficult in HMMs; therefore, as a compromise, we adopt a “one-step” hierarchical model, where we estimate population parameters from “unconstrained” fits on the data, which are then used as a prior to regularize the final model fits. This approach is motivated by analogy to the first step of EM fit in a hierarchical model, in which population- and subject-level parameters are iteratively re-estimated in terms of one another until convergence (Daw, 2011; Huys et al., 2012). It is important to emphasize, since we aren’t inferring the population distributions directly, that we only estimate the population prior a single time on the “unconstrained” fits as follows.”

Reviewer #2 (Recommendations For The Authors):

Figure 3a.iii: Did the model capture the transition probabilities correctly as well?

We have updated Figure 3E to include additional panels (iii) and (iv) to show the recovered initial state probabilities and transition matrix.

For Figure 6, panel B makes it look like there is a larger influence of state on ITI rate after omission, in both the top and bottom plots. However, the violin plots in panel C show a different pattern, where state has a greater effect on ITIs following rewarded trials. Is it that the example in panel B is not representative of the population, or am I misinterpreting?

We thank the reviewer for catching this issue, as the colors were erroneously flipped in panel C. We have fixed this figure by ensuring that the colors appropriately matched the trial type (reward or omission). Additionally, we updated the colors in B and C that correspond to reward (previously gray, now blue) and omission (previously gold, now red) trials to match the color scheme used in Figure 1. We also inverted the corresponding line styles (reward changed to solid, omission changed to dashed) to match the convention used in Figure 7. To differentiate from the reward/omission color changed, we additionally changed the colors in Figure 6D and Figure 7 Supplement 1, where the color for “time” was changed from blue to gray, and the color for “state” was changed from red to gold.

For figure 4B right, I am confused. The legend says that this is the change in model performance relative to a model with one fewer state. But the y-axis says it's the change from the single-state model. Please clarify.

The plot is showing the increase in performance from the single-state model, while the significance tests were done between consecutive numbered states. We updated the significance indicators on the plot to more clearly identify that adjacent models are being compared (with the exception of the 2-state model, which is being compared to 0). We updated the Figure 4B caption text for the left panel to state: “Change in normalized, cross-validated likelihood when adding additional hidden states into the MoA-HMM, relative to the single-state model. Significant changes are computed with respect to models with one fewer states (e.g. 2-state vs 1-state, 3-state vs 2-state)”

Author response:

Thank you for reviewing our manuscript and providing constructive feedback. We are grateful that you recognize the importance of our work and find the evidences presented compelling. We will revise our manuscripts in accordance with reviewers’ recommendations. Below is our plan.

(1) As recommended by Reviewer 1, we will improve the image resolution and presentation in the figures, by adjusting dark colors into brighter ones, including single-channel images, and incorporating schematic illustrations to dipict morphological changes.

(2) Following the suggestions of reviewer 2, we will provide explanations and speculative insights into potential non-tissue autonomous effects.

(3) As suggested by reviewer 2, we will perform principal component analyses on our RNA-seq and Cut&Tag data. 

(2) Once we have addressed all the major and minor points raised by the reviewers, we will provide a detailed point-to-point response and submit the revised version of the manuscript.

Author response:

We would like to express our sincere gratitude to both of you, and the reviewers, for the time and effort you have invested in reviewing our manuscript. We greatly appreciate the constructive feedback provided and are committed to addressing the suggested revisions.

In response to the public reviews, we would like to outline the following plan of action:

(1) Addressing Weaknesses in the Manuscript: We have carefully considered the comments regarding the weaknesses identified in the manuscript. Specifically, we will:

- Provide further clarification on the mechanism of IVM resistance in our study.

- Expand our discussion of the limitations and future directions of the research, addressing the concerns related to the potential translation of our findings to parasitic nematodes.

(2) Additional Experiments: We are currently conducting additional experiments to address the reviewers' suggestions, which include:

- Testing whether the overexpression of a relevant GluCl, such as AVR-15, can restore Ivermectin sensitivity in ubr-1 mutants.

- Examining the impact of Ceftriaxone treatment on the Ivermectin resistance in worms lacking key GluCls, such as avr-15, avr-14, and glc-1.

- Incorporating an analysis of major human parasitic nematodes in the phylogeny and discussing the conservation of relevant mechanisms across species.

- Double-checking the Dye filling (Dyf) phenotype in ubr-1 mutants, as suggested.

(3) Point-by-Point response: We will respond to both sets of comments (public reviews and editorial recommendations) in a comprehensive point-by-point manner in the revised manuscript.

(4) Timely Revisions: We aim to complete all revisions within a single round, ensuring that we address all comments thoroughly while maintaining the integrity of the data.

Author response:

Reviewer #1 (Public review):

Summary:

IPF is a disease lacking regressive therapies which has a poor prognosis, and so new therapies are needed. This ambitious phase 1 study builds on the authors' 2024 experience in Sci Tran Med with positive results with autologous transplantation of P63 progenitor cells in patients with COPD. The current study suggests that P63+ progenitor cell therapy is safe in patients with ILD. The authors attribute this to the acquisition of cells from a healthy upper lobe site, removed from the lung fibrosis. There are currently no cell-based therapies for ILD and in this regard the study is novel with important potential for clinical impact if validated in Phase 2 and 3 clinical trials.

Strengths:

This study addresses the need for an effective therapy for interstitial lung disease. It offers good evidence that the cells used for therapy are safe. In so doing it addresses a concern that some P63+ progenitor cells may be proinflammatory and harmful, as has been raised in the literature (articles which suggested some P63+ cells can promote honeycombing fibrosis; references 26 &35). The authors attribute the safety they observed (without proof) to the high HOPX expression of administered cells (a marker found in normal Type 1 AECs. The totality of the RNASeq suggests the cloned cells are not fibrogenic. They also offer exploratory data suggesting a relationship between clone roundness and PFT parameters (and a negative association between patient age and clone roundness).

We thank the reviewer for the important comments.

Weaknesses:

The authors can conclude they can isolate, clone, expand, and administer P63+ progenitor cells safely; but with the small sample size and lack of a placebo group, no efficacy should be implied.

We thank the reviewer for the suggestion and agree that we should be more cautious to discuss the efficacy of current study.

Specific points:

(1) The authors acknowledge most study weaknesses including the lack of a placebo group and the concurrent COVID-19 in half the subjects (the high-dose subjects). They indicate a phase 2 trial is underway to address these issues.

N/A

(2) The authors suggest an efficacy signal on pages 18 (improvement in 2 subjects' CT scans) and 21 (improvement in DLCO) but with such a small phase 1 study and such small increases in DLCO (+5.4%) the authors should refrain from this temptation (understandable as it is).

We believe that exploring potential efficacy signal is also one important aim of this study in addition to safety evaluation. All these efficacy endpoint analyses had been planned in prior to the start of clinical trials (as registered in ClinicalTrial.gov) and the results anyhow need be analyzed and reported in the manuscript. And we will cautiously discuss the significance of the efficacy signal and avoid over-interpretation.

(3) Likewise most CT scans were unchanged and those that improved were in the mid-dose group (albeit DLCO improved in the 2 patients whose CT scans improved).

Yes, it is.

(4) The authors note an impressive 58m increase in 6MWTD in the high-dose group but again there is no placebo group, and the low-dose group has no net change in 6MWTD at 24 weeks.

Yes.

(5) I also raise the question of the enrollment criteria in which 5 patients had essentially normal DLCO/VA values. In addition there is no discussion as to whether the transplanted stem cells are retained or exert benefit by a paracrine mechanism (which is the norm for cell-based therapies).

Thank you for your detailed feedback.  The enrollment criteria are based on DLCO instead of DLCO/VA. And we would like to further discuss the possible benefit by paracrine mechanism in the revised manuscript.

Reviewer #2 (Public review):

Summary:

This manuscript describes a first-in-human clinical trial of autologous stem cells to address IPF. The significance of this study is underscored by the limited efficacy of standard-of-care anti-fibrotic therapies and increasing knowledge of the role p63+ stem cells in lung regeneration in ARDS. While models of acute lung injury and p63+ stem cells have benefited from widespread and dynamic DAD and immune cell remodeling of damaged tissue, a key question in chronic lung disease is whether such cells could contribute to the remodeling of lung tissue that may be devoid of acute and dynamic injury. A second question is whether normal regions of the lung in an otherwise diseased organ can be identified as a source of "normal" p63+ stem cells, and how to assess these stem cells given recently identified p63+ stem cell variants emerging in chronic lung diseases including IPF. Lastly, questions of feasibility, safety, and efficacy need to be explored to set the foundation for autologous transplants to meet the huge need in chronic lung disease. The authors have addressed each of these questions to different extents in this initial study, which has yielded important if incomplete information for many of them.

Strengths:

As with a previous study from this group regarding autologous stem cell transplants for COPD (Ref. 24), they have shown that the stem cells they propagate do not form colonies in soft agar or cancers in these patients. While a full assessment of adverse events was confounded by a wave of Covid19 infections in the study participants, aside from brief fevers it appears these transplants are tolerated by these patients.

We thank the reviewer for the important comments.

Weaknesses:

The source of stem cells for these autologous transplants is generally bronchoscopic biopsies/brushings from 5th-generation bronchi. Although stem cells have been cloned and characterized from nasal, tracheal, and distal airway biopsies, the systematic cloning and analysis of p63+ stem cells across the bronchial generations is less clear. For instance, p63+ stem cells from the nasal and tracheal mucosa appear committed to upper airway epithelia marked by 90% ciliated cells and 10% goblet cells (Kumar et al., 2011. Ref. 14). In contrast, p63+ stem cells from distal lung differentiate to epithelia replete with Club, AT2, and AT1 markers. The spectrum of p63+ stem cells in the normal bronchi of any generation is less studied. In the present study, cells are obtained by bronchoscopy from 3-5 generation bronchi and expanded by in vitro propagation. Single-cell RNAseq identifies three clusters they refer to as C1, C2, and C3, with the major C1 cluster said to have characteristics of airway basal cells and C2 possibly the same cells in states of proliferation. Perhaps the most immediate question raised by these data is the nature of the C1/C2 cells. Whereas they are clearly p63/Krt5+ cells as are other stem cells of the airways, do they display differentiation character of "upper airway" marked by ciliated/goblet cell differentiation or those of the lung marked by AT2 and AT1 fates? This could be readily determined by 3-D differentiation in so-called air-liquid interface cultures pioneered by cystic fibrosis investigators and should be done as it would directly address the validity of the sourcing protocol for autologous cells for these transplants. This would more clearly link the present study with a previous study from the same investigators (Shi et al., 2019, Ref. 9) whereby distal airway stem cells mitigated fibrosis in the murine bleomycin model. The authors should also provide methods by which the autologous cells are propagated in vitro as these could impact the quality and fate of the progenitor cells prior to transplantation.

We totally agree that the sub-population of the progenitor cells should be further analyzed. We would try this in the revised manuscript. And the methods to expand P63+ lung progenitor cells have been described in full details by Frank McKeon/Wa Xian group (Rao, et.al., STAR Protocols, 2020), which is adapted to pharmaceutical-grade technology patented by Regend Therapeutics, Ltd.

The authors should also make a more concerted effort to compare Clusters 1, 2, and 3 with the variant stem cell identified in IPF (Wang et al., 2023, Ref. 27). While some of the markers are consistent with this variant stem cell population, others are not. A more detailed informatics analysis of normal stem cells of the airways and any variants reported could clarify whether the bronchial source of autologous stem cells is the best route to these transplants. 

We thank for reviewer for the good suggestion and would like to make more detailed comparison in the revised manuscript.

Other than these issues the authors should be commended for these first-in-human trials for this important condition.

Thank you so much for the kind compliment.

Author response:

Public Review:

In this work, the authors develop a new computational tool, DeepTX, for studying transcriptional bursting through the analysis of single-cell RNA sequencing (scRNA-seq) data using deep learning techniques. This tool aims to describe and predict the transcriptional bursting mechanism, including key model parameters and the steady-state distribution associated with the predicted parameters. By leveraging scRNA-seq data, DeepTX provides high-resolution transcriptional information at the single-cell level, despite the presence of noise that can cause gene expression variation. The authors apply DeepTX to DNA damage experiments, revealing distinct cellular responses based on transcriptional burst kinetics. Specifically, IdU treatment in mouse stem cells increases burst size, promoting differentiation, while 5FU affects burst frequency in human cancer cells, leading to apoptosis or, depending on the dose, to survival and potential drug resistance. These findings underscore the fundamental role of transcriptional burst regulation in cellular responses to DNA damage, including cell differentiation, apoptosis, and survival. Although the insights provided by this tool are mostly well supported by the authors' methods, certain aspects would benefit from further clarification.

The strengths of this paper lie in its methodological advancements and potential broad applicability. By employing the DeepTXSolver neural network, the authors efficiently approximate stationary distributions of mRNA count through a mixture of negative binomial distributions, establishing a simple yet accurate mapping between the kinetic parameters of the mechanistic model and the resulting steady-state distributions. This innovative use of neural networks allows for efficient inference of kinetic parameters with DeepTXInferrer, reducing computational costs significantly for complex, multi-gene models. The approach advances parameter estimation for high-dimensional datasets, leveraging the power of deep learning to overcome the computational expense typically associated with stochastic mechanistic models. Beyond its current application to DNA damage responses, the tool can be adapted to explore transcriptional changes due to various biological factors, making it valuable to the systems biology, bioinformatics, and mechanistic modelling communities. Additionally, this work contributes to the integration of mechanistic modelling and -omics data, a vital area in achieving deeper insights into biological systems at the cellular and molecular levels.

We thank the reviewers for their positive opinion on our manuscript. As reflected in our detailed responses to the reviewers’ comments, we will make significant changes to address their concerns comprehensively.

This work also presents some weaknesses, particularly concerning specific technical aspects. The tool was validated using synthetic data, and while it can predict parameters and steady-state distributions that explain gene expression behaviour across many genes, it requires substantial data for training. The authors account for measurement noise in the parameter inference process, which is commendable, yet they do not specify the exact number of samples required to achieve reliable predictions. Moreover, the tool has limitations arising from assumptions made in its design, such as assuming that gene expression counts for the same cell type follow a consistent distribution. This assumption may not hold in cases where RNA measurement timing introduces variability in expression profiles.

Thank you for your detailed and constructive feedback on our work. We will address the key concerns raised from the following points:

(1) Clarification on the required sample size: We tested the robustness of our inference method on simulated datasets by varying the number of single-cell samples. Our results indicated that the predictions of burst kinetics parameters become accurate when the number of cells reaches 500 (Supplementary Figure S3d, e). This sample size is smaller than the data typically obtained with current single-cell RNA sequencing (scRNA-seq) technologies, such as 10x Genomics and Smart-seq3 (Zheng GX et al., 2017; Hagemann-Jensen M et al., 2020). Therefore, we believed that our algorithm is well-suited for inferring burst kinetics from existing scRNA-seq datasets, where the sample size is sufficient for reliable predictions. We will clarify this point in the main text to make it easier for readers to use the tool.

(2) Assumption-related limitations: One of the fundamental assumptions in our study is that the expression counts of each gene are independently and identically distributed (i.i.d.) among cells, which is a commonly adopted assumption in many related works (Larsson AJM et al., 2019; Ochiai H et al., 2020; Luo S et al., 2023). However, we acknowledged the limitations of this assumption. The expression counts of the same gene in each cell may follow distinct distributions even from the same cell type, and dependencies between genes could exist in realistic biological processes. We recognized this and will deeply discuss these limitations from assumptions and prospect as an important direction for future research.

The authors present a deep learning pipeline to predict the steady-state distribution, model parameters, and statistical measures solely from scRNA-seq data. Results across three datasets appear robust, indicating that the tool successfully identifies genes associated with expression variability and generates consistent distributions based on its parameters. However, it remains unclear whether these results are sufficient to fully characterize the transcriptional bursting parameter space. The parameters identified by the tool pertain only to the steady-state distribution of the observed data, without ensuring that this distribution specifically originates from transcriptional bursting dynamics.

We appreciate your insightful comments and the opportunity to clarify our study’s contributions and limitations. Although we agree that assessing whether the results from these three realistic datasets can represent the characterize transcriptional burst parameter space is challenging, as it depends on data property and conditions in biology, we firmly believe that DeepTX has the capacity to characterize the full parameter space. This believes stems from the extensive parameters and samples we input during model training and inference across a sufficiently large parameter range (Method 1.3). Furthermore, the training of the model is both flexible and scalable, allowing for the expansion of the transcriptional burst parameter space as needed. We will clarify this in the text to enable readers to use DeepTX more flexibly.

On the other hand, we agree that parameter identification is based on the steady-state distribution of the observed data (static data), which loses information about the fine dynamic process of the burst kinetics. In principle, tracking the gene expression of living cells can provide the most complete information about real-time transcriptional dynamics across various timescales (Rodriguez J et al., 2019). However, it is typically limited to only a small number of genes and cells, which could not investigate general principles of transcriptional burst kinetics on a genome-wide scale. Therefore, leveraging the both steady-state distribution of scRNA-seq data and mathematical dynamic modelling to infer genome-wide transcriptional bursting dynamics represents a critical and emerging frontier in this field. For example, the statistical inference framework based on the Markovian telegraph model, as demonstrated in (Larsson AJM et al., 2019), offers a valuable paradigm for understanding underlying transcriptional bursting mechanisms. Building on this, our study considered a more generalized non-Mordovian model that better captures transcriptional kinetics by employing deep learning method under conditions such as DNA damage. This provided a powerful framework for comparative analyses of how DNA damage induces alterations in transcriptional bursting kinetics across the genome. We will highlight the limitations of current inference using steady-state distributions in the text and look ahead to future research directions for inference using time series data across the genome.

A primary concern with the TXmodel is its reliance on four independent parameters to describe gene state-switching dynamics. Although this general model can capture specific cases, such as the refractory and telegraph models, accurately estimating the parameters of the refractory model using only steady-state distributions and typical cell counts proves challenging in the absence of time-dependent data.

We thank you for highlighting this critical concern regarding the TXmodel's reliance on four independent parameters to describe gene state-switching dynamics. We acknowledge that estimating the parameters of the TXmodel using only steady-state distributions and typical single-cell RNA sequencing (scRNA-seq) data poses significant challenges, particularly in the absence of time-resolved measurements.

As described in the response of last point, while time-resolved data can provide richer information than static scRNA-seq data, it is currently limited to a small number of genes and cells, whereas static scRNA-seq data typically capture genome-wide expression. Our framework leverages deep learning methods to link mechanistic models with static scRNA-seq data, enabling the inference of genome-wide dynamic behaviors of genes. This provides a potential pathway for comparative analyses of transcriptional bursting kinetics across the entire genome.

Nonetheless, the refractory model and telegraphic model are important models for studying transcription bursts. We will discuss and compare them in terms of the accuracy of inferred parameters. Certainly, we agree that inferring the molecular mechanisms underlying transcriptional burst kinetics using time-resolved data remains a critical future direction. We will include a brief discussion on the role and importance of time-resolved data in addressing these challenges in the discussion section of the revised manuscript.

The claim that the GO analysis pertains specifically to DNA damage response signal transduction and cell cycle G2/M phase transition is not fully accurate. In reality, the GO analysis yielded stronger p-values for pathways related to the mitotic cell cycle checkpoint signalling. As presented, the GO analysis serves more as a preliminary starting point for further bioinformatics investigation that could substantiate these conclusions. Additionally, while GSEA analysis was performed following the GO analysis, the involvement of the cardiac muscle cell differentiation pathway remains unclear, as it was not among the GO terms identified in the initial GO analysis.

We thank the reviewer for this valuable feedback and for pointing out the need for clarification regarding the GO and GSEA analyses. We agree that the connection between the cardiac muscle cell differentiation pathway identified in the GSEA analysis and the GO terms from the initial analysis requires further clarification. This discrepancy arises because GSEA examines broader sets of pathways and may capture biological processes not highlighted by GO analysis due to differences in the statistical methods and pathway definitions used. We will revise the manuscript to address this point, explicitly discussing the distinct yet complementary nature of GO and GSEA analyses and providing a clearer interpretation of the results.

As the advancement is primarily methodological, it lacks a comprehensive comparison with traditional methods that serve similar functions. Consequently, the overall evaluation of the method, including aspects such as inference accuracy, computational efficiency, and memory cost, remains unclear. The paper would benefit from being contextualised alongside other computational tools aimed at integrating mechanistic modelling with single-cell RNA sequencing data. Additional context regarding the advantages of deep learning methods, the challenges of analysing large, high-dimensional datasets, and the complexities of parameter estimation for intricate models would strengthen the work.

We greatly appreciate your insightful feedback, which highlights important considerations for evaluating and contextualizing our methodological advancements. Below, we emphasize our advantages from both the modeling perspective and the inference perspective compared with previous model. As our work is rooted in a model-based approach to describe the transcriptional bursting process underlying gene expression, the classic telegraph model (Markovian) and non-Markovian models which are commonly employed are suitable for this purpose:

Classic telegraph model: The classic telegraph model allows for the derivation of approximate analytical solutions through numerical integration, enabling efficient parameter point estimation via maximum likelihood methods, e.g., as explored in (Larsson AJM et al., 2019). Although exact analytical solutions for the telegraph model are not available, certain moments of its distribution can be explicitly derived. This allows for an alternative approach to parameter inference using moment-based estimation methods, e.g., as explored in (Ochiai H et al., 2020). However, it is important to note that higher-order sample moments can be unstable, potentially leading to significant estimation bias.

Non-Markovian Models: For non-Markovian models, analytical or approximate analytical solutions remain elusive. Previous work has employed pseudo-likelihood approaches, leveraging statistical properties of the model’s solutions to estimate parameters, e.g., as explored in (Luo S et al., 2023). However, the method may suffer from low inference efficiency.

In our current work, we leverage deep learning to estimate parameters of TXmodel, which is non-Markovian model. First, we represent the model's solution as a mixture of negative binomial distributions, which is obtained by the deep learning method. Second, through integration with the deep learning architecture, the model parameters can be optimized using automatic differentiation, significantly improving inference efficiency. Furthermore, by employing a Bayesian framework, our method provides posterior distributions for the estimated dynamic parameters, offering a comprehensive characterization of uncertainty. Compared to traditional methods such as moment-based estimation or pseudo-likelihood approaches, we believe our approach not only achieves higher inference efficiency but also delivers posterior distributions for kinetics parameters, enhancing the interpretability and robustness of the results. We will present and emphasize the computational efficiency and memory cost of our methods the revised version.

Reference

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Hagemann-Jensen, M., Ziegenhain, C., Chen, P., Ramsköld, D., Hendriks, G.J., Larsson, A.J.M., Faridani, O.R., Sandberg, R. 2020. Single-cell RNA counting at allele and isoform resolution using Smart-seq3. Nat Biotechnol 38: 708-714. DOI: https://dx.doi.org/10.1038/s41587-020-0497-0, PMID: 32518404

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Ochiai, H., Hayashi, T., Umeda, M., Yoshimura, M., Harada, A., Shimizu, Y., Nakano, K., Saitoh, N., Liu, Z., Yamamoto, T., Okamura, T., Ohkawa, Y., Kimura, H., Nikaido, I. 2020. Genome-wide kinetic properties of transcriptional bursting in mouse embryonic stem cells. Science Adavances 6: eaaz6699. DOI: https://dx.doi.org/10.1126/sciadv.aaz6699, PMID: 32596448

Luo, S., Wang, Z., Zhang, Z., Zhou, T., Zhang, J. 2023. Genome-wide inference reveals that feedback regulations constrain promoter-dependent transcriptional burst kinetics. Nucleic Acids Research 51: 68-83. DOI: https://dx.doi.org/10.1093/nar/gkac1204, PMID: 36583343

Rodriguez, J., Ren, G., Day, C.R., Zhao, K., Chow, C.C., Larson, D.R. 2019. Intrinsic dynamics of a human gene reveal the basis of expression heterogeneity. Cell 176: 213-226.e218. DOI: https://dx.doi.org/10.1016/j.cell.2018.11.026, PMID: 30554876

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Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Recommendations For The Authors):

(1) Gap of knowledge:

From the introduction, I got the impression that the manuscript tries to answer the question of whether homeostatic structural plasticity is functionally redundant to synaptic scaling. However, the importance of this question needs to be worked out better. Also, I think it is hard to tackle this question with the shown experiments as one would have to block all other redundant mechanisms and see whether HSP functionally replaces them.

We appreciate the reviewer’s valuable feedback regarding the relationship between homeostatic structural plasticity (HSP) and synaptic scaling. The main objective of our study is indeed to investigate whether structural plasticity is homeostatically regulated, and if so, whether it acts as a redundant or heterogeneous mechanism in relation to synaptic scaling, which is widely recognized as a primary homeostatic process.

In our revised introduction, we have clarified this central question and its significance. Specifically, we explored why experimentally observed changes in spine density, a measure of structural plasticity, do not exhibit the same homeostatic characteristics as changes in spine head size, which reflects synaptic scaling, particularly under conditions of activity blockade.

We hypothesized two key points:

(1) Structural plasticity may not follow a monotonically activity-dependent rule as strictly as synaptic scaling.

(2) The observed changes in spine density may be influenced by the simultaneous modulation of spine size, suggesting that structural plasticity and synaptic scaling interact within the same biological system.

Both hypotheses were tested through a combination of experimental observations and systematic computer simulations. Our conclusions demonstrate that spine-number-based structural plasticity follows a biphasic activity-dependent rule. While it largely overlaps with synaptic scaling under typical conditions, it exhibits heterogeneity under extreme conditions, such as activity silencing. Furthermore, our simulations revealed that both mechanisms can compete and complement each other within neural networks.

We believe that these results offer a nuanced understanding of the interaction between structural plasticity and synaptic scaling, highlighting their redundancy under most conditions but also their heterogeneity under specific circumstances. Blocking all other redundant mechanisms, as suggested, would provide a more reductionist view, which may not capture the complexity and interplay of these processes in a physiological setting. Our approach reflects this complexity, providing insight into how these mechanisms operate together in a naturalistic context.

We have revised the introduction to better convey these points and emphasize the significance of this question for understanding the dynamics of homeostatic regulation in neural networks.

Similarly, the simulations do not really tackle redundancy as, e.g. network growth cannot be achieved by scaling alone.

We appreciate the reviewer’s comment regarding synaptic scaling's limitations in achieving network growth. We would like to clarify that we did not intend to suggest that structural plasticity and synaptic scaling are fully redundant. In fact, it is well established in the literature that structural plasticity plays a dominant role during development, particularly in network growth, which synaptic scaling alone cannot achieve.

The primary objective of our study was to investigate the interaction between structural plasticity and synaptic scaling under conditions of activity perturbation, rather than during network growth or development. To avoid any confusion regarding developmental processes, we chose to grow the network using only structural plasticity in our simulations. Synaptic scaling was then introduced (or not) during the phase of activity deprivation to specifically examine its role in regulating homeostasis under these conditions.

We have revised the corresponding sections of the manuscript to clarify this distinction, and we have ensured that the simulations reflect our focus on activity perturbation rather than network development. This distinction should help readers avoid conflating developmental processes with the specific goals of our study.

Instead, the section on "Integral feedback mechanisms" (L112-129) contains a much better description of the actual goals of the paper than is given in the introduction. Moreover, this section does not seem to include any new results (at least the Ca-dependent structural plasticity and synaptic scaling rules seem to be very common for me). I, therefore, suggest fusing this paragraph in the introduction to obtain a clearer and better understandable gap of knowledge, which is addressed by the paper.

We agree that the "Integral feedback control" section provides key information relevant to both the Introduction and Methodology. It outlines the theoretical framework and serves as a basis for the experimental design.

To better reflect this, we have revised the Introduction to include the gap in knowledge. However, we opted to retain the section in the Results, slightly modified, to set the context for the first experiment.

Along this line, as it seems a central point of the manuscript to distinguish the controller dependencies on Calcium, the different dependencies (working models) should be described in more detail. Also, the description of the inconsistencies of the previous results on HSP can be moved from the discussion (l419-l441) to the introduction.

We have revised the manuscript to place less emphasis on the controller models while retaining the core principles of control theory. The description of the HSP model has been moved to the Introduction, as suggested, while the detailed history remains in the Discussion to maintain the manuscript's consistency.

Systematic text revision: Regarding comment (1), we thank the reviewer for suggesting the text reorganization. We have adjusted several parts in the introduction, M&M section, and results section to increase clarity.

(2) Pharmacological Choice:

It should be discussed why NBQX is used to induce the homeostatic effect instead of TTX. As there are studies showing that it might block homeostatic rewiring (doi.org/10.1073/pnas.0501881102) as well as synaptic scaling (10.1523/JNEUROSCI.3753-08.2009), it seems unclear whether the observed effects are actually corresponding to those in other publications.

The rationale for using NBQX in our experiments, rather than TTX, is detailed in the public response. We selected NBQX based on specific experimental motivations relevant to our study’s objectives, while acknowledging the potential differences in effects compared to other studies.

Local text revision: We added one paragraph in the discussion section to explain the idea better.

(3) Model-Experiment Connection:

The paper combines simulations with experimental work, which is very good. However, in my opinion, the only connection between the two parts is that the experiments suggest a non-monotonic dependency between firing rate and synapse density (i.e. the biphasic dependency). The rest of the experimental results seem to be neglected in the modeling part. It is not even shown that the model reproduces the experiments. Instead, the model is tested in different situations and paradigms (blocking AMPARs in the whole culture vs network growth or silencing a sub-population). I think it would make the paper stronger and more consequential when a reproduction of the experiment by the model is demonstrated (with analogue analyses).

The experimental results serve three main purposes. First, as the reviewer noted, the spine analysis was conducted to inform the biphasic rule. Second, spine size analysis was performed to replicate published findings and confirm our modeling results, showing that activity deprivation leads to fewer synapses with larger sizes or higher weights. Third, the correlation analysis of spine density and size across dendritic segments suggested a hybrid combination of two types of plasticity across different neurons.

While we addressed these aspects in the Results and Discussion sections, the collective presentation in Fig. 2 may have caused some confusion. To improve clarity, we have now split the experimental results, presenting them alongside the relevant modeling data in Fig. 2, Fig. 8, and Fig. 9.

Also, there are a few more mismatches between the experiment and the model that you will want to discuss:

• The size-dependent homeostatic effect (l154ff, Fig2F) is not reflected by the used scaling model.

We revised Fig 8 and the corresponding text to explain how the scaling model reflects such an effect.

• The model assumes reduced Ca levels. Yet, the experimental protocol blocks AMPARs, which are to my knowledge not the primary source of Ca influx, but rather the NMDARs.

The model is based on neural activity, with calcium concentration serving as an internal integral signal of the firing rate, allowing for integral control. While calcium plays a critical role in homeostasis, we caution against drawing a strict correspondence between the model's calcium dynamics and the experimental protocol, as calcium can be sourced from multiple pathways in neurons beyond AMPARs, such as NMDARs, voltage gated calcium channels, and intracellular stores. Also, our recent work demonstrated that under baseline conditions, the majority of AMPARs are not Ca2+ permeable, i.e., GluA2-lacking (Kleidonas et al., 2023)

Improving the calcium dynamics, including secondary calcium release and calcium stores, is part of our future plan to refine the HSP model and address experimental findings that are not fully explained by the current model.

• The model further assumes silencing by input removal, whereas the recurrent connections stay intact. Wouldn't this rather correspond to a deafferentation experiment, where connections to another brain area are cut?

Thank you for pointing at this. The modeling section was not intended to directly replicate the tissue culture experiments but rather to provide insights into a broader range of scenarios, including pharmacological treatments, deafferentation, lesions, and even monocular deprivation.

Systematic text revision: Regarding comment (3), the goal of our modeling work was more than reproducing. To better serve the purposes of experimental results used in the present study, to inform, confirm, and inspire, we have systematically adjusted the layout of experimental and modeling results to link them better.

(4) Is the recurrent component too weak?

Your results show that HSP does not restore activity after silencing (deafferentation), whereas you discuss that earlier models did achieve this by active neighbors in a spatially organized network. However, the silenced neurons in your simulations also receive inputs through the "recurrent" connections from their neighbors (at least shortly after silencing). Therefore, given the recurrent input is strong enough, they should be able to recover in a similar way as the spatially organized ones. As a consequence, I obtained the impression that, in your model networks, activity is strongly driven by external stimulation and less by recurrent connections. I understand that this is important to achieve silencing through removing the Poisson stimulation. Yet, this fact may be responsible for the failure to restore activity such that presented effects are only applicable for networks that are strongly driven by external inputs, but not for strongly recurrent networks, which would severely limit the generality of the results. As a consequence, the paper would benefit from a systematic analysis of the trade-off between recurrent strength and input strength. Maybe, different constant negative currents could be injected in all neurons, such that HSP creates more recurrent synapses in the network.

We appreciate this insight. However, increasing recurrent input strength is beyond the scope of the current study, as it would fundamentally alter the predefined network dynamics of the Brunel network used. As noted in the manuscript, complete isolation or cell death is not always the outcome after input deprivation, lesion, or stroke, which cannot be fully explained by the Gaussian HSP rule alone. Butz and colleagues offered a solution using growth rules that maximized recurrent input, and we recognize the importance of their work.

That said, we approached the issue from a different angle, emphasizing the role of synaptic scaling in recurrence rather than relying solely on recurrent input strength. In biological networks, external inputs may vary, recurrency can be weak or strong, and synaptic scaling can dominate. Our model offers a complementary hypothesis, suggesting that these factors, in combination, contribute to the diverse and sometimes contradictory results found in the literature, rather than posing a strict constraint on network topology.

Local text revision: We emphasized these points in the Discussion section again.

(5) Missing conclusions / experimental predictions

As already described, the modelling work is not reproducing the presented or previous experimental data. Hence, the goal of modelling should be to derive a more general understanding and make experimental predictions. Yet, the conclusions in the discussion stay superficial and vague and there are no specific experimental predictions derived from the model results.

For example, the authors report that the recovery of activity in silenced cultures is observed in a previously spatially structured model but not in theirs -- at least with slow or no scaling. Yet it is left to the reader to think about whether the current model is an improvement to the previous one, how they could be experimentally distinguished, or to which experimental findings they relate or compare, which I would expect at this point. I would advise reworking the discussion and thoroughly working out which new insights the modelling part of the study has generated (not to be confused with the assumptions of the model aka the biphasic plasticity rule) and relating them to experimental pre- and postdiction.

We recognize the reviewer’s concern, which is closely related to comment (4). We have addressed these points by reorganizing the text to better clarify the purpose of our experimental work and its connection to the modeling results.

Specifically, we have reworked the discussion to highlight the new insights gained from the modeling, and how these can inform experimental predictions and interpretations. This includes distinguishing our model from previous ones and providing clearer connections to experimental findings.

Systematic text revision: Most of the comments on combining experiments and modeling results and on developing the story based on our expectations raised here are sincere and may also reflect the expectations and concerns of a broader readership, so we have accordingly adjusted the text in the Results and Discussion sections to make our points clear.

Suggestions for minor changes:

Fig 1I: Please check the graph and make it more self-explaining. For example, mark the "setpoint" activity (in my opinion, both curves should be at baseline there. In that case, however, I do not see the biphasic behavior anymore). Maybe the table and the graph can be aligned along the activity axis? Also: synaptic inhibition should be increased and not decreased, right?

Local text and figure revision: I guess the reviewer meant for Fig. 2I? We have improved the visualization to avoid confusion.

L74-81: I would reverse the order of associative and homeostatic plasticity in this paragraph.

Local text and figure revision: We have fine-tuned the order in the first and second paragraphs to match the readers' expectations.

L74-75: Provide references for such theories.

Local text and figure revision: fixed.

L84-86: Please provide a reference for the claim that negative feedback, redundancy, and heterogeneity contribute to robustness.

Local text and figure revision: fixed.

L 95-97: I think the heterogeneity aspect needs to be worked out a bit better. Do you mean that the described mechanisms contribute to firing rate homeostasis in a different mixture for each neuron (as shown assumed in the last figure)?

Local text and figure revision: The term heterogeneity is used in the manuscript for two major different settings: (1) heterogeneity in terms of control theory and (2) different combinations of HSP and SS rules. We have named the second condition as diversity to avoid confusion.

L 132: The question of linearity has not been posed so far. Also, I think "monotonous" would be a much better term than linear (as a test for linearity would require more than 2 datapoints).

Local text and figure revision: We agreed linear is not a good term. We replaced it with ‘monotonic’ throughout the manuscript.

Fig2 Bii: The data for 50um is clearly not Gaussian.

We did not imply that the 50 µM condition is Gaussian. Instead, we noted that the non-linearity observed in both the 200 nM and 50 µM data suggests a non-monotonic growth rule rather than a linear one. We applied the Gaussian rule because it has been extensively studied in previous simulations, allowing us to benchmark our findings against those results.

Fig2 D, E inset: The point at time 0 does not convey any information and could be left out.

The time zero data is included to demonstrate that the three groups have a similar baseline, ensuring that any observed differences are due to the treatment and not pre-existing biases in the grouping.

L 178: As the Gaussian rule drops below zero above the upper set-point again, it is rather tri-phasic than bi-phasic.

We intended to convey that inhibition results in either spine growth or deletion, reflecting a bi-phasic response rather than a true tri-phasic one.

Fig 6A: You may want to mark the eta variables in the curves.

Local text and figure revision: fixed.

Fig 6E: The curve of the S population extending to the next panel looks a bit messy.

We retained the curve extension to visually convey the impression of excessive network activity.

L272: It needs to be better described/motivated how protocol 1 and 2 are supposed to study the role of recurrent connection as well as what kind of biological situation this may be.

Local text and figure revision: The corresponding text has been adjusted to avoid confusion.

L 272: It is not clear how faster simulation leads to less recurrent connectivity, when the stimulation protocol and the rates stay the same and the algorithm compensates for the timestep properly. Maybe you rather want to say that you silence 10x longer and stimulate 10x longer?

Local text revision: The corresponding text has been adjusted to avoid confusion.

L. 302: "reactivate"?

Local text revision: fixed.

L 322f: I would suggest showing the connectivity matrix for a time-point with restored activity as well.

Local text and figure revision: fixed.

Fig 8A: The use of the morphological reconstructions is a bit misleading as the model uses point neuron.

Local text revision: Now after reorganization, it is in Fig.9. We kept the reconstruction figure for motivational purposes, suggesting how to understand the meaning of the combinations in more biologically realistic scenarios. The corresponding text has been adjusted to avoid confusion.

Fig 8E-F: the y axis should be in the same orientation as in panel D.

Local text and figure revision: Good idea and fixed in the new Fig. 9.

Fig. 8F: The results here look a little bit random. Maybe more runs with the same parameters would smooth out the contours or reveal a phase transition.

Local text and figure revision: Thank you for the suggestion. We conducted an additional ten random trials to average the traces and heatmaps, improving the clarity of the results now presented in Fig. 9.

L411: Note that there are earlier HSP models by Damasch and van Ooyen & van Pelt, that might be worth discussing here.

Local text revision: fixed.

L416 "beyond synaptic scaling" reference needed.

Local text revision: fixed.

L419: The biphasic rule was suggested by Butz already.

Local text revision: We adjusted the text to emphasize our contribution in suggesting/confirming the biphasic rule based on direct experimental observations.

L 419-44: Most of this is actually state-of-the art and may be better placed in the introduction to justify the use of NBQX as a competititve blocker.

Local text revision: We adjusted the text in the introduction and Discussion sections to cover the raised points.

L487: In my opinion, although scaling adapts the weights quickly, the information about deviating firing rate is still stored in the calcium signal such that it will also give rise to structural changes (although they may be small when the rate is low). Thus, I think that fast scaling does not abolish structural changes.

Local text revision: We adjusted the text to account for other factors that could lead to the same or opposite conclusions.

L502f: Sentence unclear. Do you mean Ca is an integrated (low-pass filtered) version of the firing rate?

Yes.

L504: What is the cumulative temporal effect of error in estimating firing rates?

We were referring to the potential instability in numeric simulations if the firing rate is not tracked by an integral signal (calcium concentration) but is instead estimated through average spike counts over time. In our model, calcium serves as a proxy for the firing rate to guide homeostatic structural plasticity. The intake and decay constants are set to minimize the accumulation of errors over time, making long-term error accumulation unlikely. In any case, this is not intended to be a precise measure of the firing rate but rather a smooth guide for homeostatic control.

Local text revision: We rewrote the section so as not to cause extra concerns.

L505: Which two rules are meant here? Ca- and firing rate based or HSP and scaling?

Local text revision: The two rules are the HSP rule and the HSS rule. We have adjusted the text to improve clarity.

L505ff: I did not really understand the control theoretic view here and Supp Fig 5 is not self-explaining enough to help. In my view, scaling is a proportional controller for the calcium level (the setpoint is defined for calcium and not firing rate). Also, all of the HSP rules do neither contain an integral nor a differential of the error and are thus nonlinear but proportional controllers in first approximation. If this part is supposed to stay in the manuscript, the supporting information should contain a more detailed mathematical explanation. Relevant previous work on homeostatic control by synaptic scaling and homeostatic rewiring, e.g. doi: 10.23919/ECC54610.2021.9655157 should be discussed

Local text revision: We have updated the last paragraph to increase clarity. The HSP and HSS rules are proportional and integral for neural activity, as neural firing rate homeostasis is the meaningful goal. However, it is also correct that the integral component is gone if we view calcium concentration as the goal or setpoint. This paper is discussed and cited in a paragraph above this one.

Reviewer #2 (Recommendations For The Authors):

I have some additional suggestions and questions for the authors, which I am presenting following the order of the figures.

Fig 1A: I'm a little bit puzzled by the timescales between Hebbian and homeostatic plasticity; a wealth of data suggests that Hebbian plasticity acts on a faster timescale than homeostatic plasticity, while Aii-Aiii implies the opposite. In lesion-induced degeneration, for instance, which is mentioned later by the authors, spine loss has been suggested to be Hebbian (LTD) while the subsequent recovery is homeostatic. Additionally, it will not be clear to the reader if the same stimulus could induce Hebbian and homeostatic plasticity, or why; the rest of the manuscript seems to imply that any stimulus could and would trigger homeostatic plasticity, which is not the case. Finally, there should be a mention somewhere that Hebbian structural plasticity also exists.

Local text and figure revision: We thank the reviewer for pointing out the time scale issue, which was not explicitly considered here and is now updated.

Fig. 2Bii: There is no significant difference at 200nm NBQX for sEPSC amplitude, contrary to what is stated in the text (line 136). Which one is it?

Local text revision: We thank the reviewer for pointing out the mistake. We have inspected the original statistical file and corrected the text.

Fig. 2F: The description of Fig. 2F in the text confused me for the longest time. I am still unsure why 200nm NBQX is described as leading to a general size increase when it follows the control line so closely, crosses 0 at the same point, and is even below the control line for the largest spine sizes. Similarly, 50um NBQX neatly overlaps with the control condition except for the smallest and largest spines, so the "shrinkage of middle-sized spines" doesn't seem different from the control condition. I also couldn't find any data supporting the statement that 50um NBQX increased only the size of "a small subset of large spines". Maybe the authors could clarify this section? I would also suggest adding statistics between the treatments at each spine size bin to support the claims, as they are central to the rest of the paper.

Importantly, there is no description of the normalization nor the quantification of the difference between days in the methods; I am assuming post-pre for the difference and (post-pre)/pre for the normalization, but this should be much more detailed in the methodology. I was happy to see the baseline raw spine sizes in Supplementary Fig. 1, and would also suggest adding the raw spine sizes after treatment for comparison.

Local text and figure revision: We have adjusted the text and figure to improve clarity.

Fig. 2G/S2A: a scale for the label sizes would be helpful. I would also like to have the same correlation for 50um NBQX treatment and the control condition (at least in the supplementary figures).

Local text and figure revision: We have adjusted the text and figure to improve clarity.

Fig. 2I: I might be missing something, but why is the activity line flat when there are changes in spine density and size?

Local text and figure revision: We have adjusted the text and figure to improve clarity.

Fig. 3C-D: they are referenced in the text as Fig. 1C-D (lines 188-194).

Local text revision: fixed.

Fig. 5: it is interesting that the biphasic model captures both spine loss and recovery, fitting well with lesion-induced degeneration and recovery. Does this mean that the model captures other types of plasticity, or does it suggest to the authors that both steps are homeostatic?

Indeed, the biphasic HSP rule captures two types of activity dependence. The pioneering work by Gallinaro and Rotter (2018) also demonstrated that the HSP rule, even in its monotonic/linear form, exhibits associative properties, which are typically associated with Hebbian plasticity.

Fig. 6A: This figure requires a more detailed legend - what are the various insets? Does the top right graph only have one curve because they are overlapping and the growth rules are the same for axons and dendrites?

Local text revision: fixed.

Fig. 6E: There is usually an overshoot when a stimulus is removed, in this case at the end of the silencing period (as shown in Fig. 1Aiii). Is there a reason why this is not recapitulated here? It shouldn't be as extreme as in the right panel so there should be no degeneration.

We agree that removing the stimulus would typically trigger an opposite homeostatic process. However, in this protocol, we aimed to emphasize the role of recurrency by presenting extreme cases to illustrate potential scenarios for the readers.

Local text revision: We revised this paragraph to walk the readers through the rationale better.

Fig. 6: the authors mention distance-dependent connectivity (line 268), but I couldn't find any data related to that statement. I was particularly curious about that aspect, so I would like to know what this statement is based on, especially as they touch again on the role of morphology in Fig. 8, and distance-dependent connectivity is more prominent in the discussion. On a similar note, would the authors have data from other layers of CA1 that would show similar or other rules? Please note that I am not asking to include these data in the present paper - I am just curious if these data exist (or if the experiments are considered).

Such an extensive dataset is included and thoroughly investigated in another study that has just been published in Lenz et al., 2023. We updated the reference in the revised text.

Fig. 7E top: the scalebar is missing.

Local text revision: fixed.

Fig. 8A: do the colors have meaning? If yes, please state them. Also indicate that the left two neurons are pyramidal cells from CA1 and the right neurons are granule cells from the dentate gyrus.

Local text revision: fixed.

Line 302: "reactive" should be "reactivate".

Local text revision: fixed.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Aging reduces tissue regeneration capacity, posing challenges for an aging population. In this study, the authors investigate impaired bone healing in aging, focusing on calvarial bones, and introduce a two-part rejuvenation strategy. Aging depletes osteoprogenitor cells and reduces their function, which hinders bone repair. Simply increasing the number of these cells does not restore their regenerative capacity in aged mice, highlighting intrinsic cellular deficits. The authors' strategy combines Wnt-mediated osteoprogenitor expansion with intermittent fasting, which remarkably restores bone healing. Intermittent fasting enhances osteoprogenitor function by targeting NAD+ pathways and gut microbiota, addressing mitochondrial dysfunction - an essential factor in aging. This approach shows promise for rejuvenating tissue repair, not only in bones but potentially across other tissues.

Strengths:

This study is exciting, impressive, and novel. The data presented is robust and supports the findings well.

Weaknesses:

As mentioned above the data is robust and supports the findings well. I have minor comments only.

We thank the reviewer for their enthusiastic and positive assessment of our study. We appreciate the recognition of the novelty and robustness of our data and findings. We have carefully considered the reviewer's comments and have revised the manuscript accordingly. We believe these revisions further strengthen the clarity and impact of our work.

Reviewer #2 (Public review):

Summary:

Reeves et al explore a model of bone healing in the context of aging. They show that intermittent fasting can improve bone healing, even in aged animals. Their study combines a 'bone bandage' which delivers a canonical Wnt signal with intermittent fasting and shows impacts on the CD90 progenitor cell population and the healing of a critical-sized defect in the calvarium. They also explore potential regulators of this process and identify mitochondrial dysfunction in the age-related decline of stem cells. In this context, by modulating NAD+ pathways or the gut microbiota, they can also enhance healing, hinting at an effect mediated by complex impacts on multiple pathways associated with cellular metabolism.

Strengths:

The study shows a remarkable finding: that age-related decreases in bone healing can be restored by intermittent fasting. There is ample evidence that intermittent fasting can delay aging, but here the authors provide evidence that in an already-aged animal, intermittent fasting can restore healing to levels seen in younger animals. This is an important finding as it may hint at the potential benefits of intermittent fasting in tissue repair.

Weaknesses:

The authors explore potential mechanisms by which the intermittent fasting protocol might impact bone healing. However, they do not identify a magic bullet here that controls this effect. Indeed, the fact that their results with intermittent fasting can be replicated by changing the gut microbiota or modulating fundamental pathways associated with NAD, suggests that there is no single mechanism that drives this effect, but rather an overall complex impact on metabolic processes, which may be very difficult to untangle.

We thank the reviewer for their positive assessment of our study and for highlighting the significant finding that intermittent fasting can restore age-related declines in bone healing. We appreciate the observation that our results suggest a complex interplay of metabolic processes rather than a single "magic bullet" mechanism. Indeed, the ability of gut microbiota modulation or NAD+ pathway targeting to replicate intermittent fasting's benefits underscores this complexity. While we recognize the challenges of disentangling these interconnected pathways, we believe our findings offer valuable insights into the multifaceted nature of intermittent fasting's impact on aged tissue repair. We hope this study serves as a foundation for future research aimed at identifying the individual contributions of these pathways and developing targeted therapeutic strategies.

Reviewer #3 (Public review):

Summary:

This study aims to address the significant challenge of age-related decline in bone healing by developing a dual therapeutic strategy that rejuvenates osteogenic function in aged calvarial bone tissue. Specifically, the authors investigate the efficacy of combining local Wnt3a-mediated osteoprogenitor stimulation with systemic intermittent fasting (IF) to restore bone repair capacity in aged mice. The highlights are:

(1) Novel Approach with Aged Models:

This pioneering study is among the first to demonstrate the rejuvenation of osteoblasts in significantly aged animals through intermitted fasting, showcasing a new avenue for regenerative therapies.

(2) Rejuvenation Potential in Aged Tissues:

The findings reveal that even aged tissues retain the capacity for rejuvenation, highlighting the potential for targeted interventions to restore youthful cellular function.

(3) Enhanced Vascular Health:

The study also shows that vascular structure and function can be significantly improved in aged tissues, further supporting tissue regeneration and overall health.<br /> Through this innovative approach, the authors seek to overcome intrinsic cellular deficits and environmental changes within aged osteogenic compartments, ultimately achieving bone healing levels comparable to those seen in young mice.

Strengths:

The study is a strong example of translational research, employing robust methodologies across molecular, cellular, and tissue-level analyses. The authors leverage a clinically relevant, immunocompetent mouse model and apply advanced histological, transcriptomic, and functional assays to characterise age-related changes in bone structure and function. Major strengths include the use of single-cell RNA sequencing (scRNA-seq) to profile osteoprogenitor populations within the calvarial periosteum and suture mesenchyme, as well as quantitative assessments of mitochondrial health, vascular density, and osteogenic function. Another important point is the use of very old animals (up to 88 weeks, almost 2 years) modelling the human bone aging that usually starts >65 yo. This comprehensive approach enables the authors to identify critical age-related deficits in osteoprogenitor number, function, and microenvironment, thereby justifying the combined Wnt3a and IF intervention.

Weaknesses:

One limitation is the use of female subjects only and the limited exploration of immune cell involvement in bone healing. Given the known role of the immune system in tissue repair, future studies including a deeper examination of immune cell dynamics within aged osteogenic compartments could provide further insights into the mechanisms of action of IF.

We thank the reviewer for their thorough summary and positive assessment of our study, particularly highlighting its translational nature, the robust methodologies employed, and the relevance of our aged animal model. We appreciate the insightful suggestion to include male subjects and to explore immune cell dynamics in future investigations.

We acknowledge the limitation of using only female mice in the current study and agree that future studies incorporating both sexes and investigating immune cell contributions within aged osteogenic compartments would offer valuable insights into the mechanisms underlying intermittent fasting and its impact on bone healing.

Our focus on female mice was informed by their distinct characteristics, including delayed healing and higher fracture risk (PMID: 37508423, PMID: 34434120). Importantly, female mice present a more challenging case for bone repair, making them a stringent test for evaluating the effectiveness of our rejuvenation approaches. Moreover, our research protocol, approved under animal license, adhered to ethical principles and the 3Rs, allowing us to reduce the number of animals required by focusing on a single sex.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The authors should provide a justification for the use of female mice in this study. Additionally, the section on animal methods should be expanded to align with ARRIVE guidelines.

We thank the reviewer for their valuable feedback. In response to the comment regarding the use of female mice, we have included a justification in the updated manuscript. As noted, female mice were selected for this study due to their distinct characteristics, such as delayed healing and higher fracture risk (PMID: 37508423, PMID: 34434120), which provide a more challenging model for evaluating bone repair strategies. We believe this made our study a stringent test of the efficacy of the rejuvenation approaches being investigated.

Additionally, we have revised the animal methods section to ensure it aligns with the ARRIVE guidelines.

(2) Intermittent fasting can influence circadian rhythms in various ways. In the RNA-seq data, do the authors observe any changes related to circadian rhythm pathways?

The reviewer raises an important point regarding the influence of intermittent fasting (IF) on circadian rhythms. Our RNA-seq data revealed significant alterations in circadian rhythm pathways, particularly within the aged periosteal CD90+ cell population during IF. Specifically, the PAR bZip family transcription factors Dbp, Hlf, and Tef (q < 0.05) were significantly upregulated, consistent with their established roles as circadian rhythm regulators (PMID: 16814730, PMID: 31428688).

In suture CD90+ cells from the Aged + IF group, Dbp expression was significantly elevated compared to the Aged AL control group. Moreover, several other circadian-controlled genes, including Sirt1, Kat2b, Csnk1e, Ezh2, Fbxw11, and Ucp2 (p < 0.05), were also upregulated (Fig. 4b), suggesting enrichment of Clock/Per2/Arntl transcriptional targets, essential components of the circadian clock.

The observed upregulation of circadian rhythm effectors like Dbp, Hlf, and Tef further suggests a potential role for circadian transcription in CD90+ cell rejuvenation and bone repair in aged mice. While previous studies have primarily focused on the role of circadian rhythms in osteoblasts in vitro (PMID: 34579752, PMID: 30290183), our findings provide compelling evidence for their involvement in bone regeneration in vivo, providing compelling evidence for future investigation into this mechanism.

Chip-SEQ studies have shown D-box sites near promoters in Wnt/β-catenin components (e.g. Lrp6, Lrp5, Wnt8a, Fzd4) in pro-osteogenic transcription factor Zbtb16 (and see Fig 5), and in 11 of the 44 mouse collagen genes (PMID: 31428688). These components are known to regulate osteogenesis, and their proximity to circadian-controlled transcription factors suggests a possible overlap between circadian regulation and Wnt signaling in promoting bone repair.  Additionally, circadian rhythmicity, stem cell function, and Wnt signaling are interlinked (PMID: 29277155, PMID: 25414671). Food intake is a powerful regulator of the circadian rhythm in several organs (PMID: 11114885, PMID: 32363197), but little is known about the diet-circadian interaction in bone repair. The possibility that circadian transcription can be harnessed to target Aged stem cell function towards bone repair is a promising prospect.

We have incorporated this information in Figure 2 - figure supplement 3G-H, the results section as well as in the discussion.

Reviewer #2 (Recommendations for the authors):

(1) The authors refer to 'altered cellular mechanobiology', 'age-related changes in mechanobiology', etc. Here, they are using this terminology to refer to changes in F-actin intensity and nuclear shape. While I agree that these measures are indicators of a cellular response to mechanical cues, calling this 'changes in mechanobiology' doesn't sound quite correct to me. 'Mechanobiology' to me, is a field of study. Perhaps the authors should consider changing their terminology.

We appreciate the reviewer’s insightful comment on the terminology used in our manuscript. We agree that the term "mechanobiology" is a broad field of study and using it in the context of changes in F-actin intensity and nuclear shape may be misleading. We have revised the text to better reflect the specific cellular responses to mechanical cues, such as changes in the cytoskeleton and nuclear morphology, rather than referring to them as "altered mechanobiology." The updated terminology more accurately conveys the observed cellular alterations in response to mechanical forces. We have made these adjustments throughout the manuscript for clarity and precision.

(2) Three of the measures the authors use to highlight age-related changes (and rejuvenation) in their animal model are F-actin intensity, nuclear shape, and vascularisation. However, they never really explain what they believe these readouts mean practically/functionally. Indeed, it makes sense that less vascularisation would be associated with an aged phenotype and preclude healing, but this is only mentioned somewhat cursorily in the discussion. While vascularisation is discussed in the context of aging in the discussion, it is not discussed in the context of healing (which would seem relevant in the context of vascularisation being used as a readout in the healing models in response to Akk and IF treatment). Similarly, the changes in F-actin intensity and nuclear shape might suggest changes in the stiffness of the periosteum (as mentioned in the discussion), which could indeed be an indicator of an aged phenotype; however, their role in healing (in response to Akk and IF) are not clearly articulated.

We appreciate the reviewer’s insightful comments and have made revisions to clarify the implications of age-related changes in vascularization, F-actin intensity, and nuclear shape, as well as the functional significance of these observations in the context of healing and rejuvenation.

Vascularization:

Vascularization and modulation of blood flow are critical for calvarial bone repair, as supported by multiple studies (e.g., PMID: 38032405, PMID: 21156316, PMID: 25640220). Early in the calvarial repair process, blood vessels grow independently of osteoprogenitor cells, establishing a supportive environment that promotes osteoprogenitor migration and subsequent ossification (PMID: 38834586). Furthermore, angiogenic vessels from the periosteum at defect edges contribute to creating a specialized microenvironment essential for bone healing (PMID: 38834586, PMID: 38032405). Compromised vascularization significantly impairs the healing of critical-sized calvarial defects (PMID: 29702250).

Our data reveal a decline in periosteal vascularization with age, potentially compromising this microenvironment and impairing repair in aged animals. Importantly, our findings indicate that intermittent fasting (IF) reverses this phenotype by restoring periosteal vascularization. This rejuvenation of the vascular microenvironment aligns with improved bone repair outcomes in aged mice subjected to IF. We have revised the manuscript to emphasize the importance of vascularization in healing and to highlight the role of IF in restoring this critical aspect of the bone healing microenvironment.

F-actin intensity and nuclear shape:

Age-related changes in F-actin intensity and nuclear shape are associated with increased tissue stiffness, a hallmark of aging. Tissue stiffness has been shown to impair progenitor cell function and hinder repair in various systems, including neuroprogenitors (PMID: 31413369). Softening the extra cellular matrix in aged tissues has been demonstrated to partially restore progenitor function and improve repair outcomes, as seen in the case of neuroprogenitors (PMID: 31413369). In our study, IF reversed age-associated changes in F-actin expression and nuclear shape, restoring these parameters to a phenotype resembling that of younger animals. This suggests that IF mitigates the mechanical changes associated with aging, reducing tissue stiffness and rejuvenating the periosteum to facilitate improved bone healing, similar to the outcomes observed in younger models.

Following the reviewer’s advice, we have revised the text to clearly articulate the correlations and interpretations of our data regarding tissue mechanics and bone repair. Thank you for highlighting these critical aspects.

(3) In relation to my point 2) on nuclear shape, there are reports that aging is linked to changes in Lamin B1. Have the authors considered this? It might provide a clearer link between their data and the tissue-level phenotypes they observe.

Thank you for your comment regarding the potential link between aging and changes in Lamin B1. Following your suggestion, we performed Lamin B1 immunostaining on samples from Young, Adult, Aged, and Aged + IF groups. However, no significant differences in Lamin B1 levels were observed across these groups. These findings indicate that changes in Lamin B1 in osteoprogenitors are not apparent during aging, suggesting that Lamin B1 alterations in the context of aging may be tissue- and cell-type-specific.

The new data was added in Figure 1 - figure supplement 2i-j.

(4) In the data associated with Figure 2, the authors find that in the aged mice, MMP9 expression is increased, but MMP2 expression is decreased. They associate the decrease in MMP2 expression with decreased migration, but the canonical function of MMP9 should be similar to that of MMP2. Are there tissue-specific differences in the activity of MMP2/9 that could account for this?

Thank you for the thoughtful comment. While both MMP-2 and MMP-9 are involved in ECM remodeling and share some overlapping canonical functions, their roles are context-dependent and exhibit tissue-specific differences that could explain the observed changes in aged mice. MMP-2 has been shown to play a critical role in maintaining the structural and functional integrity of flat bones, such as those in the craniofacial skeleton, by supporting bone remodeling (PMID: 17400654, PMID: 17440987, PMID: 16959767). The decreased expression of MMP-2 in aged mice may impair these local processes, leading to reduced migratory capacity of osteoprogenitors and contributing to aging-related changes in flat bone structure and function.

In contrast, MMP-9 is more prominently involved in long bone remodeling, particularly at the growth plate where it regulates hypertrophic chondrocyte turnover, vascularization, and ossification during endochondral bone formation (PMID: 21611966, PMID: 9590175, PMID: 23782745, PMID: 16169742 ). Additionally, MMP-2 and MMP-9 differ in their regulation of specific ECM substrates and their interactions with bone-resident cells, which may further drive divergent outcomes in distinct bone types. For example, MMP-9’s role in osteoclastogenesis and its regulation of ECM proteins like type I collagen could be more critical in long bones, while MMP-2’s involvement in fine-tuning ECM microarchitecture may hold greater importance in flat bones.

The increased expression of MMP-9 in aged calvarial osteoprogenitors may reflect a compensatory mechanism in response to the reduced MMP-2 activity, possibly in response to increased ECM turnover demands. Further studies examining the precise molecular pathways driving these changes in osteoprogenitors will help clarify the underlying mechanisms and their contributions to age-related alterations in flat bone structure and function.

(5) In lines 391-2, the authors conclude that the data from Figure 4 shows that "during IF, CD90 cells, despite being aged, are more capable of ECM modulation and migration". The authors certainly present evidence that this is true, but the RNAseq showed that the enriched GO terms were predominantly associated with immune responses ('response to cytokine') and the proliferation phenotype seems very strong. Therefore, I would suggest that this overarching statement regarding the findings be less focussed on this one aspect of the finding, which doesn't look to be the dominant phenotype of the cellular response. And indeed, the authors move on from here to explore a mechanism associated with metabolism, not specifically with ECM remodelling.

We greatly appreciate the reviewer insight regarding the interpretation of our findings, particularly the conclusion drawn from Figure 4.

In response, we have revised the conclusion to more accurately reflect these findings.

The revised text in the conclusion now reads: " Together, these findings suggest that IF rejuvenates aged CD90+ cells, in part, by enhancing proliferation, immune response, ECM remodeling, Wnt/β-catenin pathway, and metabolism, including increased ATP levels and decreased AMPK levels.”

We hope that this adjustment better aligns with your suggestion and provides a more accurate summary of the key findings.

(6) Fasting blood glucose levels are often cited as an indicator of metabolic health. Did the authors look at this in their animals who underwent the IF protocol? Could this have had an impact on the healing response?

We thank the reviewer for this insightful comment. Throughout our study, we have withdrawn blood from the animals for various analyses that were not included in this manuscript in order to maintain focus on the osteoprogenitors.

Our analysis included the assessment of the metabolic health of the animals using fasting blood glucose levels and the area under the curve (AUC) of the intraperitoneal glucose tolerance test (IPGTT).

Fasting blood glucose levels reflect the animals' ability to maintain stable glucose levels after fasting, while the AUC from the IPGTT measures how efficiently glucose is cleared from the bloodstream following a glucose challenge. Typically, lower fasting blood glucose levels and reduced AUC indicate improved insulin sensitivity, better glucose metabolism, and enhanced metabolic control (PMID: 18812462, PMID: 19638507).

Our findings show that intermittent fasting (IF) significantly reduced both the fasting blood glucose levels and the AUC in the IPGTT. This indicates that IF enhances metabolic flexibility, likely through improved insulin sensitivity and better glucose homeostasis. By lowering fasting blood glucose, IF reduces the reliance on excessive gluconeogenesis during fasting, while a reduced AUC indicates more efficient postprandial glucose clearance, consistent with enhanced insulin action and reduced fluctuations in blood glucose levels. The new data has been incorporated in Figure 3 - figure supplement 1d-g.

Methods:

“Blood glucose level measurement

Fasting blood glucose levels were measured (Accu-Check tests strips) from 6h fasting mice by blood sampling the tail vein. For intraperitoneal glucose tolerance test (IPGTT), glucose was injected intraperitoneally (2 g/kg), and the blood glucose levels were measured after 15, 30, 60 and 120 minutes.”

Improved metabolic health through lower fasting glucose and reduced AUC can have profound implications for tissue repair (PMID: 32809434). Stable glucose levels ensure a consistent energy supply for key cellular processes, such as cell proliferation, migration, and differentiation, which are essential for regeneration. Enhanced insulin sensitivity supports nutrient delivery to cells and reduces inflammation, creating an environment conducive to tissue healing. Additionally, intermittent fasting's ability to optimize glucose metabolism and regulate insulin secretion may enhance the function of stem and progenitor cells, further improving the tissue repair process (PMID: 28843700). Together, these findings suggest a mechanistic link between improved metabolic health and the enhanced healing observed in animals subjected to intermittent fasting.

(7) In Supplementary Figure 10, the authors look at bone remodelling by assessing TRAP staining, as an indicator of osteoclast activity. I'm not sure if these data add all that much to the study. The authors have looked at bone formation at a tissue level using microCT. Here, they look at bone resorption at a cellular level with the TRAP assay. Overall, this probably suggests more bone remodelling, but the TRAP assay on its own at the cellular level could also be interpreted as an osteoporosis-like phenotype. This is clearly not the case because the authors show robust bone healing by microCT. In short, as an isolated measure of osteoclast activity at the cellular level without cellular-level assays of osteoblast activity, the interpretation of these data is not that clear. The microCT speaks far more of the phenotype and is, in my opinion, sufficient to make this point.

We thank the reviewer for their comments regarding the interpretation of the TRAP staining data and its context within the study. We appreciate the concern that, without direct assays of osteoblast activity, the TRAP assay could lead to ambiguity.

We have shown that intermittent fasting significantly increases the number and function of osteoprogenitor cells, the precursors to osteoblasts. While we acknowledge that these data do not directly measure osteoblast numbers or activity, they strongly suggest an increased capacity for osteoblast differentiation and bone formation. This aligns with the microCT findings of robust bone structure and healing.

After careful consideration and given that the microCT and histology findings  already provide robust and comprehensive evidence for bone structure and healing, we have decided to remove the TRAP staining data from the manuscript. We believe this change simplifies the manuscript and strengthens its focus on the most impactful data.

(8) In the discussion, the authors make a number of links between aging and IF. However, one of the exciting conclusions of this manuscript is that IF aids in healing in aged animals. In this context, IF has not impacted the aging process itself because the animals have not experienced an IF protocol across their lifespan, but rather only after injury. In this context, perhaps the authors should also be focussing their discussion on evidence of the short-term response to IF rather than its effects on aging, which are longer-term.

We appreciate the reviewer's comment and agree that emphasizing the short-term effects of intermittent fasting is crucial. Our study is the first to examine this protocol in Aged animals.

To address this, we have revised the discussion and highlighted how short-term IF enhances metabolic health, promotes osteoprogenitor functionality, and supports bone remodeling, as observed in our study.

Reviewer #3 (Recommendations for the authors):

(1) The authors should clarify details on intermittent fasting protocols, especially regarding caloric intake differences between fasting and non-fasting days, to aid reproducibility.

We appreciate the reviewer's suggestions and have incorporated them by clarifying the relevant details. The new data are presented in Figure 3 - figure supplement 1a-c.

Methods:

“Caloric intake calculation

To assess the caloric intake of mice, the food was weighted when made available to the mice (Win), and when removed (Wout). The daily consumed food was calculated based on the weight difference (Win - Wout), then converted to kcal (1 g = 3.02 kcal, LabDiet, 5053), and expressed as kcal/mouse/day for each cage (n cage ³ 3 with 1 to 5 mice/cage).”

(2) Did the authors evaluate the effect of their intermittent fasting protocol on fasting blood glucose levels?

Following the reviewer comment we included two measurements: 1) Fasting blood glucose, which reflects the ability to maintain glucose homeostasis during fasting, and 2) fasting blood glucose levels and the area under the curve (AUC) of the intraperitoneal glucose tolerance test (IPGTT), which measures glucose clearance efficiency after a glucose challenge. Lower values for both typically indicate improved insulin sensitivity, glucose metabolism, and metabolic control.

Our findings demonstrate that intermittent fasting significantly reduced both fasting blood glucose and IPGTT AUC, suggesting enhanced metabolic flexibility, likely through improved insulin sensitivity and glucose homeostasis. Lower fasting blood glucose with IF indicates reduced reliance on gluconeogenesis during fasting, while a reduced AUC suggests more efficient postprandial glucose clearance, consistent with enhanced insulin action and reduced blood glucose fluctuations. This new data is included in Figure 3 - figure supplement 1.

Generally, the improved metabolic environment supports tissue repair by ensuring adequate energy for cell proliferation and migration, reducing inflammation, and promoting the function of stem cells involved in tissue regeneration. Thus, this outcome of intermittent fasting may create a more favorable environment for tissue repair, potentially accelerating the healing of damaged tissues and improving overall regenerative capacity.

(3) In Figure 1E-F, the nuclei have an interesting shape and the authors quantified F-actin. Given the role of lamin B in nuclear integrity, an analysis of lamin B expression and its structural integrity in aged osteoprogenitors could provide valuable insights into cellular aging mechanisms and their potential reversal with intermittent fasting.

In response to the reviewer's comment, we performed Lamin B1 immunostaining on samples from Young, Adult, Aged, and Aged + IF groups. We observed no significant differences in Lamin B1 levels across these groups. This suggests that age-related changes in Lamin B1 are not evident in osteoprogenitors and may be tissue- or cell-type specific. The new data was added in Figure 1 - figure supplement 2i-j.

(4) The authors should explain, in the main text or the methods section, why are they only using females in this study.

We appreciate the reviewer's comment regarding the use of female mice. Female mice were chosen for this study due to their delayed healing and higher fracture risk (PMID: 37508423, PMID: 34434120), presenting a more challenging model for evaluating bone repair strategies and providing a stringent test of our rejuvenation approaches. This justification has been added to the revised manuscript. The animal methods section has also been updated to comply with ARRIVE guidelines.

(5) This story stands alone and has an incredible amount of data. However, for a follow-up study, I would like to suggest consideration of including a broader analysis of immune cell involvement within the osteogenic compartments to strengthen the mechanistic understanding of IF's impact.

We thank the reviewer for this insightful suggestion. We agree that investigating the role of immune cells within the osteogenic compartments could provide valuable mechanistic insights into how intermittent fasting influences tissue regeneration. Immune cells are key mediators of inflammation and repair, and their interactions with osteoprogenitors and other cells in the bone healing environment likely contribute to IF's effects.

While our study focuses on IF's impact on osteoprogenitor function and tissue repair, we acknowledge the importance of future research exploring immune cell involvement. Techniques like single-cell RNA sequencing or flow cytometry could characterize immune cell populations and their functional states within osteogenic niches, allowing for a deeper understanding of immune-skeletal interactions during IF-mediated bone healing. We appreciate the reviewer highlighting this promising avenue for future research.

Minor corrections to the text and figures:

(1) References formatting should be revised (eg. line 41).

The reference formatting was corrected.

(2) Line 144 - what do the authors mean by p2 in the references?

Thank you for your comment, we corrected the error and removed p2 from the reference.

Author response:

Reviewer #1 (Public review):

The significance of the target molecule and mechanisms may help in understanding the molecular mechanisms of metformin.

We greatly appreciate the reviewer’s insightful comment regarding the significance of the target molecule and its mechanisms in understanding the molecular actions of metformin. ATP5I is responsible for the dimerization of the F₁F₀-ATPase(1-3). Hence, we propose conducting BN-PAGE followed by a western blot using the β-subunit of the F1 domain of F1F0-ATP synthase to investigate whether metformin affects its dimerization. This will provide a more direct evidence of the on target action of metformin on ATP5I. Due to the high abundance of F₁F₀-ATP synthase in cells and the slow ability of metformin to enter mitochondria, we plan to perform long-term treatments (3 and 6 days) with high concentrations of metformin (10 mM) to enhance the likelihood of detecting subtle yet biologically relevant shifts in the monomer and dimer populations. Prolonged exposure is expected to reveal the cumulative effects of metformin on F₁F₀-ATP synthase dimers/monomers ratio. We do not expect that metformin will totally mimic the cumulative effect of the dimerization as in ATP5I KO cells but we think it will be important to report to what extent this ratio is affected.

Reviewer #2 (Public review):

(1) The interpretation of the cellular co-localization of the biotin-biguanide conjugate with TOMM20 (Figure 1-D) as mitochondrial "accumulation" of the conjugate is overstated because it cannot exclude binding of the conjugate to the mitochondrial membrane. It would have been more convincing if additional incubations with the biotin-biguanide conjugate in combination with metformin had shown that metformin is competitive with the biotin-conjugate.

We appreciate the reviewer’s insightful comment and agree that the resolution provided by fluorescence microscopy makes it challenging to pinpoint the specific mitochondrial compartment where the biotin-biguanide conjugate localizes, even with additional markers such as TOMM20 antibodies for the inner mitochondrial membrane. While it remains a possibility that the conjugate binds to the mitochondrial surface, another plausible explanation is that the biotin moiety may facilitate entry into mitochondria through a biotin-specific transporter, adding further mechanistic intricacies. Furthermore, while a competition assay with metformin might help investigate interactions with mitochondrial targets and transporters (OCT family), it would not compete for biotin-mediated transport. Thus, while we acknowledge the reviewer’s suggestion, we believe such an experiment may not provide conclusive evidence regarding the conjugate’s mitochondrial localization or mechanism of entry. Instead, we will revise the manuscript to more accurately describe the findings as "mitochondrial association" rather than "mitochondrial accumulation," ensuring that our interpretation remains consistent with the resolution and limitations of the data presented.

(2) The manuscript reports the identification of 69 proteins by mass spectrometry of the pull-down assay of which 31 proteins were eluted by metformin. However, no Mass Spectrometry data is presented of the peptides identified. The methodology does not state the minimum number of peptides (1, 2?) that were used for the identification of the 31/69 proteins.

Concerning the mass spectrometry results, our intention was to provide a comprehensive table summarizing these findings in a separate data sheet, as part of the data availability section. To address the reviewer’s comment and ensure full transparency, we will include this table as supplementary material in the revised manuscript. Additionally, we will update the methodology section to explicitly state these criteria and ensure clarity regarding the identification process.

(3) The validation of ATP5I was based on the use of recombinant protein (which was 90% pure) for the SPR and the use of a single antibody to ATP5I. The validity of the immunoblotting rests on the assumption that there is no "non-specific" immunoactivity in the relevant mol wt range. Information on the validation of the antibody would be helpful.

Regarding the recombinant protein used for SPR, its purity was evaluated using a Coomassie-stained gel. For the antibody used in immunoblotting, its specificity was validated through knockout cell lines, ensuring minimal concerns about non-specific immunoactivity within the relevant molecular weight range. Unfortunately, the KO data comes in the paper after the first immunoblots are presented. In the revised manuscript, we will clearly outline these validation steps in the methods section and additional manufacturer documentation for the antibody we used.

(4) Knock-out of ATP5I markedly compromised the NAD/NADH ratio (Fig.3A) and cell proliferation (Figure 3D). These effects may be associated with decreased mitochondrial membrane potential which could explain the low efficacy of metformin (and most of the data in Figures 3-5). This possibility should be discussed. Effects of [metformin] on the NAD/NADH ratio in control cells and ATP5I-KO would have been helpful because the metformin data on cell growth is normalized as fold change relative to control, whereas the NAD/NADH ratio would represent a direct absolute measurement enabling comparison of the absolute effect in control cells with ATP5I KO.

The mitochondrial membrane potential depends on a functional electron transport chain which drives proton pumping from the matrix to the intermembrane space. Metformin can decrease the mitochondrial membrane potential and this usually explained as a consequence of complex I inhibition(4). It has been published the metformin requires this membrane potential to accumulate in mitochondria so the actions of metformin are self-limiting due to this requirement. The reviewer is right that ATP5I KO cells could be resistant to metformin because they may have a lower membrane potential. We do not believe this to be the case because the response to phenformin, another biguanide that can enter mitochondria through the membrane without the need of the OCT transporters(5), is also affected in ATP5IKO cells. Of note, compensatory mechanisms such as enhanced glycolysis, as observed in ATP5I-KO cells (elevated ECAR and increased sensitivity to 2-D-deoxyglucose), and the ATPase activity of F₁F₀-ATP synthase could potentially help maintain membrane potential suggesting that this might not be an issue in the ATP5I KO cells. We will discuss these possibilities in the revised manuscript.

Nevertheless, to experimentally address this point, we propose measuring mitochondrial membrane potential using tetramethylrhodamine methyl ester (TMRE) and ATP levels using luciferase-based assays (CellTiter-Glo) in ATP5I-KO cells.

Regarding the NAD+/NADH in both control and KO cells may not be very helpful because this ratio can be corrected by LDH which is induced as part of the glycolytic adaptation that occurs after inhibition of respiration. Since our KO cells have been propagated already for several passages, the extent of this adaptation is likely different from metformin-treated cells. As we mentioned in answering Reviewer 1, we will provide a more direct measurement of metformin acting on ATP5I: the levels of F1F0-ATPase dimers and monomers.

(5) Figure-6 CRISPR/Cas9 KO at 16mM metformin in comparison with 70nM rotenone and 2 micromolar oligomycin (in serum-containing medium). The rationale for the use of such a high concentration of metformin has not been explained. In liver cells metformin concentrations above 1mM cause severe ATP depletion, whereas therapeutic (micromolar) concentrations have minimal effects on cellular ATP status. The 16mM concentration is ~2 orders of magnitude higher than therapeutic concentrations and likely linked to compromised energy status. The stronger inhibition of cell proliferation by 16mM metformin compared with rotenone or oligomycin raises the issue of whether the changes in gene expression may be linked to the greater inhibition of mitochondrial metabolism. Validation of the cellular ATP status and NAD/NADH with metformin as compared with the two inhibitors could help the interpretation of this data.

To address the reviewer’s final comment, we would like to clarify the rationale behind our experimental approach. NALM-6 cells are very glycolytic, have low respiration rates, and weak dependence on ATP5I (DepMap score: -0.47)(6). The concentration of 16 mM metformin was chosen based on the IC50 for this cell line. This approach aligns with our focus on the anticancer mechanism of action rather than the antidiabetic effects of metformin. Both ATP status and NAD+/NADH ratios will depend on the extent of the compensatory glycolysis. On the other hand, our genetic screening evaluates cell proliferation as an integration of all metabolic activities required for the process. This unbiased screening revealed a common pathway affected by metformin and oligomycin different that the pathway affected by rotenone, which is consistent with the finding that metformin acts of the F₁F₀ATPase.

Reviewer #3 (Public review):

(1) Most of the data are based on measurements of the oxygen consumption rate (OCR) and extracellular acidification rate (ECAR) measured by the Seahorse analyser in control and ATP5l KO cells. However, these measurements are conducted by a single injection of a biguanide, followed over time and presented as fold change. By doing so, the individual information on the effect of metformin and derivate on control and KO cells are lost. In addition, the usual measurement of OCR is coupled with certain inhibitors and uncouplers, such as oligomycin, FCCP, and Antimycin A/rotenone, to understand the contribution of individual complexes to respiration. Since biguanides and ATP5l KO affect protein levels of components of complex I and IV, it would be informative to measure their individual contributions/effects in the Seahorse. To further strengthen the data, it would be helpful to obtain measurements of actual ATP levels in these cells, as this would explain the activation of AMPK.

We appreciate the reviewer’s observations regarding the Seahorse measurements and acknowledge the potential limitations of presenting the data as fold change. Due to experimental challenges in maintaining KP-4 and ATP5I-KO cells with sufficient nutrients, caused by their rapid glucose uptake and subsequent lactate production, it was more practical to present the Seahorse results in this format. Using inhibitors at each time point during the Seahorse experiment was not feasible, as the delay between inhibitor injections and the corresponding changes in oxygen consumption rate (OCR) and extracellular acidification rate (ECAR) would introduce variability and complicate the interpretation of dynamic responses. Nevertheless, we recognize the importance of understanding the contributions of specific respiratory complexes to OCR and ECAR. To address this, we will include a representative figure showcasing a typical Seahorse analysis, highlighting ATP turnover and proton leak after oligomycin addition, maximal respiration with FCCP, and disruption with rotenone and antimycin A. While these experiments are inherently complex due to the metabolic demands of ATP5I-KO cells, this approach will provide a clearer breakdown of mitochondrial activity. Furthermore, as mentioned in our response to Reviewer 2, we will measure ATP levels using a luciferase-based assay (CellTiter-Glo) in both control and ATP5I-KO cells to better explain AMPK activation. This will provide additional context to strengthen the interpretation of mitochondrial function and metabolic compensation mechanisms in these cells.

(2) The authors report on alterations in mitochondrial morphology upon ATP5l KO, which is measured by subjective quantifications of filamentous versus puncta structures. Fiji offers great tools to quantify the mitochondrial network unbiasedly and with more accuracy using deconvolution and skeletonization of the mitochondria, providing the opportunity to measure length, shape, and number quantitatively. This will help to understand better, whether mitochondria are really fragmented upon ATP5l KO and rescued by its re-introduction.

Concerning the analysis of mitochondrial morphology, we acknowledge the potential benefits of using Fiji and additional plugins such as MiNA for more accurate and unbiased quantification. Indeed, this approach could provide stronger evidence for mitochondrial fragmentation upon ATP5I-KO and its potential rescue by ATP5I reintroduction. We will consider integrating this methodology into our analysis to enhance the precision and robustness of our findings.

(3) Finally, the authors report in the last part of the paper a genetic CRISPR/Cas9 KO screen in NALM-6 cells cultured with high amounts of metformin to identify potential new mediators of metformin action. It is difficult to connect that to the rest of the paper because a) different concentrations of metformin are used and b) the metabolic effects on energy consumption are not defined. They argue about the molecular function of the obtained hits based on literature and on a comparison of the pattern of genetic alterations based on treatments with known inhibitors such as oligomycin and rotenone. However, a direct connection is not provided, thus the interpretation at the end of the results that "the OMA1-DEL1-HRI pathway mediates the antiproliferative activity of both biguanides and the F1ATPase inhibitor oligomycin" while increasing glycolysis, needs to be toned down. This is an interesting observation, but no causality is provided. In general, this part stands alone and needs to be better connected to the rest of the paper.

NALM-6 are very glycolytic, have low respiration rates, and weak dependence on ATP5I(6), forcing us to use higher concentrations of metformin to inhibit their growth. Recent results show that metformin targets PEN2 in the cytosol to increase AMPK activity, controlling both the glucose lowering and the life span extension abilities of metformin 7. This work raises the question whether the antiproliferative and anticancer effects of metformin are due to a mitochondrial activity or are controlled by this new pathway of AMPK activation. Hence, the genetic screening was performed to unbiasedly find how metformin works. The results provide compelling evidence for mitochondria and in particular the ATP synthase as potential targets of metformin and a foundation for future studies. We will revise the text and abstract to better reflect the exploratory nature of this finding and ensure clarity.

(1) Paumard, P. et al. Two ATP synthases can be linked through subunits i in the inner mitochondrial membrane of Saccharomyces cerevisiae. Biochemistry 41, 10390-10396 (2002). https://doi.org/10.1021/bi025923g

(2) Paumard, P. et al. The ATP synthase is involved in generating mitochondrial cristae morphology. EMBO J 21, 221-230 (2002). https://doi.org/10.1093/emboj/21.3.221

(3) Habersetzer, J. et al. ATP synthase oligomerization: from the enzyme models to the mitochondrial morphology. Int J Biochem Cell Biol 45, 99-105 (2013). https://doi.org/10.1016/j.biocel.2012.05.017

(4) Xian, H. et al. Metformin inhibition of mitochondrial ATP and DNA synthesis abrogates NLRP3 inflammasome activation and pulmonary inflammation. Immunity 54, 1463-1477 e1411 (2021). https://doi.org/10.1016/j.immuni.2021.05.004

(5) Hawley, S. A. et al. Use of cells expressing gamma subunit variants to identify diverse mechanisms of AMPK activation. Cell metabolism 11, 554-565 (2010). https://doi.org/10.1016/j.cmet.2010.04.001

(6) Hlozkova, K. et al. Metabolic profile of leukemia cells influences treatment efficacy of L-asparaginase. BMC Cancer 20, 526 (2020). https://doi.org/10.1186/s12885-020-07020-y

(7) Ma, T. et al. Low-dose metformin targets the lysosomal AMPK pathway through PEN2. Nature 603, 159-165 (2022). https://doi.org/10.1038/s41586-022-04431-8

Author response:

We thank the reviewers for taking the time to read and critically assess our manuscript.

We agree with the main points and they will be addressed in both writing and in additional experiments in a revised version of the paper.

The shared and major point of criticism are non-conclusive metabolomic data that indicate the bc1-complex in T. gondii as a MMV1028806 target tachyzoites and bradyzoites. Regarding the former, our conclusion was mainly based on both metabolite abundance changes that are observed after treatment with one bona-fide bc1-complex inhibitor atovaquone and also steady-state stable isotope incorporation patterns. While it is true that secondary effects of metabolic inhibition occur and are often dominant, isotope labelling equilibria take more time to establish and may reflect more accurately blocked metabolic reactions i.e. the primary target.

Regardless, we will follow the excellent suggestions to functionally assay particular mitochondrial electron transfer reactions to corroborate or revise our conclusions regarding the primary MMV1028806 target.

For more details please refer the full author responses that will accompany the revised manuscript.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

Sun et al. are interested in how experience can shape the brain and specifically investigate the plasticity of the Toll-6 receptor-expressing dopaminergic neurons (DANs). To learn more about the role of Toll-6 in the DANs, the authors examine the expression of the Toll-6 receptor ligand, DNT-2. They show that DNT-2 expressing cells connect with DANs and that loss of function of DNT-2 in these cells reduces the number of PAM DANs, while overexpression causes alterations in dendrite complexity. Finally, the authors show that alterations in the levels of DNT-2 and Toll-6 can impact DAN-driven behaviors such as climbing, arena locomotion, and learning and long-term memory.

Strengths:

The authors methodically test which neurotransmitters are expressed by the 4 prominent DNT-2 expressing neurons and show that they are glutamatergic. They also use Trans-Tango and Bac-TRACE to examine the connectivity of the DNT-2 neurons to the dopaminergic circuit and show that DNT-2 neurons receive dopaminergic inputs and output to a variety of neurons including MB Kenyon cells, DAL neurons, and possibly DANS.

We are very pleased that Reviewer 1 found our connectivity analysis a strength.

Weaknesses:

(1) To identify the DNT-2 neurons, the authors use CRISPR to generate a new DN2-GAL4.

They note that they identified at least 12 DNT-2 plus neurons. In Supplementary Figure 1A, the DNT-2-GAL4 driver was used to express a UAS-histoneYFP nuclear marker. From these figures, it looks like DNT-2-GAL4 is labeling more than 12 neurons. Is there glial expression?

Indeed, we claimed that DNT-2 is expressed in at least 12 neurons (see line 141, page 6 of original manuscript), which means more than 12 could be found. The membrane tethered reporters we used – UAS-FlyBow1.1, UASmcD8-RFP, UAS-MCFO, as well as UAS-DenMark:UASsyd-1GFP – gave a consistent and reproducible pattern. However, with DNT-2GAL4>UAS-Histone-YFP more nuclei were detected that were not revealed by the other reporters. We have found also with other GAL4 lines that the patterns produced by different reporters can vary. This could be due to the signal strength (eg His-YFP is very strong) and perdurance of the reporter (e.g. the turnover of His-YFP may be slower than that of the other fusion proteins).

We did not test for glial expression, as it was not directly related to the question addressed in this work.

(2) In Figure 2C the authors show that DNT-2 upregulation leads to an increase in TH levels using q-RT-PCR from whole heads. However, in Figure 3H they also show that DNT-2 overexpression also causes an increase in the number of TH neurons. It is unclear whether TH RNA increases due to expression/cell or the number of TH neurons in the head.

Figure 3H shows that over-expression of DNT-2 FL increased the number of Dcp1+ apoptotic cells in the brain, but not significantly (p=0.0939). The ability of full-length neurotrophins to induce apoptosis and cleaved neurotrophins promote cell survival is well documented in mammals. We had previously shown that DNT-2 is naturally cleaved, and that over-expression of DNT-2 does not induce apoptosis in the various contexts tested before (McIlroy et al 2013 Nature Neuroscience; Foldi et al 2017 J Cell Biol; Ulian-Benitez et al 2017 PLoS Genetics). Similarly, throughout this work we did not find DNT-2FL to induce apoptosis.

Instead, in Figure 3G we show that over-expression of DNT-2FL causes a statistically significant increase in the number of TH+ cells. This is an important finding that supports the plastic regulation of PAM cell number. We thank the Reviewer for highlighting this point, as we had forgotten to add the significance star in the graph. In this context, we cannot rule out the possibility that the increase in TH mRNA observed when we over-express DNT-2FL could not be due to an increase in cell number instead. Unfortunately, it is not possible for us to separate these two processes at this time. Either way, the result would still be the same: an increase in dopamine production when DNT-2 levels rise.

We have now edited the abstract lines 38-39 adding that “By contrast, over-expressed DNT-2 increased DAN cell number,…”, within the main text in Results page 10 lines 259-265 and in the Discussion section page 15 lines 391, 393-396.

(3) DNT-2 is also known as Spz5 and has been shown to activate Toll-6 receptors in glia (McLaughlin et al., 2019), resulting in the phagocytosis of apoptotic neurons. In addition, the knockdown of DNT-2/Spz5 throughout development causes an increase in apoptotic debris in the brain, which can lead to neurodegeneration. Indeed Figure 3H shows that an adult specific knockdown of DNT-2 using DNT2-GAL4 causes an increase in Dcp1 signal in many neurons and not just TH neurons.

Indeed, we did find Dcp1+ TH-negative cells too (although not widely throughout the brain), although this is not shown in the images of Figure 3H where we showed only TH+ Dcp+ cells.

That is not surprising, as DNT-2 neurons have large arborisations that can reach a wide range of targets; DNT-2 is secreted, and could reach beyond its immediate targets; Toll-6 is expressed in a vast number of cells in the brain; DNT-2 can bind promiscuously at least also Toll-7 and other Keks, which are also expressed in the adult brain (Foldi et al 2017 J Cell Biology; Ulian-Benitez et al 2017 PLoS Genetics; Li et al 2020 eLife). Together with the findings by McLaughlin et al 2019, our findings further support the notion that DNT-2 is a neuroprotective factor in the adult brain. It will be interesting to find out what other neuron types DNT-2 maintains.

We have made some edits on these points in page 10 lines 259-265.

We would like to thank Reviewer 1 for their positive comments on our work and their interesting and valuable feedback.

Reviewer #2 (Public review):

This paper examines how structural plasticity in neural circuits, particularly in dopaminergic systems, is regulated by Drosophila neurotrophin-2 (DNT-2) and its receptors, Toll-6 and Kek-6. The authors show that these molecules are critical for modulating circuit structure and dopaminergic neuron survival, synaptogenesis, and connectivity. They show that loss of DNT-2 or Toll-6 function leads to loss of dopaminergic neurons, dendritic arborization, and synaptic impairment, whereas overexpression of DNT-2 increases dendritic complexity and synaptogenesis. In addition, DNT-2 and Toll-6 modulate dopamine-dependent behaviors, including locomotion and long-term memory, suggesting a link between DNT-2 signaling, structural plasticity, and behavior.

A major strength of this study is the impressive cellular resolution achieved. By focusing on specific dopaminergic neurons, such as the PAM and PPL1 clusters, and using a range of molecular markers, the authors were able to clearly visualize intricate details of synapse formation, dendritic complexity, and axonal targeting within defined circuits. Given the critical role of dopaminergic pathways in learning and memory, this approach provides a good opportunity to explore the role of DNT-2, Toll-6, and Kek-6 in experience-dependent structural plasticity. However, despite the promise in the abstract and introduction of the paper, the study falls short of establishing a direct causal link between neurotrophin signaling and experience-induced plasticity.

Simply put, this study does not provide strong evidence that experience-induced structural plasticity requires DNT-2 signaling. To support this idea, it would be necessary to observe experience-induced structural changes and demonstrate that downregulation of DNT-2 signaling prevents these changes. The closest attempt to address this in this study was the artificial activation of DNT-2 neurons using TrpA1, which resulted in overgrowth of axonal arbors and an increase in synaptic sites in both DNT-2 and PAM neurons. However, this activation method is quite artificial, and the authors did not test whether the observed structural changes were dependent on DNT-2 signaling. Although they also showed that overexpression of DNT-2FL in DNT-2 neurons promotes synaptogenesis, this phenotype was not fully consistent with the TrpA1 activation results (Figures 5C and D).

In conclusion, this study demonstrates that DNT-2 and its receptors play a role in regulating the structure of dopaminergic circuits in the adult fly brain. However, it does not provide convincing evidence for a causal link between DNT-2 signaling and experience-dependent structural plasticity within these circuits.

We would like to thank Reviewer 2 for their very positive assessment of our approach to investigate structural circuit plasticity. We are delighted that this Reviewer found our cellular resolution impressive. We are also very pleased that Reviewer 2 found that our work demonstrates that DNT-2 and its receptors regulate the structure of dopaminergic circuits in the adult fly brain. This is already a very important finding that contributes to demonstrating that, rather than being hardwired, the adult fly brain is plastic, like the mammalian brain. Furthermore, it is remarkable that this involves a neurotrophin functioning via Toll and kinase-less Trks, opening an opportunity to explore whether such a mechanism could also operate in the human brain.

We are very pleased that this Reviewer acknowledges that this work provides a good opportunity to explore the role of DNT-2, Toll-6, and Kek-6 in experience-dependent structural plasticity. We provide a molecular mechanism and proof of principle, and we demonstrate a direct link between the function of DNT-2 and its receptors in circuit plasticity. We also showed a link of DNT-2 to neuronal activity, as neuronal activity increased the production of DNT-2GFP, induced the cleavage of DNT-2 and a feedback loop between DNT-2 and dopamine, and both neuronal activity and increased DNT-2 levels promoted synaptogenesis.

As the Reviewer acknowledges this approach provides a good opportunity to explore the role of DNT-2, Toll-6, and Kek-6 in experience-dependent structural plasticity. Finding out the direct link in response to lived experience is a big task, beyond the scope of this manuscript, and we will be testing this with future projects. Nevertheless, it is important to place our findings within this context together with the link to mammalian neurotrophins (as explained in the discussion), as it is here where the findings have deep and impactful implications.

To accommodate the criticism of this Reviewer, we have now toned down our narrative. This does not diminish the importance of the findings, it makes the argument more stringent. Please see edits in: Abstract page 2 lines 42-44; and Discussion page 22 line 586 – which were the only points were a direct claim had been made.

We would like to thank Reviewer 2 for the positive and thoughtful evaluation of our work, and for their feedback.

Reviewer #3 (Public review):

Summary:

The authors used the model organism Drosophila melanogaster to show that the neurotrophin Toll-6 and its ligands, DNT-2 and kek-6, play a role in maintaining the number of dopaminergic neurons and modulating their synaptic connectivity. This supports previous findings on the structural plasticity of dopaminergic neurons and suggests a molecular mechanism underlying this plasticity.

Strengths:

The experiments are overall very well designed and conclusive. Methods are in general state-of-the-art, the sample sizes are sufficient, the statistical analyses are sound, and all necessary controls are in place. The data interpretation is straightforward, and the relevant literature is taken into consideration. Overall, the manuscript is solid and presents novel, interesting, and important findings.

We are delighted that Reviewer 3 found our work solid, novel, interesting and with important findings. We are also very pleased that this Reviewer found that all necessary controls have been carried out.

Weaknesses:

There are three technical weaknesses that could perhaps be improved.

First, the model of reciprocal, inhibitory feedback loops (Figure 2F) is speculative. On the one hand, glutamate can act in flies as an excitatory or inhibitory transmitter (line 157), and either situation can be the case here. On the other hand, it is not clear how an increase or decrease in cAMP level translates into transmitter release. One can only conclude that two types of neurons potentially influence each other.

Thank you for pointing out that glutamate can be inhibitory. In response, we have removed the word ‘excitatory’ from the only point it had been used in the text: page 7 line 167.

In mammals, the neurotrophin BDNF has an important function in glutamatergic synapses, thus we were intrigued by a potential evolutionary conservation. Our evidence that DNT-2A neurons could be excitatory is indirect, yet supportive: exciting DNT-2 neurons with optogenetics resulted in an increase in GCaMP in PAMs (data not shown); over-expression of DNT-2 in DNT-2 neurons increased TH mRNA levels; optogenetic activation of DNT-2 neurons results in the Dop2R-dependent downregulation of cAMP levels in DNT-2 neurons. Dop2R signals in response to dopamine, which would be released only if dopaminergic neurons had been excited. Accordingly, glutamate released from DNT-2 neurons would have been rather unlikely to inhibit DANs.

cAMP is a second messenger that enables the activation of PKA. PKA phosphorylates many target proteins, amongst which are various channels. This includes the voltage gated calcium channels located at the synapse, whose phosphorylation increases their opening probability. Other targets regulate synaptic vesicle release. Thus, a rise in cAMP could facilitate neurotransmitter release, and a downregulation would have the opposite effect. Other targets of PKA include CREB, leading to changes in gene expression. Conceivably, a decrease in PKA activity could result in the downregulation of DNT-2 expression in DNT-2 neurons. This negative feedback loop would restore the homeostatic relationship between DNT-2 and dopamine levels.

We agree with this Reviewer that whereas our qRT-PCR data show that over-expression of DNT-2 increases TH mRNA levels, this does not demonstrate that originates from PAM neurons. Similarly, although our EPAC data imply that dopamine must be released from DANs and received by DNT-2 neurons to explain those data, the evidence did not include direct visualisation of dopamine release in response to DNT-2 neuron activation. To accommodate these criticisms, we have edited the summary Figure 2E adding question marks to indicate inference points and page 9 line 221.

Our data indeed demonstrate that DNT-2 and PAM neurons influence each other, not potentially, but really. We have provided data that: DNT-2 and PAMs are connected through circuitry; that the DNT-2 receptors Toll-6 and kek-6 are expressed in DANs, including in PAMs; that alterations in the levels of DNT-2 (both loss and gain of function) and loss of function for the DNT-2 receptors Toll-6 and Kek-6 alter PAM cell number, alter PAM dendritic complexity and alter synaptogenesis in PAMs; alterations in the levels of DNT-2, Toll-6 and kek-6 in adult flies alters dopamine dependent behaviours of climbing, locomotion in an arena and learning and long-term memory. These data firmly demonstrate that the two neuron types DNT-2 and PAMs influence each other.

We have also shown that over-expression of DNT-2 in DNT-2 neurons increases TH mRNA levels, whereas activation of DNT-2 neurons decreases cAMP levels in DNT-2 neurons in a dopamine/Dop2R-dependent manner. These data show a functional interaction between DNT-2 and PAM neurons.

Second, the quantification of bouton volumes (no y-axis label in Figure 5 C and D!) and dendrite complexity are not convincingly laid out. Here, the reader expects fine-grained anatomical characterizations of the structures under investigation, and a method to precisely quantify the lengths and branching patterns of individual dendritic arborizations as well as the volume of individual axonal boutons.

Figure 5C, D do contain Y-axis labels, all our graphs in main manuscript and in supplementary files contain Y-axis labels.

In fact, we did use a method to precisely quantify the lengths and branching patterns of individual dendritic arborisations, volume of individual boutons and bouton counting. These analyses were carried out using Imaris software. For dendritic branching patterns, the “Filament Autodetect” function was used. Here, dendrites were analysed by tracing semi-automatically each dendrite branch (ie manual correction of segmentation errors) to reconstruct the segmented dendrite in volume. From this segmented dendrite, Imaris provides measurements of total dendrite volume, number and length of dendrite branches, terminal points, etc. For bouton size and number, we used the Imaris “Spot” function. Here, a threshold is set to exclude small dots (eg of background) that do not correspond to synapses/boutons. All samples and genotypes are treated with the same threshold, thus the analysis is objective and large sample sizes can be analysed effectively. We had already provided a description of the use of Imaris in the methods section.

We have now exapanded the protocol on how we use Imaris to analyse dendrites and synapses, in: Materials and Methods section, page 28 lines 756-768 and page 29 lines 778-799.

Third, Figure 1C shows two neurons with the goal of demonstrating between-neuron variability. It is not convincingly demonstrated that the two neurons are actually of the very same type of neuron in different flies or two completely different neurons.

We thank Reviewer 3 for raising this interesting point. It is not possible to prove which of the four DNT-2A neurons per hemibrain, which we visualised with DNT-2>MCFO, were the same neurons in every individual brain we looked at. This is because in every brain we have looked at, the soma of the neurons were not located in exactly the same location. Furthermore, the arborisation patterns are also different and unique, for each individual brain. Thus, there is natural variability in the position of the soma and in the arborisation patterns. Such variability presumably results from the combination of developmental and activity-dependent plasticity. Importantly, for every staining we carried out using DNT-2GAL4 and various membrane reporters and MCFO clones, we never found two identical DNT-2 neuron profiles.

To increase the evidence in support of this point, we have now expanded Figure 1, adding one more image of DNT-2>FlyBow (Figure 1A) and two more images of DNT-2>MCFO (Figure 1D). In total, seven images in Figure 1 and two further images in Figure 5A demonstrate the variability of DNT-2 neurons.

We would like to thank Reviewer 3 for the very positive evaluation of our work and the interesting and valuable feedback.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

In the fly list, several fly lines are missing references and sources. 

Apologies for this over-sight, this has now been corrected.

We thank Reviewer 1 for their effort and time to scrutinise our work, and for their very positive and helpful feedback.

Reviewer #2 (Recommendations for the authors):

(1) Here I provide some more specific comments that I hope will help the authors further improve the study.

(2) L148: "single neuron clones revealed variability in the DNT-2A". How do the authors know that they are labeling the same subtype of DNT-2A neurons? 

There are four anterior DNT-2A cells per hemibrain, that project from the SOG area to the SMP. It is not possible to verify that every time we look at exactly the same neuron, because the exact position of the somas and the arborisation patterns vary from brain to brain. We know this from two sources of data: (1) when using DNT-2GAL4 to visualise the expression of membrane reporters (e.g. UAS-FlyBow, UAS-mCD8-GFP, UAS-CD8-RFP) no brain ever showed a pattern identical to that of another brain, neither in the exact position of the somas nor in the exact arborisation patterns. (2) When we generated DNT-2>MCFO clones to visualise 1-2 cells at a time, no single neuron or 2-neuron clones ever showed an identical pattern. The most parsimonious interpretation is that the exact location of the somas and the exact arborisation patterns vary across individual flies. Developmental variability in neuronal patterns has also been reporter by Linneweber et al (2020) Science.

To make our evidence more compelling, and in response to this Reviewer’s query, we have now added further images. Please find in revised Figure 1 A,B three examples of three different brains expressing DNT-2>FlyBow1.1. In Figure 1D, two more examples (altogether 4) of DNT-2>MCFO clones. Here it is clear to see that no neuron shape is identical to that of others, demonstrating variability in individual fly brains. We now show four images in Figure 1 and two more in Figure 5A that demonstrate the variability of DNT-2A neurons.

(3) Figure 1E: Are all DNT-2A neurons positive for vGlut and Dop2R? This figure shows only two DNT-2A neurons. 

Yes, all four DNT-2A neurons per hemibrain are vGlut positive and we have now added more images to Supplementary Figure S1A (right), also showing that presynaptic DNT-2A endings at SMP also coincide with a vGlut+ domain (Figure S1A left).

Yes, all all four DNT-2A neurons per hemibrain are Dop2R positive and we have now added more images to Supplementary Figure S1B.

(4) L156: Glutamate is generally considered to be inhibitory in the adult fly brain. More evidence is needed before the authors can claim that "DNT-2A neurons are excitatory glutamatergic neurons". 

Thank you for pointing this out. Although our data do not conclusively demonstrate it, they are consistent with DNT-2A neurons being excitatory. BDNF is most commonly released from glutamatergic neurons in mammals, its release is activity-dependent and leads to formation and stabilisation of synapses.  The phenotypes we have observed are consistent with this and reveal functional evolutionarily conservation: (1) exciting DNT-2 neurons with TrpA1 results in increased production and cleavage of DNT-2GFP and de novo synaptogenesis; (2) over-expression of DNT-2 in the adult induces de novo synaptogenesis; (3) down-regulation or loss of DNT-2 and its receptors Toll-6 and Kek-6 impair synaptogenesis. Furthermore, we show that DNT-2 dependent synaptogenesis is between DNT-2 and dopaminergic neurons, which are involved in the control of locomotion, reward learning and long-term memory, and dopamine itself is required for such behaviour. Consistently with this we found that: (1) over-expression of DNT-2 increases TH mRNA levels, which would lead to the up-regulation of dopamine production; (2) exciting DNT-2 neurons increases locomotion speed in an arena; (3) knock-down of DNT-2 and its receptors decreases locomotion, whereas over-expression of DNT-2 increases locomotion; (4) over-expression of DNT-2 increases learning and long-term memory. Finally, in a previous version in bioRxiv, we also showed using optogenetics and calcium imaging that exciting DNT-2 neurons induced GCaMP signalling in their output PAM neurons, and in this version we show that exciting DNT-2 neurons regulates cAMP in DNT-2 neurons via dopamine-release dependent feedback. Altogether, the most parsimonious interpretation of these data is that vGlut+ DNT-2 neurons are excitatory.

In any case, to address this reviewer’s point, we have now removed the word ‘excitatory’ from page 7 line 167.

(5) Figure 1H, I: A more detailed description of the Toll-6 and Kek-6 expressing neurons will be helpful. Are they expressed in specific types of PAM and PPL1 DANs? The legend in Figure S2 mentions labeling in γ2α′1 zones, but it seems to be more than that.

This information had been already provided, presumable this Reviewer overlooked this. This was already described in great detail by comparing our microscopy data with the single cell RNA-seq data available through Fly Cell Atlas (https://flycellatlas.org) and Scope (https://scope.aertslab.org/#/b77838f4-af3c-4c37-8dd9-cf7a41e4b034/*/welcome).

Please see our previously submitted Table S1 “Expression of Tolls, keks and Toll downstream adaptors in cells related to DNT-2A neurons”.

(6) Figure S3 should be controls for Figure 2A. It is incorrectly labeled as controls for Figure 3A. 

Thank you for pointing out this typo, this has now been corrected.

(7) L197: The authors state, "This showed that DNT-2 could stimulate dopamine production in neighboring DANs". However, the results do not fully support this conclusion because the experiments measure overall TH levels in the brain, not specifically in neighboring DANs. The observed effect could be indirect via other neurons. 

Indeed, we have now edited the text to: “This showed that DNT-2 could stimulate dopamine production”: page 8 line 208.

(8) Figure 3: If Toll-6 is expressed in specific subtypes of PAM DANs, are they the dying cells when Toll-6 was knocked down? I think the paper will be significantly improved if the authors provide a more in-depth analysis of the phenotype. Also, permissive temperature controls are missing for the experiments in (E)-(H). Permissive controls are essential to confirm that the observed effects are due to adult-specific RNAi knockdown.

Current tools do not enable us to visualise Toll-6+ neurons at the same time as manipulating DNT-2 neurons and at the same time as monitoring Dcp1. Stainings with Dcp1 in the adult brain are not trivial. Thus, we cannot guarantee this. However, Toll-6 is the preferential receptor for DNT-2, and given that apoptosis increases when we knock-down DNT-2, the most parsimonious interpretation is that the dying cells bear the DNT-2 receptor Toll-6. Even if DNT-2 can promiscuously bind other Toll receptors, the simplest way to interpret these data remains that DNT-2 promotes cell survival by signalling via its receptors, as no other possible route is known to date. This would be consistent with all other data in this figure.

We thank this Reviewer for the feedback on the controls. Unfortunately, these are not trivial experiments, they require considerable time, effort, dedication and skill. This manuscript has already taken 5 years of daily hard work. We no longer have the staff (ie the first author left the lab) nor resources to dedicate to address this point.

(9) Figure 4B: This phenotype in DNT-2 mutants is very striking. Did the neurons still survive and did their axonal innervation in the lobes remain intact?

Homozygous DNT-2 mutants are viable and have impair climbing, as we had already shown in Figure 7C.

(10) L261: The authors mention that "PAM-β2β′2 neurons express Toll-6 (Table S1)". However, I cannot find this information in Table S1. 

Unfortunately, I cannot identify the source of that statement at present and the first authors has left the lab. In any case, although the fact that knocking down Toll-6 in these neurons causes a phenotype means they must, it does not directly prove it. We have now corrected this to: “PAM-b2b'2 neuron dendrites overlap axonal DNT2 projections”, page 11 line 280.

(11) Figure 4C, D: What about their synaptogenesis? Do they agree with the result in Figure 4B? 

This was not tested at the time. Unfortunately, these are not trivial experiments and require considerable time, effort, dedication and skill. Addressing this point experimentally is not possible for us at this point. In any case, given the evidence we already provide, it is highly unlikely they would alter the interpretation of our findings and the value of the discoveries already provided.

(12) L270: The authors state: "To ask whether DNT-2 might affect axonal terminals, we tested PPL1 axons." However, it is unclear why the focus was shifted to PPL1 neurons when similar analyses could have been performed on PAM DANs for consistency. In addition, it would be beneficial to assess dendritic arbor complexity and synaptogenesis in PPL1-γ1-pedc neurons to provide a more comprehensive comparison between PPL1 and PAM DANs. Performing parallel analyses on both neuron types would strengthen the study by providing insight into the generality and specificity of DNT-2 in different dopaminergic circuits. 

The question we addressed with Figure 4 was whether the DNT-2 and its receptors could modify axons, dendrites and synapses, ie all features of neuronal plasticity. The reason we used PPL1-g1-pedc to analyse axonal terminals was because of their morphology, which offered a clearer opportunity to visualise axonal endings than PAMs did. An exhaustive analysis of PPL1-g1-pedc is beyond the scope of this work and not the central focus.

(13) Figure 4G lacks a permissive temperature control, which is essential to confirm that the observed effects are due to adult-specific RNAi knockdown. 

We thank this Reviewer for this feedback, which we will bear in mind for future projects.

(14) Figure 5A requires quantification and statistical comparison.

We thank this Reviewer for this feedback. We did consider this, but the data are too variable to quantify and we decided it was best to present it simply as an observation, interesting nonetheless. This is consistent as well with the data in Figure 1, which we have now expanded with this revision, which show the natural variability in DNT-2 neurons.

(15) Figure 5B: Many green signals in the control image are not labeled as PSDs, raising concerns about the accuracy of the image analysis methods used for synapse identification. While I trust that the authors have validated their analysis approach, it would strengthen the study if they provided a clearer description or evidence of the validation process. 

This was done using the Imaris “Spot function”, in volume. A threshold is set to exclude spots due to GFP background and select only synaptic spots. The selection of spots and quantification are done automatically by Imaris. All spots below the threshold are excluded, regardless of genotype and experimental conditions, rendering the analysis objective. We have now provided a detailed description of the protocol in the Materials and Methods section: page 29 lines 778-799.

(16) Figure 5C lacks genotype controls (i.e., DNT2-GAL4-only and UAS-TrpA1-only). These controls are essential because elevated temperatures alone, without activation of DNT2 neurons, could potentially increase Syt-GCaMP production, leading to an increase in the number of Syt+ synapses. Including these controls would help ensure that the observed effects are truly due to the activation of DNT2 neurons and not temperature-related artifacts. 

We thank this Reviewer for this feedback, which we will bear in mind for future projects.

(17) L314-316: The authors state, "Here, the coincidence of... revealed that newly formed synapses were stable." I think this statement needs to be toned down because there is no evidence that these pre- and post-synaptic sites are functionally connected. 

The Reviewer is correct that our data did not visualise together, in the same preparation and specimen, both pre- and post-synaptic sites. Still, given that PAMs have already been proved by others to be required for locomotion, learning and long-term memory, our data strongly suggest that synapses between them at the SMP are functionally connected.

Nevertheless, as we do not provide direct cellular evidence, we have now edited the text to tone down this claim: “Here, the coincidence of increased pre-synaptic Syt-GFP from PAMs and post-synaptic Homer-GFP from DNT-2 neurons at SMP suggests that newly formed synapses could be stable”, page 13 line 351.

(18) Figure 5D lacks permissive temperature controls. Also, the DNT-2FL overexpression phenotypes are different from the TpA1 activation phenotypes. The authors may want to discuss this discrepancy. 

Regarding the controls, these are not appropriate for this data set. These data were all taken at a constant temperature of 25°C, there were no shifts, and therefore do not require a permissive temperature control. We thank this Reviewer for drawing our attention to the fact that we made a mistake drawing the diagram, which we have now corrected in Figure 5D.

Regarding the discrepancy, this had already been discussed in the Discussion section of the previously submitted version, page 19 Line 509-526. Presumably this Reviewer missed this before.

(19) Figure 6A, B lack permissive temperature controls. These controls are important if the authors want to claim that the behavioral defects are due to adult-specific manipulations. In addition, there is no statistical difference between the PAM-GAL4 control and the RNAi knockdown group. The authors should be careful when stating that climbing was reduced in the RNAi knockdown flies (L341-342). 

We thank this Reviewer for this feedback, which we will bear in mind for future projects.

Point taken, but climbing of the tubGAL80ts, PAM>Toll-6RNAi flies was significantly different from that of the UAS-Toll-6RNAi/+ control.

(20) Figure 6C: It seems that the DAN-GAL4 only control (the second group) also rescued the climbing defect. The authors may want to clarify this point. 

The phenotype for this genotype was very variable, but certainly very distinct from that of flies over-expressing Toll-6[CY].

We thank Reviewer 2 for their very thorough analysis of our paper that has helped improve the work.

Reviewer #3 (Recommendations for the authors): 

Overall, the manuscript reports highly interesting and mostly very convincing experiments. 

We are very grateful to this Reviewer for their very positive evaluation of our work.

Based on my comments under the heading "public review", I would like to suggest three possible improvements. 

First, the quantification of structural plasticity at the sub-cellular level should be explained in more detail and potentially improved. For example, 3D reconstructions of individual neurons and quantification of the structure of boutons and dendrites could be undertaken. At present, it is not clear how bouton volumes are actually recorded accurately. 

Thank you for the feedback. The analyses of dendrites and synapses were carried out in 3D-volumes using Imaris “Filament” module and “Spot function”, respectively. Dendrites are analysed semi-automatically, ie correcting potential branching errors of Imaris, and synapses are counted automatically, after setting appropriate thresholds. Details have now been expanded in the Materials and Sections section: page 28 lines 756-768 and page 29 lines 780-799.

We would also like to thank Imaris for enabling and facilitating our remote working using their software during the Covid-19 pandemic, post-pandemic lockdowns and lab restrictions that spanned for over a year.

Second, the variability between DNT-2A-positive neurons with increasing sample size compared to a control (DNT-2A-negative neurons) should be demonstrated. Figure 2C does currently not present convincing evidence of increased structural variability. 

It is unclear what data the Reviewer refers to. Figure 2C shows qRT-PCR data, and it does not show structural variability, which instead is shown with microscopy. If it is the BacTrace data in Figure 2B, the controls had been provided and the data were unambiguous. If Reviewer means Figure 1C, it is unclear why DNT-2GAL4-negative flies are needed when the aim was to visualise normal (not genetically manipulated) DNT-2 neurons. Thus, unfortunately we do not understand what the point is here.

The observation that DNT-2 neurons are very variable, naturally, is highly interesting, and presumably this is what drew the attention of Reviewer 3. We agree that showing further data in support of this is interesting and valuable. Thus, in response to this Reviewer’s comment we have now increased the number of images that demonstrate variability of DNT-2 neurons:

(1) We have added an extra image, altogether providing three images in new Figure 1A showing three different individual brains stained with DNT-2GAL4>UAS-FlyBow1.1. These show common morphology and features, but different location of the somas and distinct detailed arborisation patterns. Two more images using DNT-2GAL4 are provided in Figure 5A.

(2) We have now added two further MCFO images, altogether showing four examples where the somas are not always in the same location and the axons arborise consistently at the SMP, but the detailed projections are not identical: new Figure 1D.

These data compellingly show natural variability in DNT-2 neuron morphology.

Third, I propose to simplify the feedback model (Figure 2F) to be less speculative. 

Indeed, some details in Figure 2F are speculative as we did not measure real dopamine levels. Accordingly, we have now edited this diagram, adding question marks to indicate speculative inference, to distinguish from the arrows that are grounded on the data we provide.

Accordingly, we have also edited the text in:

- page 9, lines 221: “Altogether, this shows that DNT-2 up-regulated TH levels (Figure 2E), and presumably via dopamine release, this inhibited cAMP in DNT-2A neurons (Figure 2F)”.

- page 20, lines 515: “Importantly, we showed that activating DNT-2 neurons increased the levels and cleavage of DNT-2, up-regulated DNT-2 increased TH expression, and this initial amplification resulted in the inhibition of cAMP signalling via the dopamine receptor Dop2R in DNT-2 neurons.”

As minor points: 

(1) Appetitive olfactory learning is based on Tempel et al., (1983); Proc Natl Acad Sci U S A. 1983 Mar;80(5):1482-6. doi: 10.1073/pnas.80.5.1482. This paper should perhaps be cited. 

Thank you for bringing this to our attention, we have now added this reference to page 14 line 394.

(2) Line 34: I would add ..."ligand for Toll-6 AND KEK-6,". 

Indeed, thank you, now corrected.

(3) Line 39: DNT-2-POSITIVE NEURONS. 

Now corrected, thank you.

(4) The levels of TH mRNA were quantified. Why not TH or dopamine directly using antibodies, ELISA, or HPLC? After all, later it is explicitly written that DNT modulates dopamine levels (line 481)! 

We thank this Reviewer for this suggestion. We did try with HPLC once, but the results were inconclusive and optimising this would have required unaffordable effort by us and our collaborators. Part of this work spanned over the pandemic and subsequent lockdowns and lab restrictions to 30% then 50% lab capacity that continued for one year, making experimental work extremely challenging. Although we were unable to carry out all the ideal experiments, the DNT-2-dependent increase in TH mRNA coupled with the EPAC-Dop2R data provided solid evidence of a DNT-2-dopamine link.

(5) Line 271: The PPL1-g1-pedc neuron has mainly (but not excusively) a function in short-term memory! 

They do, but others have also shown that PPL1-g1-pedc neurons have a gating function in long-term memory (Placais et al 2012; Placais et al 2017; Huang et al 2024) and are required for long-term memory (Adel and Griffith 2020; Boto et al 2020).

(6) Line 401: Reward learning requires PAM neurons. PPL1 neurons are required for aversive learning. 

Indeed, PPL1 neurons are required for aversive learning, but they also have a gating function in long-term memory common for both reward and aversive learning (Adel and Griffith, 2020 Neurosci Bull; Placais et al, 2012 Nature Neuroscience; Placais et al 2017 Nature Communications; Huang et al 2024 Nature).

Overall, the manuscript presents extremely interesting, novel results, and I congratulate the authors on their findings. 

We would like to thank this Reviewer for taking the time to scrutinise our work, their helpful feedback that has helped us improve the work and for their interest and positive and kind works.

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment

The work is important and of potential value to areas other than the bone field because it supports a role and mechanism for beta-catenin that is novel and unusual. The findings are significant in that they support the presence of another anabolic pathway in bone that can be productively targeted for therapeutic goals. The data for the most part are convincing. The work could be strengthened by better characterizing the osteoclast KO of Malat1 related to the Lys cre model and by including biochemical markers of bone turnover from the mice.

We thank the editors and reviewers for their time and their positive and insightful comments. We are pleased that the editors and reviewers were very enthusiastic, as stated in their Strength comments. We have performed experiments and addressed all of the points raised by the reviewers. We have revised the manuscript accordingly and the reviewers’ points are specifically addressed below. 

Public Reviews:

Reviewer #1 (Public Review):

Summary

The authors were trying to discover a novel bone remodeling network system. They found that an IncRNA Malat1 plays a central role in the remodeling by binding to β-catenin and functioning through the β-catenin-OPG/Jagged1 pathway in osteoblasts and chondrocytes. In addition, Malat1 significantly promotes bone regeneration in fracture healing in vivo. Their findings suggest a new concept of Malat1 function in the skeletal system. One significantly different finding between this manuscript and the competing paper pertains to the role of Malat1 in osteoclast lineage, specifically, whether Malat1 functions intrinsically in osteoclast lineage or not.

Strengths:

This study provides strong genetic evidence demonstrating that Malat1 acts intrinsically in osteoblasts while suppressing osteoclastogenesis in a non-autonomous manner, whereas the other group did not utilize relevant conditional knockout mice. As shown in the results, Malat1 knockout mouse exhibited abnormal bone remodeling and turnover. Furthermore, they elucidated molecular function of Malat1, which is sufficient to understand the phenotype in vivo.

We are grateful to the reviewer for highlighting the novelty, strengths and significance of our work.

Weaknesses:

Discussing differences between previous paper and their status would be highly informative and beneficial for the field, as it would elucidate the solid underlying mechanisms.

These points have been fully addressed in the point-to-point response below.

Reviewer #2 (Public Review):

Summary:

The authors investigated the roles of IncRNA Malat1 in bone homeostasis which was initially believed to be non-functional for physiology. They found that both Malat1 KO and conditional KO in osteoblast lineage exhibit significant osteoporosis due to decreased osteoblast bone formation and increased osteoclast resorption. More interestingly they found that deletion of Malat1 in osteoclast lineage cells does not affect osteoclast differentiation and function. Mechanistically, they found that Malat1 acts as a co-activator of b-Catenin directly regulating osteoblast activity and indirectly regulating osteoclast activity via mediating OPG, but not RANKL expression in osteoblast and chondrocyte. Their discoveries establish a previously unrecognized paradigm model of Malat1 function in the skeletal system, providing novel mechanistic insights into how a lncRNA integrates cellular crosstalk and molecular networks to fine-tune tissue homeostasis, and remodeling.

Strengths:

The authors generated global and conditional KO mice in osteoblast and osteoclast lineage cells and carefully analyzed the role of Matat1 with both in vivo and in vitro systems. The conclusion of this paper is mostly well supported by data.

We are grateful to the reviewer for highlighting the novelty, strengths and significance of our work.

Weaknesses:

More objective biological and biochemical analyses are required.

These points have been fully addressed in the point-to-point response below.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Qin and colleagues study the role of Malat1 in bone biology. This topic is interesting given the role of lncRNAs in multiple physiologic processes. A previous study (PMID 38493144) suggested a role for Malat1 in osteoclast maturation. However, the role of this lncRNA in osteoblast biology was previously not explored. Here, the authors note osteopenia with increased bone resorption in mice lacking Malat1 globally and in osteoblast lineage cells. At the mechanistic level, the authors suggest that Malat1 controls beta-catenin activity. These results advance the field regarding the role of this lncRNA in bone biology.

Strengths:

The manuscript is well-written and data are presented in a clear and easily understandable manner. The bone phenotype of osteoblast-specific Malat1 knockout mice is of high interest. The role of Malat1 in controlling beta-catenin activity and OPG expression is interesting and novel.

We are grateful to the reviewer for highlighting the novelty, strengths and significance of our work.

Weaknesses:

The lack of a bone phenotype when Malat1 is deleted with LysM-Cre is of interest given the previous report suggesting a role for this lncRNA in osteoclasts. However, to interpret the findings here, the authors should investigate the deletion efficiency of Malat1 in osteoclast lineage cells in their model. The data in the fracture model in Figure 8 seems incomplete in the absence of a more complete characterization of callus histology and a thorough time course. The role of Malat1 and OPG in chondrocytes is unclear since the osteocalcin-Cre mice (which should retain normal Malat1 levels in chondrocytes) have similar bone loss as the global mutants.

These points have been fully addressed in the point-to-point response below.

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

There are several suggestions for improving the manuscript, and we hope that you will review the recommendations carefully and make changes to the paper to address the concerns raised. Suggestions have been made to better characterize the osteoclast KO of Malat1 related to the Lys cre model as well as suggestions to include biochemical markers of bone turnover from your mice.

These points have been fully addressed in the point-to-point response below.

Reviewer #1 (Recommendations For The Authors):

(1) Replicate numbers in Figure 3 should be noted.

We thank the reviewer for this point. The experiments in Fig. 3 have been replicated three times, which is now noted in the figure legend.

(2) It is novel to identify OPG expression in chondrocytes. More discussion is expected.

Yes, a paragraph regarding this point has been added to the Discussion section.  

Reviewer #2 (Recommendations For The Authors):

(1) It is better to show serum osteoblast bone formation marker and osteoclast resorption marker, such as P1NP and CTx, in both Malat1 KO and osteoblast conditional KO mice.

We thank the reviewer for this important point. Since CTx values are often influenced by food intake, we measured serum TRAP levels, which also reflect changes in osteoclastic bone resorption. We have observed that the serum osteoblastic bone formation marker P1NP was decreased, while osteoclastic bone resorption marker TRAP was increased, in both Malat1^-/- and Malat1^ΔOcn mice. These changes in serum biochemical markers of bone turnover are consistent with the bone phenotype caused by Malat1 deficiency. The new data are shown in Fig.1i, Fig. 2e, and Fig.5b.    

(2) in vitro osteoblast differentiation assay is required to further confirm Malat1 regulates osteoblast differentiation.

We thank the reviewer for this suggestion. As recommended, we have performed in vitro osteoblast differentiation multiple times using calvarial cells, a commonly used system in the field. However, we observed big variability in the culture results across different experimental batches, whether conducted by different scientists or the same individual. This variability is likely due to differences in the purity of the cultured cells, as literature shows that the current culture system in the field contains a mixture of tissue cells, including not only osteoblasts but also other cells, such as stromal and hematopoietic lineage cells (DOI: 10.1002/jbmr.4052). We hope to test osteoblast differentiation using a purer culture system once it becomes available in the field. In contrast, our in vivo data, indicated by multiple parameters, show consistent osteoblast and bone formation phenotypes across a large number of mice. Therefore, the in vivo results in our study strongly support our conclusion regarding Malat1's role in osteoblastic bone formation.

(3) The authors found that Matat1 regulates osteoclast activity through OPG expression not only in osteoblasts, but also in chondrocytes and concluded that chondrocyte is involved in the crosstalk with osteoclast lineage cells in marrow. This is a very novel finding. Do the authors have any in vivo data to support this point, such as deleting Malat1 in chondrocyte lineage cells with chondrocyte-specific Cre?

We appreciate the reviewer for highlighting our novel findings and providing valuable suggestions. Given the considerable time required to generate chondrocyte-specific conditional KO mice, we plan to thoroughly investigate the crosstalk between chondrocytes and osteoclasts via Malat1 in vivo in our next project.

Reviewer #3 (Recommendations For The Authors):

(1) Ideally would show male and female data side by side in the main text figures

We thank the reviewer for this suggestion. The male and female data are now displayed side by side in Fig. 1b. 

(2) The sample size for the in vivo datasets is quite large. A power calculation should be provided to better understand how the authors decided to analyze so many mice.

Due to staff turnover during the pandemic, the first authors and several co-authors were involved in breeding the mice and collecting and analyzing bone samples. To avoid bias in sample selection, we pooled all the samples, resulting in a highly consistent phenotype across mice. This robust approach further strengthens our conclusion. 

(3) The candidate gene approach to look at beta-catenin is a bit random, it would be ideal to assess Malat1 binding proteins in osteoblasts in an unbiased way. Also, does Malat1 bind bcatenin in other cell types? The importance of this point is further underscored by ref 47 which indicates that Malat binds TEAD3.

As β-catenin is a key regulator in osteoblasts, we believe that studying the interaction between β-catenin and Malat1 is not random. Instead, this approach is well-founded and based on established knowledge in the field (as discussed below). In parallel, we are investigating genome-wide Malat1-bound targets beyond β-catenin, which will be reported in future studies. 

More detailed points have been discussed in the manuscript: 

Given that we identified Malat1 as a critical regulator in osteoblasts, we sought to investigate the mechanisms underlying the regulation of osteoblastic bone formation by Malat1. β-catenin is a central transcriptional factor in canonical Wnt signaling pathway, and plays an important role in positively regulating osteoblast differentiation and function (28-33). Upon stimulation, most notably from canonical Wnt ligands, β-catenin is stabilized and translocates into the nucleus, where it interacts with coactivators to activate target gene transcription. Previous reports observed a link between Malat1 and β-catenin signaling pathway in cancers (34,35), but the underlying molecular mechanisms in terms of how Malat1 interacts with β-catenin and regulates its nuclear retention and transcriptional activity are unclear. 

Ref47 tested Malat1 binding to Tead3 in osteoclasts. However, a key difference between our findings and those of Ref47 is that both our in vitro and in vivo data, using myeloid osteoclastspecific conditional Malat1 KO mice, do not support an intrinsically significant role for Malat1 in osteoclasts. 

(4) The statement on page 6 concluding that Malat acts as a scaffold to tether β-catenin in the nucleus is not supported by data in Fig 3d demonstrating that b-catenin nucleus translocation in response to Wnt3a is similar in control and Malat-deficient cells.

The experiment in Fig. 3d is not designed to demonstrate Malat1 and β-catenin binding, but it is essential as the result rules out the possibility that Malat1 may affect β-catenin nuclear translocation. Moreover, we have utilized two robust approaches, CHIRP and RIP, to demonstrate that Malat1 acts as a scaffold to tether β-catenin in the nucleus (Fig. 3a, b, c, Supplementary Fig. 3). 

(5) Figure 4e: can the authors show Malat deletion efficiency in the LysM-Cre model? This is important in light of the negative data in this figure and ref 47 which claims an osteoclast intrinsic role for Malat

We thank the reviewer for this suggestion. The deletion efficiency of Malat1 in the LysM-Cre mice is very high (>90%). This data is now presented in Fig. 4e. 

(6) Figure 5: since the magnitude of the effects on osteoclasts at the histology level are mild, it would be nice to also look at serum markers of bone resorption (CTX)

The magnitude of osteoclast changes at the histological level in Fig. 5 is not mild in our view, as we observe 25-30% changes with statistical significance in the osteoclast parameters of Malat1ΔOcn mice. Since CTx values are often influenced by food intake, we measured serum TRAP levels, which reflect changes in osteoclastic bone resorption. As shown in Fig.5b, serum TRAP levels are significantly elevated in Malat1^ΔOcn mice compared to control mice.

(7) Data showing chondrocytic expression of OPG is not as novel as the authors claim. Should think about growth plate versus articular sources of OPG. Growth plate chondrocytes express OPG to regulate osteoclasts in the primary spongiosa which resorb mineralized cartilage.

In the present study, we do not focus on comparing the sources of OPG from the chondrocytes in the growth plate versus articular cartilage. The novelty of our work lies in the discovery that Malat1 links chondrocyte and osteoclast activities through the β-catenin-OPG/Jagged1 axis. This Malat1-β-catenin-OPG/Jagged1 axis represents a novel mechanism regulating the crosstalk between chondrocytes and osteoclasts. 

(8) The relevance of the chondrocyte role of Malat is unclear since the bone phenotype in global and osteocalcin-Cre mice is similar.

Bone mass was decreased by 20% in Malat1^ΔOcn mice, while a 30% reduction was observed in global KO (Malat1^-/-) mice. This difference indicates potential contributions from other cell types, such as chondrocytes, and our results in Fig. 6 further support the impact of chondrocytes in Malat1's regulation of bone mass. We plan to thoroughly investigate the crosstalk between chondrocytes and osteoclasts via Malat1 in vivo in our next project.

(9) Fracture data in Figure 8 seems incomplete, it would be ideal to support micro CT with histology and look at multiple time points.

We thank the reviewer for this suggestion. We have performed histological analysis of our samples, and found that Malat1 promotes bone healing in the fracture model (Fig. 8f), which is consistent with our μCT data.

Author response:

The following is the authors’ response to the previous reviews.

Reviewer #1 (Public Review):

In this revision, the authors significantly improved the manuscript. They now address some of my concerns. Specifically, they show the contribution of end-effects on spreading the inputs between dendrites. This analysis reveals greater applicability of their findings to cortical cells, with long, unbranching dendrites than other neuronal types, such as Purkinje cells in the cerebellum.

They now explain better the interactions between calcium and voltage signals, which I believe improve the take-away message of their manuscript. They modified and added new figures that helped to provide more information about their simulations.

However, some of my points remain valid. Figure 6 shows depolarization of ~5mV from -75. This weak depolarization would not effectively recruit nonlinear activation of NMDARs. In their paper, Branco and Hausser (2010) showed depolarizations of ~10-15mV.

More importantly, the signature of NMDAR activation is the prolonged plateau potential and activation at more depolarized resting membrane potentials (their Figure 4). Thus, despite including NMDARs in the simulation, the authors do not model functional recruitment of these channels. Their simulation is thus equivalent to AMPA only drive, which can indeed summate somewhat nonlinearly.

In the current study, we used short sequences of 5 inputs, since the convergence of longer sequences is extremely unlikely in the network configurations we have examined. This resulted in smaller EPSP amplitudes of ~5mV (Figure 6 - Supplement 2A, B). Longer sequences containing 9 inputs resulted in larger somatic depolarizations of ~10mV (Figure 6 - Supplement 2E, F). Although we had modified the (Branco, Clark, and Häusser 2010) model to remove the jitter in the timing of arrival of inputs and made slight modifications to the location of stimulus delivery on the dendrite, we saw similar amplitudes when we tested a 9-length sequence using (Branco, Clark, and Häusser 2010)’s published code (Figure 6 - Supplement 2I, J). In all the cases we tested (5 input sequence, 9 input sequence, 9 input sequence with (Branco, Clark, and Häusser 2010) code repository), removal of NMDA synapses lowered both the somatic EPSPs (Figure 6 - Supplement 2C,D,G,H,K,L) as well as the selectivity (measured as the difference between the EPSPs generated for inward and outward stimulus delivery) (Figure 6 Supplement 2M,N,O). Further, monitoring the voltage along the dendrite for a sequence of 5 inputs showed dendritic EPSPs in the range of 20-45 mV (Figure 6 - Supplement 2P, Q), which came down notably (10-25mV) when NMDA synapses were abolished (Figure 6 - Supplement 2R, S). Thus, even sequences containing as few as 5 inputs were capable of engaging the NMDA-mediated nonlinearity to show sequence selectivity, although the selectivity was not as strong as in the case of 9 inputs.

Reviewer #1 (Recommendations for the authors):

Minor points:

Figure 8, what does the scale in A represent? I assume it is voltage, but there are no units. Figure 8, C, E, G, these are unconventional units for synaptic weights, usually, these are given in nS / per input.

We have corrected these. The scalebar in 8A represents membrane potential in mV. The units of 8C,E,G are now in nS.

Reviewer #2 (Public Review):

Summary:

If synaptic input is functionally clustered on dendrites, nonlinear integration could increase the computational power of neural networks. But this requires the right synapses to be located in the right places. This paper aims to address the question of whether such synaptic arrangements could arise by chance (i.e. without special rules for axon guidance or structural plasticity), and could therefore be exploited even in randomly connected networks. This is important, particularly for the dendrites and biological computation communities, where there is a pressing need to integrate decades of work at the single-neuron level with contemporary ideas about network function.

Using an abstract model where ensembles of neurons project randomly to a postsynaptic population, back-of-envelope calculations are presented that predict the probability of finding clustered synapses and spatiotemporal sequences. Using data-constrained parameters, the authors conclude that clustering and sequences are indeed likely to occur by chance (for large enough ensembles), but require strong dendritic nonlinearities and low background noise to be useful.

Strengths:

(1) The back-of-envelope reasoning presented can provide fast and valuable intuition. The authors have also made the effort to connect the model parameters with measured values. Even an approximate understanding of cluster probability can direct theory and experiments towards promising directions, or away from lost causes.

(2) I found the general approach to be refreshingly transparent and objective. Assumptions are stated clearly about the model and statistics of different circuits. Along with some positive results, many of the computed cluster probabilities are vanishingly small, and noise is found to be quite detrimental in several cases. This is important to know, and I was happy to see the authors take a balanced look at conditions that help/hinder clustering, rather than to just focus on a particular regime that works.

(3) This paper is also a timely reminder that synaptic clusters and sequences can exist on multiple spatial and temporal scales. The authors present results pertaining to the standard `electrical' regime (~50-100 µm, <50 ms), as well as two modes of chemical signaling (~10 µm, 100-1000 ms). The senior author is indeed an authority on the latter, and the simulations in Figure 5, extending those from Bhalla (2017), are unique in this area. In my view, the role of chemical signaling in neural computation is understudied theoretically, but research will be increasingly important as experimental technologies continue to develop.

Weaknesses:

(1) The paper is mostly let down by the presentation. In the current form, some patience is needed to grasp the main questions and results, and it is hard to keep track of the many abbreviations and definitions. A paper like this can be impactful, but the writing needs to be crisp, and the logic of the derivation accessible to non-experts. See, for instance, Stepanyants, Hof & Chklovskii (2002) for a relevant example.

It would be good to see a restructure that communicates the main points clearly and concisely, perhaps leaving other observations to an optional appendix. For the interested but time-pressed reader, I recommend starting with the last paragraph of the introduction, working through the main derivation on page 7, and writing out the full expression with key parameters exposed. Next, look at Table 1 and Figure 2J to see where different circuits and mechanisms fit in this scheme. Beyond this, the sequence derivation on page 15 and biophysical simulations in Figures 5 and 6 are also highlights.

We appreciate the reviewers' suggestions. We have tightened the flow of the introduction. We understand that the abbreviations and definitions are challenging and have therefore provided intuitions and summaries of the equations discussed in the main text.

Clusters calculations

Our approach is to ask how likely it is that a given set of inputs lands on a short segment of dendrite, and then scale it up to all segments on the entire dendritic length of the cell.

Thus, the probability of occurrence of groups that receive connections from each of the M ensembles (PcFMG) is a function of the connection probability (p) between the two layers, the number of neurons in an ensemble (N), the relative zone-length with respect to the total dendritic arbor (Z/L) and the number of ensembles (M).

Sequence calculations

Here we estimate the likelihood of the first ensemble input arriving anywhere on the dendrite, and ask how likely it is that succeeding inputs of the sequence would arrive within a set spacing.

Thus, the probability of occurrence of sequences that receive sequential connections (PcPOSS) from each of the M ensembles is a function of the connection probability (p) between the two layers, the number of neurons in an ensemble (N), the relative window size with respect to the total dendritic arbor (Δ/L) and the number of ensembles (M).

(2) I wonder if the authors are being overly conservative at times. The result highlighted in the abstract is that 10/100000 postsynaptic neurons are expected to exhibit synaptic clustering. This seems like a very small number, especially if circuits are to rely on such a mechanism. However, this figure assumes the convergence of 3-5 distinct ensembles. Convergence of inputs from just 2 ense mbles would be much more prevalent, but still advantageous computationally. There has been excitement in the field about experiments showing the clustering of synapses encoding even a single feature.

We agree that short clusters of two inputs would be far more likely. We focused our analysis on clusters with three of more ensembles because of the following reasons:

(1) The signal to noise in these clusters was very poor as the likelihood of noise clusters is high.

(2) It is difficult to trigger nonlinearities with very few synaptic inputs.

(3) At the ensemble sizes we considered (100 for clusters, 1000 for sequences), clusters arising from just two ensembles would result in high probability of occurrence on all neurons in a network (~50% in cortex, see p_CMFG in figures below.). These dense neural representations make it difficult for downstream networks to decode (Foldiak 2003).

However, in the presence of ensembles containing fewer neurons or when the connection probability between the layers is low, short clusters can result in sparse representations (Figure 2 - Supplement 2). Arguments 1 and 2 hold for short sequences as well.

(3) The analysis supporting the claim that strong nonlinearities are needed for cluster/sequence detection is unconvincing. In the analysis, different synapse distributions on a single long dendrite are convolved with a sigmoid function and then the sum is taken to reflect the somatic response. In reality, dendritic nonlinearities influence the soma in a complex and dynamic manner. It may be that the abstract approach the authors use captures some of this, but it needs to be validated with simulations to be trusted (in line with previous work, e.g. Poirazi, Brannon & Mel, (2003)).

We agree that multiple factors might affect the influence of nonlinearities on the soma. The key goal of our study was to understand the role played by random connectivity in giving rise to clustered computation. Since simulating a wide range of connectivity and activity patterns in a detailed biophysical model was computationally expensive, we analyzed the exemplar detailed models for nonlinearity separately (Figures 5, 6, and new figure 8), and then used our abstract models as a proxy for understanding population dynamics. A complete analysis of the role played by morphology, channel kinetics and the effect of branching requires an in-depth study of its own, and some of these questions have already been tackled by (Poirazi, Brannon, and Mel 2003; Branco, Clark, and Häusser 2010; Bhalla 2017). However, in the revision, we have implemented a single model which incorporates the range of ion-channel, synaptic and biochemical signaling nonlinearities which we discuss in the paper (Figure 8, and Figure 8 Supplement 1, 2,3). We use this to demonstrate all three forms of sequence and grouped computation we use in the study, where the only difference is in the stimulus pattern and the separation of time-scales inherent in the stimuli.

(4) It is unclear whether some of the conclusions would hold in the presence of learning. In the signal-to-noise analysis, all synaptic strengths are assumed equal. But if synapses involved in salient clusters or sequences were potentiated, presumably detection would become easier? Similarly, if presynaptic tuning and/or timing were reorganized through learning, the conditions for synaptic arrangements to be useful could be relaxed. Answering these questions is beyond the scope of the study, but there is a caveat there nonetheless.

We agree with the reviewer. If synapses receiving connectivity from ensembles had stronger weights, this would make detection easier. Dendritic spikes arising from clustered inputs have been implicated in local cooperative plasticity (Golding, Staff, and Spruston 2002; Losonczy, Makara, and Magee 2008). Further, plasticity related proteins synthesized at a synapse undergoing L-LTP can diffuse to neighboring weakly co-active synapses, and thereby mediate cooperative plasticity (Harvey et al. 2008; Govindarajan, Kelleher, and Tonegawa 2006; Govindarajan et al. 2011). Thus if clusters of synapses were likely to be co-active, they could further engage these local plasticity mechanisms which could potentiate them while not potentiating synapses that are activated by background activity. This would depend on the activity correlation between synapses receiving ensemble inputs within a cluster vs those activated by background activity. We have mentioned some of these ideas in a published opinion paper (Pulikkottil, Somashekar, and Bhalla 2021). In the current study, we wanted to understand whether even in the absence of specialized connection rules, interesting computations could still emerge. Thus, we focused on asking whether clustered or sequential convergence could arise even in a purely randomly connected network, with the most basic set of assumptions. We agree that an analysis of how selectivity evolves with learning would be an interesting topic for further work.

References

• Bhalla, Upinder S. 2017. “Synaptic Input Sequence Discrimination on Behavioral Timescales Mediated by Reaction-Diffusion Chemistry in Dendrites.” Edited by Frances K Skinner. eLife 6 (April):e25827. https://doi.org/10.7554/eLife.25827.

• Branco, Tiago, Beverley A. Clark, and Michael Häusser. 2010. “Dendritic Discrimination of Temporal Input Sequences in Cortical Neurons.” Science (New York, N.Y.) 329 (5999): 1671–75. https://doi.org/10.1126/science.1189664.

• Foldiak, Peter. 2003. “Sparse Coding in the Primate Cortex.” The Handbook of Brain Theory and Neural Networks. https://research-repository.st-andrews.ac.uk/bitstream/handle/10023/2994/FoldiakSparse HBTNN2e02.pdf?sequence=1.

• Golding, Nace L., Nathan P. Staff, and Nelson Spruston. 2002. “Dendritic Spikes as a Mechanism for Cooperative Long-Term Potentiation.” Nature 418 (6895): 326–31. https://doi.org/10.1038/nature00854.

• Govindarajan, Arvind, Inbal Israely, Shu-Ying Huang, and Susumu Tonegawa. 2011. “The Dendritic Branch Is the Preferred Integrative Unit for Protein Synthesis-Dependent LTP.” Neuron 69 (1): 132–46. https://doi.org/10.1016/j.neuron.2010.12.008.

• Govindarajan, Arvind, Raymond J. Kelleher, and Susumu Tonegawa. 2006. “A Clustered Plasticity Model of Long-Term Memory Engrams.” Nature Reviews Neuroscience 7 (7): 575–83. https://doi.org/10.1038/nrn1937.

• Harvey, Christopher D., Ryohei Yasuda, Haining Zhong, and Karel Svoboda. 2008. “The Spread of Ras Activity Triggered by Activation of a Single Dendritic Spine.” Science (New York, N.Y.) 321 (5885): 136–40. https://doi.org/10.1126/science.1159675.

• Losonczy, Attila, Judit K. Makara, and Jeffrey C. Magee. 2008. “Compartmentalized Dendritic Plasticity and Input Feature Storage in Neurons.” Nature 452 (7186): 436–41. https://doi.org/10.1038/nature06725.

• Poirazi, Panayiota, Terrence Brannon, and Bartlett W. Mel. 2003. “Pyramidal Neuron as Two-Layer Neural Network.” Neuron 37 (6): 989–99. https://doi.org/10.1016/S0896-6273(03)00149-1.

• Pulikkottil, Vinu Varghese, Bhanu Priya Somashekar, and Upinder S. Bhalla. 2021. “Computation, Wiring, and Plasticity in Synaptic Clusters.” Current Opinion in Neurobiology, Computational Neuroscience, 70 (October):101–12. https://doi.org/10.1016/j.conb.2021.08.001.

Author response:

The following is the authors’ response to the previous reviews.

Reviewer #1 (Public Review):

In this revision, the authors significantly improved the manuscript. They now address some of my concerns. Specifically, they show the contribution of end-effects on spreading the inputs between dendrites. This analysis reveals greater applicability of their findings to cortical cells, with long, unbranching dendrites than other neuronal types, such as Purkinje cells in the cerebellum.

They now explain better the interactions between calcium and voltage signals, which I believe improve the take-away message of their manuscript. They modified and added new figures that helped to provide more information about their simulations.

However, some of my points remain valid. Figure 6 shows depolarization of ~5mV from -75. This weak depolarization would not effectively recruit nonlinear activation of NMDARs. In their paper, Branco and Hausser (2010) showed depolarizations of ~10-15mV.

More importantly, the signature of NMDAR activation is the prolonged plateau potential and activation at more depolarized resting membrane potentials (their Figure 4). Thus, despite including NMDARs in the simulation, the authors do not model functional recruitment of these channels. Their simulation is thus equivalent to AMPA only drive, which can indeed summate somewhat nonlinearly.

In the current study, we used short sequences of 5 inputs, since the convergence of longer sequences is extremely unlikely in the network configurations we have examined. This resulted in smaller EPSP amplitudes of ~5mV (Figure 6 - Supplement 2A, B). Longer sequences containing 9 inputs resulted in larger somatic depolarizations of ~10mV (Figure 6 - Supplement 2E, F). Although we had modified the (Branco, Clark, and Häusser 2010) model to remove the jitter in the timing of arrival of inputs and made slight modifications to the location of stimulus delivery on the dendrite, we saw similar amplitudes when we tested a 9-length sequence using (Branco, Clark, and Häusser 2010)’s published code (Figure 6 - Supplement 2I, J). In all the cases we tested (5 input sequence, 9 input sequence, 9 input sequence with (Branco, Clark, and Häusser 2010) code repository), removal of NMDA synapses lowered both the somatic EPSPs (Figure 6 - Supplement 2C,D,G,H,K,L) as well as the selectivity (measured as the difference between the EPSPs generated for inward and outward stimulus delivery) (Figure 6 Supplement 2M,N,O). Further, monitoring the voltage along the dendrite for a sequence of 5 inputs showed dendritic EPSPs in the range of 20-45 mV (Figure 6 - Supplement 2P, Q), which came down notably (10-25mV) when NMDA synapses were abolished (Figure 6 - Supplement 2R, S). Thus, even sequences containing as few as 5 inputs were capable of engaging the NMDA-mediated nonlinearity to show sequence selectivity, although the selectivity was not as strong as in the case of 9 inputs.

Reviewer #1 (Recommendations for the authors):

Minor points:

Figure 8, what does the scale in A represent? I assume it is voltage, but there are no units. Figure 8, C, E, G, these are unconventional units for synaptic weights, usually, these are given in nS / per input.

We have corrected these. The scalebar in 8A represents membrane potential in mV. The units of 8C,E,G are now in nS.

Reviewer #2 (Public Review):

Summary:

If synaptic input is functionally clustered on dendrites, nonlinear integration could increase the computational power of neural networks. But this requires the right synapses to be located in the right places. This paper aims to address the question of whether such synaptic arrangements could arise by chance (i.e. without special rules for axon guidance or structural plasticity), and could therefore be exploited even in randomly connected networks. This is important, particularly for the dendrites and biological computation communities, where there is a pressing need to integrate decades of work at the single-neuron level with contemporary ideas about network function.

Using an abstract model where ensembles of neurons project randomly to a postsynaptic population, back-of-envelope calculations are presented that predict the probability of finding clustered synapses and spatiotemporal sequences. Using data-constrained parameters, the authors conclude that clustering and sequences are indeed likely to occur by chance (for large enough ensembles), but require strong dendritic nonlinearities and low background noise to be useful.

Strengths:

(1) The back-of-envelope reasoning presented can provide fast and valuable intuition. The authors have also made the effort to connect the model parameters with measured values. Even an approximate understanding of cluster probability can direct theory and experiments towards promising directions, or away from lost causes.

(2) I found the general approach to be refreshingly transparent and objective. Assumptions are stated clearly about the model and statistics of different circuits. Along with some positive results, many of the computed cluster probabilities are vanishingly small, and noise is found to be quite detrimental in several cases. This is important to know, and I was happy to see the authors take a balanced look at conditions that help/hinder clustering, rather than to just focus on a particular regime that works.

(3) This paper is also a timely reminder that synaptic clusters and sequences can exist on multiple spatial and temporal scales. The authors present results pertaining to the standard `electrical' regime (~50-100 µm, <50 ms), as well as two modes of chemical signaling (~10 µm, 100-1000 ms). The senior author is indeed an authority on the latter, and the simulations in Figure 5, extending those from Bhalla (2017), are unique in this area. In my view, the role of chemical signaling in neural computation is understudied theoretically, but research will be increasingly important as experimental technologies continue to develop.

Weaknesses:

(1) The paper is mostly let down by the presentation. In the current form, some patience is needed to grasp the main questions and results, and it is hard to keep track of the many abbreviations and definitions. A paper like this can be impactful, but the writing needs to be crisp, and the logic of the derivation accessible to non-experts. See, for instance, Stepanyants, Hof & Chklovskii (2002) for a relevant example.

It would be good to see a restructure that communicates the main points clearly and concisely, perhaps leaving other observations to an optional appendix. For the interested but time-pressed reader, I recommend starting with the last paragraph of the introduction, working through the main derivation on page 7, and writing out the full expression with key parameters exposed. Next, look at Table 1 and Figure 2J to see where different circuits and mechanisms fit in this scheme. Beyond this, the sequence derivation on page 15 and biophysical simulations in Figures 5 and 6 are also highlights.

We appreciate the reviewers' suggestions. We have tightened the flow of the introduction. We understand that the abbreviations and definitions are challenging and have therefore provided intuitions and summaries of the equations discussed in the main text.

Clusters calculations

Our approach is to ask how likely it is that a given set of inputs lands on a short segment of dendrite, and then scale it up to all segments on the entire dendritic length of the cell.

Thus, the probability of occurrence of groups that receive connections from each of the M ensembles (PcFMG) is a function of the connection probability (p) between the two layers, the number of neurons in an ensemble (N), the relative zone-length with respect to the total dendritic arbor (Z/L) and the number of ensembles (M).

Sequence calculations

Here we estimate the likelihood of the first ensemble input arriving anywhere on the dendrite, and ask how likely it is that succeeding inputs of the sequence would arrive within a set spacing.

Thus, the probability of occurrence of sequences that receive sequential connections (PcPOSS) from each of the M ensembles is a function of the connection probability (p) between the two layers, the number of neurons in an ensemble (N), the relative window size with respect to the total dendritic arbor (Δ/L) and the number of ensembles (M).

(2) I wonder if the authors are being overly conservative at times. The result highlighted in the abstract is that 10/100000 postsynaptic neurons are expected to exhibit synaptic clustering. This seems like a very small number, especially if circuits are to rely on such a mechanism. However, this figure assumes the convergence of 3-5 distinct ensembles. Convergence of inputs from just 2 ense mbles would be much more prevalent, but still advantageous computationally. There has been excitement in the field about experiments showing the clustering of synapses encoding even a single feature.

We agree that short clusters of two inputs would be far more likely. We focused our analysis on clusters with three of more ensembles because of the following reasons:

(1) The signal to noise in these clusters was very poor as the likelihood of noise clusters is high.

(2) It is difficult to trigger nonlinearities with very few synaptic inputs.

(3) At the ensemble sizes we considered (100 for clusters, 1000 for sequences), clusters arising from just two ensembles would result in high probability of occurrence on all neurons in a network (~50% in cortex, see p_CMFG in figures below.). These dense neural representations make it difficult for downstream networks to decode (Foldiak 2003).

However, in the presence of ensembles containing fewer neurons or when the connection probability between the layers is low, short clusters can result in sparse representations (Figure 2 - Supplement 2). Arguments 1 and 2 hold for short sequences as well.

(3) The analysis supporting the claim that strong nonlinearities are needed for cluster/sequence detection is unconvincing. In the analysis, different synapse distributions on a single long dendrite are convolved with a sigmoid function and then the sum is taken to reflect the somatic response. In reality, dendritic nonlinearities influence the soma in a complex and dynamic manner. It may be that the abstract approach the authors use captures some of this, but it needs to be validated with simulations to be trusted (in line with previous work, e.g. Poirazi, Brannon & Mel, (2003)).

We agree that multiple factors might affect the influence of nonlinearities on the soma. The key goal of our study was to understand the role played by random connectivity in giving rise to clustered computation. Since simulating a wide range of connectivity and activity patterns in a detailed biophysical model was computationally expensive, we analyzed the exemplar detailed models for nonlinearity separately (Figures 5, 6, and new figure 8), and then used our abstract models as a proxy for understanding population dynamics. A complete analysis of the role played by morphology, channel kinetics and the effect of branching requires an in-depth study of its own, and some of these questions have already been tackled by (Poirazi, Brannon, and Mel 2003; Branco, Clark, and Häusser 2010; Bhalla 2017). However, in the revision, we have implemented a single model which incorporates the range of ion-channel, synaptic and biochemical signaling nonlinearities which we discuss in the paper (Figure 8, and Figure 8 Supplement 1, 2,3). We use this to demonstrate all three forms of sequence and grouped computation we use in the study, where the only difference is in the stimulus pattern and the separation of time-scales inherent in the stimuli.

(4) It is unclear whether some of the conclusions would hold in the presence of learning. In the signal-to-noise analysis, all synaptic strengths are assumed equal. But if synapses involved in salient clusters or sequences were potentiated, presumably detection would become easier? Similarly, if presynaptic tuning and/or timing were reorganized through learning, the conditions for synaptic arrangements to be useful could be relaxed. Answering these questions is beyond the scope of the study, but there is a caveat there nonetheless.

We agree with the reviewer. If synapses receiving connectivity from ensembles had stronger weights, this would make detection easier. Dendritic spikes arising from clustered inputs have been implicated in local cooperative plasticity (Golding, Staff, and Spruston 2002; Losonczy, Makara, and Magee 2008). Further, plasticity related proteins synthesized at a synapse undergoing L-LTP can diffuse to neighboring weakly co-active synapses, and thereby mediate cooperative plasticity (Harvey et al. 2008; Govindarajan, Kelleher, and Tonegawa 2006; Govindarajan et al. 2011). Thus if clusters of synapses were likely to be co-active, they could further engage these local plasticity mechanisms which could potentiate them while not potentiating synapses that are activated by background activity. This would depend on the activity correlation between synapses receiving ensemble inputs within a cluster vs those activated by background activity. We have mentioned some of these ideas in a published opinion paper (Pulikkottil, Somashekar, and Bhalla 2021). In the current study, we wanted to understand whether even in the absence of specialized connection rules, interesting computations could still emerge. Thus, we focused on asking whether clustered or sequential convergence could arise even in a purely randomly connected network, with the most basic set of assumptions. We agree that an analysis of how selectivity evolves with learning would be an interesting topic for further work.

References

Bhalla, Upinder S. 2017. “Synaptic Input Sequence Discrimination on Behavioral Timescales Mediated by Reaction-Diffusion Chemistry in Dendrites.” Edited by Frances K Skinner. eLife 6 (April):e25827. https://doi.org/10.7554/eLife.25827.

Branco, Tiago, Beverley A. Clark, and Michael Häusser. 2010. “Dendritic Discrimination of Temporal Input Sequences in Cortical Neurons.” Science (New York, N.Y.) 329 (5999): 1671–75. https://doi.org/10.1126/science.1189664.

Foldiak, Peter. 2003. “Sparse Coding in the Primate Cortex.” The Handbook of Brain Theory and Neural Networks. https://research-repository.st-andrews.ac.uk/bitstream/handle/10023/2994/FoldiakSparse HBTNN2e02.pdf?sequence=1.

Golding, Nace L., Nathan P. Staff, and Nelson Spruston. 2002. “Dendritic Spikes as a Mechanism for Cooperative Long-Term Potentiation.” Nature 418 (6895): 326–31. https://doi.org/10.1038/nature00854.

Govindarajan, Arvind, Inbal Israely, Shu-Ying Huang, and Susumu Tonegawa. 2011. “The Dendritic Branch Is the Preferred Integrative Unit for Protein Synthesis-Dependent LTP.” Neuron 69 (1): 132–46. https://doi.org/10.1016/j.neuron.2010.12.008.

Govindarajan, Arvind, Raymond J. Kelleher, and Susumu Tonegawa. 2006. “A Clustered Plasticity Model of Long-Term Memory Engrams.” Nature Reviews Neuroscience 7 (7): 575–83. https://doi.org/10.1038/nrn1937.

Harvey, Christopher D., Ryohei Yasuda, Haining Zhong, and Karel Svoboda. 2008. “The Spread of Ras Activity Triggered by Activation of a Single Dendritic Spine.” Science (New York, N.Y.) 321 (5885): 136–40. https://doi.org/10.1126/science.1159675.

Losonczy, Attila, Judit K. Makara, and Jeffrey C. Magee. 2008. “Compartmentalized Dendritic Plasticity and Input Feature Storage in Neurons.” Nature 452 (7186): 436–41. https://doi.org/10.1038/nature06725.

Poirazi, Panayiota, Terrence Brannon, and Bartlett W. Mel. 2003. “Pyramidal Neuron as Two-Layer Neural Network.” Neuron 37 (6): 989–99. https://doi.org/10.1016/S0896-6273(03)00149-1.

Pulikkottil, Vinu Varghese, Bhanu Priya Somashekar, and Upinder S. Bhalla. 2021. “Computation, Wiring, and Plasticity in Synaptic Clusters.” Current Opinion in Neurobiology, Computational Neuroscience, 70 (October):101–12. https://doi.org/10.1016/j.conb.2021.08.001.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1:

Reviewer #1 was very appreciative of our results and commented “This is a novel result in ferredoxin and a significant contribution to the field”. We are very honored and pleased.

Reviewer #2:

(1) Changing the nomenclature of the models investigated to include the oxidation state being discussed. As they are now (CM, CMNA, etc), multiple re-reads were required to ascertain which redox state was being discussed for a particular model in a given section of the text. Appending "Ox" or "Red" for oxidized or reduced would be sufficient. 

As you indicated there are several nomenclatures to distinguish the model systems in the text. On the other hand, the main issue discussed in the text is the ionization potential (IP), which is calculated by the difference in energies between oxidized and reduced states for each model. In other words, a discussion of the IP value on each model includes both the “Ox” and “Red” energies. In order to clarify the relationship between the nomenclature of models and redox states, we added sentences below.

“Note that the IP value is obtained for each model by calculating both the Ox and Red state energies of the model.” (lines 195-196).

On the other hand, we must specify the charge state when the geometry optimization is performed for CM and CMH models. Therefore, we revised the sentence as follows.

“The decrease in |IP| value indicates that the relative stability of the Red state is suppressed compared with the CMH but is significantly larger than the CM, suggesting the importance of the protonation of Asp64 (Fig. S2B). 

To consider the effect of the structural change caused by the redox on the IP, geometrical optimization of the 4Fe-4S core was performed for the CM (Red) and CMH (Red) models using the same level of theory to the single-point calculations. The optimized Cartesian coordinates are summarized in Table S3. As illustrated in Fig. S2A, the IP values of CM and CMH change from –3.27 to –2.38 eV (|DIP| = 0.89 eV), and from –1.06 to –0.19 eV (|DIP| = 0.87 eV), respectively, before and after the geometrical optimization.” (lines 224-232)

(2) In addition to the very thorough DFT investigation of the different spin and charge combinations, did the authors try a broken-symmetry calculation to obtain the ground state description of the FeS cluster? Given the ubiquity of this approach in other FeS cluster studies, it was surprising that this approach was not taken here. Granted, the DFT investigation of each possible combination is sufficiently thorough and need not be redone. 

Thank you for your comments. A term “spin-unrestricted method”, which is used in the manuscript in the text is synonym of “broken-symmetry method”. In order to emphasize this, we revised the manuscript as follows. 

“All calculations were performed by using the spin-unrestricted (broken-symmetry) hybrid DFT method with the B3LYP functional set. As the basis set, 6-31G* and 6-31+G* were used for [Fe, C, N, O, H] and [S] atoms, respectively, for the IP calculations.” (Line 451)

(3) Line 161 "an" to "a" 

We corrected the mistake. Thank you so much. (Line 161)

(4) Figure 4A seems a bit odd. Why do the traces eclipse the y-axis? And the traces between 330 and 370 nm are much noisier and appear thicker than the rest of the plot. Is this an issue with the monochromator grating used in wavelength selection? Reducing the thickness of the individual traces may help the data presentation in this figure. Also, the arrows on the plot have an opaque white background. Can this be removed so that the arrows do not eclipse the traces in the plot? 

The spectrum in the Fig.4A seemed to be odd. The spectral figure has been revised to improve its appearance. (We have also corrected E53A in Figure 5B.) This reviewer also pointed out that “the traces between 330 and 370 nm are much noisier”. We are struggling with the noise caused by the grating (or the motor malfunction) of the monochromator as you pointed out. Once the monochromator is repaired and a smooth spectrum is obtained, we will upload further revisions.

(5) Figure S9 is a very nice schematic illustrating the general findings of the study. Can this be moved to the main text?

Thank you for your helpful comment. Accordingly, the Fig.9S and its legend are moved to the main text. (Lines 675-680)

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

This manuscript by Bai et al concerns the expression of Scleraxis (Scx) by muscle satellite cells (SCs) and the role of that gene in regenerative myogenesis. The authors report the expression of this gene associated with tendon development in satellite cells. Genetic deletion of Scx in SCs impairs muscle regeneration, and the authors provide evidence that SCs deficient in Scx are impaired in terms of population growth and cellular differentiation. Overall, this report provides evidence of the role of this gene, unexpectedly, in SC function and adult regenerative myogenesis.

We appreciate the comments and thank her/him for the support.

There are a few minor points of concern.

(1) From the data in Figure 1, it appears that all of the SCs, assessed both in vitro and in vivo, express Scx. The authors refer to a scRNA-seq dataset from their lab and one report from mdx mouse muscle that also reveals this unexpected gene expression pattern. Has this been observed in many other scRNA-seq datasets? If not, it would be important to discuss potential explanations as to why this has not been reported previously.

Thanks for this question regarding data in Fig.1. We did initially use immunofluorescence staining of Pax7 and GFP on muscle sections and primary myoblast cultures prepared from Tg-ScxGFP mice to conclude that Scx was expressed in satellite cells (SCs). In addition to the cited mdx RNA-seq data, we have included a re-analysis of a published scRNA-seq data set in Fig.2E (Dell'Orso et al., Development, 2019), and our own scRNA-seq data (Fig.S5D, F). We have now re-examined an additional scRNA-seq data set of TA muscles at various regeneration time points (De Micheli et al., Cell Rep. 2020), in which Scx expression was detected in MuSC progenitors and mature muscle cells. We have added the De Micheli et al. reference and the re-analysis of that scRNA-seq data set for Scx expression as an additional panel in Fig. 2E, with accompanying text (p. 7, ln. 4-6). Thus, our immunostaining results are consistent with scRNA-seq data from our and two other independent scRNA-seq data sets.

We think that Scx expression in the adult myogenic lineage was not previously reported mainly because its expression level was low, and might be dismissed as spurious detection. Additionally, detecting such low expression levels requires sophisticated detection methods with high capture efficiency. Previous studies have noted limitations in transcript capture or transcription factor dropout in 10x Genomics-based datasets (Lambert et al., Cell, 2018; Pokhilko et al., Genome Res., 2021). The most likely and straightforward reason is that Scx was simply not a focus in prior studies amid so many other genes of interest. We have now added this last explanation in the text (p.7, ln. 8-9), following the re-analyses of Scx expression in published scRNA-seq data sets.

(2) A major point of the paper, as illustrated in Fig. 3, is that Scx-neg SCs fail to produce normal myofibers and renewed SCs following injury/regeneration. They mention in the text that there was no increased PCD by Caspase staining at 5 DPI. A failure of cell survival during the process of SC activation, proliferation, and cell fate determination (differentiation versus self-renewal) would explain most of the in vivo data. As such, this conclusion would seem to warrant a more detailed analysis in terms of at least one or two other time points and an independent method for detecting dead/dying cells (the in vitro data in Fig. 4F is also based on an assessment of activated Caspase to assess cell death). The in vitro data presented later in Fig. S4G, H do suggest an increase in cell loss during proliferative expansion of Scx-neg SCs. To what extent does cell loss (by whatever mechanism of cell death) explain both the in vivo findings of impaired regeneration and even the in vitro studies showing slower population expansion in the absence of Scx?

We appreciate these constructive suggestions. Based on the number of available control and cKO animals, we were limited to one additional time point at 3 dpi to assess PCD by TUNEL in vivo. We were disappointed again to find no appreciable levels of PCD at 3 dpi by TUNEL (new Fig.S4I), thus no quantifications were included. We also re-did the in vitro experiment using purified SCs and monitored PCD by staining for cleaved Caspase-3 using a validated tube of antibodies (positive staining after 6 h of treatment by 1 mM staurosporine of control and ScxcKO cells; included as new Fig. S4J and legend). We were pleased to find an increase of cleaved Caspase3 stained cells, i.e. PCD, of Scx-cKO SCs at day 4 in culture, compared to that of the control. We have now replaced the old Fig. 4F with new Fig.4F and 4G to document PCD. We also provided new text/legend for these new data (p.10. ln. 2-10; new legend for Fig. 4F and 4G).

(3) I'm not sure I understand the description of the data or the conclusions in the section titled "Basement membrane-myofiber interaction in control and Scx cKO mice". Is there something specific to the regeneration from Scx-neg myogenic progenitors, or would these findings be expected in any experimental condition in which myogenesis was significantly delayed, with much smaller fibers in the experimental group at 5 DPI?

We very much appreciate this comment. We agree that there is unlikely anything specific about the regeneration from Scx-negative myogenic progenitors. Unfilled or empty ghost fibers (basement membrane remnant) are expected due to small fiber and poor regeneration in the ScxcKO mice at 5 dpi. We have removed the subtitle and changed the content to an expected consequence rather than something special (p. 8, ln. 19-22).

(4) The data presented in Fig. 4B showing differences in the purity of SC populations isolated by FACS depending on the reporter used are interesting and important for the field. The authors offer the explanation of exosomal transfer of Tdt from SCs to non-SCs. The data are consistent with this explanation, but no data are presented to support this. Are there any other explanations that the authors have considered and that could be readily tested?

Thanks for highlighting this phenomenon. We struggled with the SC purity issue for a long time. The project started with using the R26RtdT reporter for tdT’s paraformaldehyde  resistant strong fluorescence (fixation) to aid visualization in vivo. Later, when we used the tdT signal to purify SCs by FACS, we found that only 80% sorted tdT+ cells are Pax7+. We then switched to the R26RYFP reporter, from which we achieved much higher purity (95%) of SCs (Pax7+) by FACS. As such, we also repeated and confirmed many in vivo experimental results using the R26RYFP reporter (included in the manuscript). Due to the low purity of tdT+SCs by FACS, we discontinued that mouse colony after we confirmed the superior utility of the R26RYFP reporter for SC isolation.

We sincerely apologize for not being able to conduct further testable experiments on this intriguing phenomenon. However, this issue has since been addressed and published by Murach et al., iScience, (2021). Like our experience, they found non-satellite mononuclear cells with tdT fluorescence after TMX treatment when SCs were isolated via FACS. To determine this was not due to off-target recombination or a technical artifact from tissue processing, they conducted extensive analyses. They found that the tdT+ mononuclear cells included fibrogenic cells (fibroblasts and FAPs), immune cells/macrophages, and endothelial cells. Additionally, they confirmed the significant potential of extracellular vesicle (EV)-mediated cargo transfer, which facilitates the transfer of full-length tdT transcript from lineage-marked Pax7+ cells to those mononuclear cells. We have modified the text to emphasize and acknowledge their contribution to this important point, and explained the difference between YFP and tdT reporter alleles in more detail (p.9, ln. 11-17).

(5) The Cut&Run data of Fig. 6 certainly provide evidence of direct Scx targets, especially since the authors used a novel knock-in strain for analyses. The enrichment of E-box motifs provides support for the 207 intersecting genes (scRNA-seq and Cut&Run) being direct targets. However, the rationale elaborated in the final paragraph of the Results section proposing how 4 of these genes account for the phenotypes on the Scx-neg cells and tissues is just speculation, however reasonable. These are not data, and these considerations would be more appropriate in the Discussion in the absence of any validation studies.

We agree with this comment and have moved speculations into the Discussion (p. 15, ln. 4-15, and from p. 18, ln. 4 to p. 19, ln. 4).

Reviewer #2 (Public Review):

Summary:

Scx is a well-established marker for tenocytes, but the expression in myogenic-lineage cells was unexplored. In this study, the authors performed lineage-trace and scRNA-seq analyses and demonstrated that Scx is expressed in activated SCs. Further, the authors showed that Scx is essential for muscle regeneration using conditional KO mice and identified the target genes of Scx in myogenic cells, which differ from those of tendons.

Strengths:

Sometimes, lineage-trace experiments cause mis-expression and do not reflect the endogenous expression of the target gene. In this study, the authors carefully analyzed the unexpected expression of Scx in myogenic cells using some mouse lines and scRNA-seq data.

We appreciate the comments and thank her/him for noting the strengths of our manuscript.

Weaknesses:

Scx protein expression has not been verified.

We are aware of this weakness. We had previously used Western blotting (WB) using cultured SCs from control and ScxcKO mice, but did not detect endogenous Scx protein even in the control. In response to this comment, we have re-done several WB experiments using new lysates from control and ScxcKO SCs and two commercial antibodies: anti-Scx antibody 1 from Abcam (ab58655) and anti-Scx antibody 2 from Invitrogen (PA5-23943). These antibodies have been reported to detect endogenous Scx protein in tendon cells in Spang et al., BMC Musculoskelet Disord (2016) and  Bochon et al., Int J Stem Cells (2021). Despite our best efforts, we were not able to detect a reliable Scx band. We have also conducted immunofluorescence using these two antibodies. Still, we failed to detect a difference of staining signals between control and cKO SCs using these antibodies. Lastly, we conducted immunofluorescence using the ScxTy1 myoblasts and we did not find the staining signal coinciding with the Ty1 signal (by double staining). We have been very frustrated by not knowing what caused this technical difficulty in our hands. Given that these were negative data, we did not include them. However, we do hope that the combined data from scRNA-seq, ScxCreERT2 lineage-tracing, Tg-ScxGFP expression, and ScxTy1 knock-in together are deemed sufficient to make up for the deficiency of data for endogenous Scx protein in regenerative myogenic cells.

Response to Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

p. 8: The text refers to Fig. 3I, but this should be Fig. 3H.

We apologize for the confusion. Please note that by keeping all 14 dpi data in the same row, we placed Fig.3I at an unconventional/unexpected position, i.e., next to 3D &3E, and above 3F-H. We were aware that this unconventional placement could cause confusion, and it did. With that said, we have now re-arranged the subfigures (same data content) so that the updated Fig.3 contains subfigures in the expected and proper spatial order. We double-checked the figure referral in the text (p. 8, ln. 16-17) and the text is correct – just that the original Fig.3I should have been at the original Fig.3H position and that is now corrected.

Reviewer #2 (Recommendations For The Authors):

(1) Given that Scx binds to the E-box and regulates gene expression, it is of interest to know the relevance between MyoD and Scx. If possible, the reviewer recommends to include some discussions.

Thanks for the comment. MyoD1 is a well-known transcript factor regulating myogenesis, whereas Scx is primarily studied in tenocytes and other connective tissues. We agree that our new findings deserve a discussion regarding the relevance between MyoD1 and Scx.  We have added a description of their differences in the discussion and two new references (p.19, ln. 7-17).

(2) Considering that Scx is a transcriptional factor, it is interesting that Scx-GFP was not detected in the nuclei of regenerated myofibers. Could the subcellular localization of Scx-GFP provide some insights into the function of Scx as a transcription factor during muscle regeneration?

Tg-ScxGFP is a transgenic line generated by random insertion into the genome (Pryce et al., 2007; cited). The plasmid used for transgenesis was constructed by replacing most of Scx’s first exon with GFP, and including ~ 9Kb flanking regulatory sequences. As such, the ScxGFP is not a fusion gene, but rather that the GFP expression is regulated by Scx promoter and enhancer(s). This GFP reporter lacks a nuclear localization signal (NLS), hence it is mainly detected in the cytoplasm; some nuclear signal is detected, presumably due to GFP’s small size permitting passive diffusion into the nucleus. Thus, the GFP signal is used as a reporter for Scx expression, but GFP subcellular localization does not provide insight into Scx function per se. Conversely, ScxTy1/Ty1 is a knock-in allele created by fusing a triple-Ty1 tag (3XTy1) to the C-terminus of Scx, and we observed that Ty1 is located in the nucleus by the immunofluorescent staining. We used the Ty1 epitope to carry out CUT&RUN experiments to gain insight to the function of Scx as a transcription factor.

(3) Fig1D The number of arrows in the Merge image is not matched with others. In addition, the star mark in the Pax7 image is likely an error.

Apologies. We have now corrected these errors in the revised Fig.1D.

(4) FigS1A Is there only one myofiber shown in the dashed line in this image? It is unclear why only this myofiber is surrounded by the dashed line.

The dashed line encircles a single fiber because it was not visible in the provided image. However, there are 3 fibers in this image. Because we did not immuno-stain for myofibers here, we circled one fiber for illustration. For clarity, we brightened the background (of the entire original images) so the background signals from myofiber boundaries are discernable without outlines.

(5) FigS1B There was no overlapped DAPI staining in the Myogenin+ cell. DAPI-staining should be present in Myogenin+ cells because myogenin is located in the nucleus.

Fig.S1B is immuno-staining for MyoD , and we marked one MyoD+DAPI+GFP+ cell/nucleus. Fig.S1C is immune-staining for Myogenin, and we also marked one (cell/nucleus) that is triple positive.

(6) The position of the asterisk for the ScxGFP in FigS1D is misaligned. In addition, the position is not matched with Fig1C. Because all myofibers are Scx-positive, it is strange that only one myofiber has an asterisk. The reviewer suggests removing the mark.

Thank you for pointing out these errors. We have now corrected the misalignment and removed the unnecessary asterisk.

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment 

This study presents valuable experimental and numerical results on the motility of a magnetotactic bacterium living in sedimentary environments, particularly in environments of varying magnetic field strengths. The evidence supporting the claims of the authors is solid, although the statistical significance comparing experiments with the numerical work is weak. The study will be of interest to biophysicists interested in bacterial motility. 

We thank the reviewers and editors for their careful reading and the constructive comments. With respect to the statement about weak statistical significance, we think that this statement mixes two separate issues, the significance of the difference between experiments at 0 and 50µT and the comparison of experiments with simulations. We have amended our manuscript to address both points as described below. The difference between the experiments at 0 and 50µT is indeed significant, and the discrepancy between experiments and simulations can be explained by unavoidable differences in the way we quantify bacterial throughput.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors present experimental and numerical results on the motility Magnetospirillum gryphiswaldense MSR-1, a magnetotactic bacterium living in sedimentary environments. The authors manufactured microfluidic chips containing three-dimensional obstacles of irregular shape, that match the statistical features of the grains observed in the sediment via microcomputer tomography. The bacteria are furthermore subject to an external magnetic field, whose intensity can be varied. The key quantity measured in the experiments is the throughput ratio, defined as the ratio between the number of bacteria that reach the end of the microfluidic channel and the number of bacteria entering it. The main result is that the throughput ratio is non-monotonic and exhibits a maximum at magnetic field strength comparable with Earth's magnetic field. The authors rationalize the throughput suppression at large magnetic fields by quantifying the number of bacteria trapped in corners between grains. 

Strengths: 

While magnetotactic bacteria's general motility in bulk has been characterized, we know much less about their dynamics in a realistic setting, such as a disordered porous material. The micro-computer tomography of sediments and their artificial reconstruction in a microfluidic channel is a powerful method that establishes the rigorous methodology of this work. This technique can give access to further characterization of microbial motility. The coupling of experiments and computer simulations lends considerable strength to the claims of the authors, because the model parameters (with one exception) are directly measured in the experiments. 

Weaknesses: 

The main weakness of the manuscript pertains to the discussion of the statistical significance of the experimental throughput ratio. Especially when comparing results at zero and 50 micro Tesla. The simulations seem to predict a stronger effect than seen in the experiments. The authors do not address this discrepancy. 

We thank the reviewer for their positive assessment and the detailed constructive remarks. 

The increase in bacterial throughput between 0 and 50 µT is indeed more pronounced in the simulations than in the experiments, partly due to the fact that there is considerably more variability in the experimental data. We did two things to address this issue: (1) We performed additional statistical test addressing the difference between the experimental results at 0 and 50 µT. Indeed, the difference is only weakly significant (in contrast to the difference of either to 500µT). The increase is however consistent with the observation in the absence of obstacles in the channel, where we see a monotonous increase from 0 to 500 µT (Supp. Figure S5). We have added the test results in the caption of Fig. 3. (2) To address the difference between simulations and experiments, we added a section in Methods on how we determine the throughput and a short discussion in the Results section. The key points are that the initial condition is different in simulations and experiments and that the throughput is therefore quantified differently. This difference is due to experimental limitations: we cannot track bacteria through the whole channel and we wanted to avoid pushing them into the channel with fluid flow to avoid effects of flow on the results. As a consequence, bacteria continue to enter the IN region of the channel from the inlet during the experiment, while in the simulation, they all start at the beginning of the channel simultaneously. We expect this to mostly affect the case with diffusive transport (B=0).

Reviewer #2 (Public Review): 

Summary: 

simulation study of magnetotactic bacteria in microfluidic channels containing sediment-mimicking obstacles. The obstacles were produced based on micro-computer tomography reconstructions of bacteria-rich sediment samples. The swimming of bacteria through these channels is found experimentally to display the highest throughput for physiological magnetic fields. Computer simulations of active Brownian particles, parameterized based on experimental trajectories are used to quantify the swimming throughput in detail. Similar behavior as in experiments is obtained, but also considerable variability between different channel geometries. Swimming at strong field is impeded by the trapping of bacteria in corners, while at weak fields the direction of motion is almost random. The trapping effect is confirmed in the experiments, as well as the escape of bacteria with reducing field strength. 

Strengths: 

This is a very careful and detailed study, which draws its main strength from the fruitful combination of the construction of novel microfluidic devices, their use in motility experiments, and simulations of active Brownian particles adapted to the experiment. Based on their results, the authors hypothesize that magnetotactic bacteria may have evolved to produce magnetic properties that are adapted to the geomagnetic field in order to balance movement and orientation in such crowded environments. They provide strong arguments in favor of such a hypothesis. 

Weaknesses: 

Some of the issues touched upon here have been studied also in other articles. It would be good to extend the list of references accordingly and discuss the relation briefly in the text. 

We thank the reviewer for the constructive comments. We answer to the point concerning previous literature in the response to the recommendations below.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Here follows a list of points the authors should address. 

(1) Are additional experiments feasible to decrease the statistical noise present in Fig. 3c? At the very least, the authors should discuss the statistical significance of the results at 50 muT vis-a-vis 0 T. 

See our response to Strengths/Weaknesses above

(2) The experimental setup is not immediately clear. I think that adding a panel from Fig. S1 (or a sketch thereof) would help clarify, especially in relation to the entry zone and end zone. 

We are not sure what you mean. Fig. 3A already contains exactly such a panel. We have however added another supplementary figure that shows an additional detailed view of the setup (Fig. S3). In addition, we revised several figures: We have replaced Fig. S1 with a better version and exchanged the schematic view of the obstacle channel in Fig 1, removing the additional inlets that were not used in this study (also in Fig 3A), Instead we added a comment in Methods explaining their presence. Hopefully this makes the setup clear.

(3) It should be also stated that there is no external flow imposed on the channel. 

We have added such a statement in the description of the experiment (in section 2.2 Swimming of magnetotactic bacteria through sediment-mimicking obstacle channels.  

(4) Fig. 3c and Fig. 6c are seemingly showing the same quantity (or closely related ones). The authors should use the same symbol and give an explicit mathematical definition. 

The two quantities are not exactly the same, as we cannot directly quantify the flux of bacteria through the channel in our experiments. On the one hand, we cannot track bacteria through the whole channel, on the other hand, the initial conditions are not exactly the same as in the simulations. In the simulations all bacteria start at the same time at the entrance to the channel. In the experiments, they enter from the inlet and do so at different times (pushing them in with fluid flow would be possible, but carries the risk of perturbing the results due to induced flow through the channel). We have added a new section in the Methods section that explains this difference and describes the procedure used to obtain the throughput from the experiments in detail. We have also added a corresponding comment in the Result section, where the simulations are compared with the experiments. 

Minor issues: 

- Figures have different styles that should be unified. For example, the panel labels sometimes have round brackets and sometimes they don't.

See above

- Page 6, (muCT) should have the Greek letter mu 

Thanks, corrected.

- Fig. 3a is not very clear; see my point 2 above. 

See above

Reviewer #2 (Recommendations For The Authors): 

I have only a few comments and questions, which the authors should address: 

(1) The observed exponential dependence of decay time on the "well" depth could be related to the exponential density distribution of active particles in a gravitational field, which has been derived previously. Might be interesting to discuss such a possible connection. 

Thank you for the suggestion, the two cases are indeed somewhat analogous with behaviors reminiscent of thermal processes with an effective temperature. Such a description is however not generally possible (even for sedimentation, only some features are described). We plan to address in future work whether it can be made more quantitative in our case of escape from the corner traps. We have included a short discussion of the analogy in the section on trapping and escape. 

(2) The authors should consider the following relevant references, and discuss them briefly in their manuscript:

- Sedimentation, trapping, and rectification of dilute bacteria J Tailleur, ME Cates EPL 86, 60002 (2009) 

- Human spermatozoa migration in microchannels reveals boundary-following navigation P Denissenko, V Kantsler, DJ Smith, J Kirkman-Brown Proc. Natl. Acad. Sci. USA 109, 8007-8010 (2012) 

- Wall accumulation of self-propelled spheres J Elgeti, G Gompper Europhysics Letters 101, 48003 (2013) 

- Wall entrapment of peritrichous bacteria: a mesoscale hydrodynamics simulation study SM Mousavi, G Gompper, RG Winkler Son Maber 16 (20), 4866-4875 (2020) 

- A Geometric Criterion for the Optimal Spreading of Active Polymers in Porous Media C Kurzthaler, S Mandal, T Bhabacharjee, H Löwen, SS Daba, HA Stone Nat. Commun. 12, 7088 (2021) 

- Run-to-Tumble Variability Controls the Surface Residence Times of E. coli Bacteria G Junot, T Darnige, A Lindner, VA Martinez, J Arlt, A Dawson, WCK Poon, H Auradou, E Clement Phys. Rev. Leb. 128, 248101 (2022) 

- Dynamics and phase separation of active Brownian particles on curved surfaces and in porous media P Iyer, RG Winkler, DA Fedosov, G Gompper Phys. Rev. Research 5, 033054 (2023) 

We agree that there is a lot of literature on these aspects, specifically interaction of self-propelled objects with walls and motion of swimmers through porous media. We have slightly extended our overview of previous literature in the introduction and included most of these references.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1: 

(1) Their results with human macrophages suggest that there are differences between murine and human macrophages in inflammasome-mediated restriction of STm growth. For example, Thurston et al. showed that in murine macrophages that inflammasome activation controls the replication of mutant STm that aberrantly invades the cytosol, but only slightly limits replication of WT STm. In contrast, here the authors found that primed human macrophages rely on caspase-1, gasdermin D and ninjurin-1 to restrict WT STm. I wonder if the priming of the human macrophages in this study could account for the differences in these studies. Along those lines, do the authors see the same results presented in this study in the absence of priming the macrophages with Pam3CSK4. I think that determining whether the control of intracellular STm replication is dependent on priming is very important.

We thank the Reviewer for their careful attention to our manuscript and for their thoughtful comments. We have addressed this question about the impact of priming by repeating the bacterial intracellular burden assays in unprimed WT and CASP1-/- THP-1 cells. We have added additional figures to the manuscript to address this: Figure 1 – Figure Supplement 3. Under unprimed conditions, CASP1-/- cells still harbored significantly higher bacterial burdens at 6 hpi and a significant fold-increase in bacterial CFUs compared to WT cells. These results suggest that the caspase-1-mediated restriction of intracellular Salmonella replication in human macrophages is independent of priming. 

(2) Another difference with the Thurston et al. paper is the way that the STm inoculum was prepared - stationary phase bacteria that were opsonized. Could this also account for differences between the two studies rather than differences between murine and human macrophages in inflammasome-dependent control of STm?

We thank the Reviewer for this excellent suggestion. To address this possibility, we repeated the bacterial intracellular burden assays in WT and CASP1-/- THP-1 cells using stationary phase bacteria. We infected WT and CASP1-/- THP-1 cells with stationary phase Salmonella, and we subsequently assayed for intracellular bacterial burdens. These data have now been added to the manuscript in Figure 1 – Figure Supplement 4. Interestingly, we did not observe any fold-change in the bacterial colony forming units in both the WT and CASP1-/- THP-1 cells for the stationary phase Salmonella. These data indicate that by 6 hours postinfection, Salmonella do not replicate efficiently in human macrophages unless grown under SPI-1-inducing conditions. Furthermore, these results suggest that differences in how the Salmonella inoculum is prepared may contribute to the discrepancies between our study and previous studies, as noted by the Reviewer. 

(3) The authors show that the pore-forming proteins GSDMD and Ninj1 contribute to control of STm replication in human macrophages. Is it possible that leakage of gentamicin from the media contributes to this control?

Response: We thank the Reviewer for their insightful comment. We have addressed this question on the impact of gentamicin by repeating the bacterial intracellular burden assays using a lower concentration of gentamicin in combination with extensively washing the cells with RPMI media to remove the gentamicin. WT and CASP1-/- THP-1 cells were infected with WT Salmonella. Then, at 30 minutes post-infection, cells were treated with 25 μg/ml of gentamicin to kill any extracellular bacteria. At 1 hour post-infection (hpi), the cells were washed for a total of five times with fresh RPMI to remove the gentamicin, and then the media was replaced with fresh media containing no gentamicin. In parallel, we also treated cells with 100 μg/ml of gentamicin at 30 minutes post-infection, washed the cells five times with fresh RPMI at 1 hpi to remove the gentamicin, and then replaced the media with fresh media containing 10 μg/ml of gentamicin. This data has now been included in the manuscript as Figure 1 – Figure Supplement 5. We observed similar levels in the intracellular bacterial burdens at 1 hpi and 6 hpi and a fold-increase in bacterial colony forming units in CASP1-/- cells compared to WT cells across both gentamicin conditions, suggesting that gentamicin appears to not contribute to the intracellular control of Salmonella replication in human macrophages. Of note, we also tried repeating the bacterial intracellular burden assays without gentamicin, using only washes to remove extracellular at 1 hpi; however, under these experimental conditions, we observed high levels of extracellular Salmonella. Therefore, we relied on using a lower concentration of gentamicin to kill extracellular Salmonella in conjunction with extensive washing to remove the gentamicin for the remainder of the infection. 

(4) One major question that remains to be answered is whether casp-1 plays a direct role in the intracellular localization of STm. If the authors quantify the percentage of vacuolar vs. cytosolic bacteria at early time points in WT and casp-1 KO macrophages, would that be the same in the presence and absence of casp-1? If so, then this would suggest that there is a basal level of bacterial-dependent lysis of the SCV and in WT macrophages the presence of cytosolic PAMPS trigger cell death and bacteria can't replicate in the cytosol. However, in the inflammasome KO macrophages, the host cell remains alive and bacteria can replicate in the cytosol.

We thank this Reviewer for raising this important point. We have addressed this experimentally by quantifying the percentage of vacuolar vs. cytosolic Salmonella at 2 hpi in WT, NAIP-/-, and CASP1-/- THP-1 cells using a chloroquine (CHQ) resistance assay. This data has now been included in the manuscript in the new Figure 5A. The original subfigures of Figure 5 have consequently been rearranged. We did not observe any significant differences in vacuolar and cytosolic bacterial burdens at this early time point in WT, NAIP-/-, and CASP1-/- THP-1 cells. As noted by the Reviewer, these results suggest that the basal level of bacterialdependent lysis of the SCV in human macrophages is not dependent on caspase-1 or NAIP. 

Reviewer #3: 

(1) The main weaknesses of the study are the inherent limitations of tissue culture models. For example, to study interaction of Salmonella with host cells in vitro, it is necessary to kill extracellular bacteria using gentamicin. However, since Salmonella-induced macrophage cell death damages the cytosolic membrane, gentamicin can reach intracellular bacteria and contribute to changes in CFU observed in tissue culture models (major point 1). This can result in tissue culture "artefacts" (i.e., observations/conclusions that cannot be recapitulated in vivo). For example, intracellular replication of Salmonella in murine macrophages requires T3SS-2 in vitro, but T3SS-2 is dispensable for replication in macrophages of the spleen in vivo (Grant et al., 2012).  

We thank the Reviewer for their helpful comments and insightful suggestions. We have addressed some of the concerns about gentamicin in our response to Reviewer #1 above. To address the Reviewer’s concerns further, we have included language to acknowledge the limitations of our study based on the artefacts of tissue culture models in our Discussion section: “In this study, we utilized tissue culture models to examine intracellular Salmonella replication in human macrophages. These in vitro systems allow for precise control of experimental conditions and, therefore, serve as powerful tools to interrogate the molecular mechanisms underlying inflammasome responses and Salmonella replication in both immortalized and primary human cells. Still, there are limitations of tissue culture models, as they lack the inherent complexity of tissues and organs in vivo. To assess whether our findings reflect Salmonella dynamics in the mammalian host, it will be important to complement our studies and extend the implications of our work using approaches that model more complex systems, such as organoids or organ explant models co-cultured with immune cells, and in vivo techniques, such as humanized mouse models.”

(2) In Figure 1: are increased CFU in WT vs CASP1-deficient THP-1 cells due to Caspase 1 restricting intracellular replication or due to Caspase-1 causing pore formation to allow gentamicin to enter the cytosol thereby restricting bacterial replication? The same question arises about Caspase-4 in Figure 2, where differences in CFU are observed only at 24h when differences in cell death also become apparent. The idea that gentamicin entering the cytosol through pores is responsible for controlling intracellular Salmonella replication is also consistent with the finding that GSDMD-mediated pore formation is required for restricting intracellular Salmonella replication (Figure 3). Similarly, the finding that inflammasome responses primarily control Salmonella replication in the cytosol could be explained by an intact SCV membrane protecting Salmonella from gentamicin (Figure 5). 

We thank the Reviewer for highlighting this important point regarding gentamicin.

We have addressed this question in our response above to Review #1 and in Figure 1 – Figure Supplement 5. We observed caspase-1-mediated restriction of Salmonella in human macrophages even when cells were treated with a lower concentration of gentamicin (25 μg/ml) for 30 minutes and then extensively washed with RPMI media to remove any gentamicin for the remainder of the infection. These data suggest that gentamicin is likely not responsible for controlling intracellular Salmonella in human macrophages.

Author response:

We thank all three reviewers and the editors for their detailed comments on our manuscript.  The two main themes of this feedback concern the paper’s generality and its presentation.  Reviewers #2 and #3 raise questions about how the discrepancies in fitness statistics we report will be realized across organisms, environments, and in models with interactions beyond resource competition (e.g., toxicity or cross-feeding).  All reviewers and the editors have also expressed the need for the presentation to be improved, including a broader introduction to the concept of fitness (Reviewer #1), a clearer explanation of our model (Reviewer #1), better explanations of how quantifying fitness answers key biological questions (Reviewer #3), and improvements to the most technical sections to ensure accessibility to experimentalists (Reviewer #3).

In light of these comments, we wish to clarify that the goal of this paper is to provide a proof-of-principle for how different choices in quantifying fitness can lead to different analysis outcomes.  Since the focus of this paper is on the theoretical concepts, we focus on a few example data sets and a simple model to demonstrate the existence of these discrepancies.  While other organisms and environments, especially with more complex growth dynamics and interactions, could certainly have additional or different discrepancies in fitness statistics, we believe the simplicity of our approach is valuable because it demonstrates that even basic features of microbial growth (common across systems) with realistic parameter values are sufficient to cause significant differences in fitness depending on these quantification choices.  We agree with the reviewers that a systematic documentation of how these fitness discrepancies are empirically realized is important, but we believe that question is best explored in separate future works that can focus fully on this empirical rather than theoretical question.

We plan to revise the manuscript in several ways, following the suggestions of the three reviewers and the editor.  First, we will better articulate the main goal and conclusions of this manuscript, especially its generality and limitations.  Second, we will work to streamline and clarify several points in the main text identified by the reviewers to make it more accessible and useful to a broader audience, especially experimentalists who routinely measure fitness in their work.  We are grateful to the reviewers and the editor for their time and effort in assessing the manuscript, and we look forward to providing an updated version that addresses these concerns.

Author response:

Reviewer #1 (Public review):

Li et al. investigate Ca2+ signaling in T. gondii and argue that Ca2+ tunnels through the ER to other organelles to fuel multiple aspects of T. gondii biology. They focus in particular on TgSERCA as the presumed primary mechanism for ER Ca2+ filling. Although, when TgSERCA was knocked out there was still a Ca2+ release in response to TG present.

Note that we did not knockout SERCA as it is an essential gene so it would not be possible to isolate parasites that do not express SERCA. We created conditional mutants that downregulate the expression of SERCA and some activity is present in the mutant after 24 h of ATc treatment.

Overall the Ca2+ signaling data do not support the conclusion of Ca2+ tunneling through the ER to other organelles in fact they argue for direct Ca2+ uptake from the cytosol.

The authors show EM membrane contact sites between the ER and other organelles, so Ca2+ released by the ER could presumably be taken up by other organelles but that is not ER Ca2+ tunneling.

They clearly show that SERCA is required for T. gondii function.

Overall, the data presented to not fully support the conclusions reached

We agree that the data does not support Ca2+ tunneling as defined and characterized in mammalian cells. In response to this comment, we modified the title and the text accordingly.

However, we think that the study shows far more than just the role of SERCA in T. gondii functions. We argue that the study shows that the ER (through the activity of the SERCA pump) sequesters and re-distributes calcium to other organelles following influx through the PM. The experiments show that the ER is able to take calcium from the cytosol as it enters the parasite through SERCA activity, and this activity is important for the transition of the parasite between various extracellular calcium exposures. We believe that the role of the ER in redistributing calcium following exposure to physiological levels of extracellular calcium is demonstrated in the experiments shown in Figs 1H-I, 4G-H and 5G,H, I, J, K . There are no previous T. gondii studies that address the question of how intracellular stores are filled with calcium, which are essential for the continuation of the lytic cycle, meaning they are essential for the parasitism of T. gondii.

Data argue for direct Ca2+ uptake from the cytosol

The ER most likely takes up calcium from the cytosol following its entry through the PM and redistributes it to the other organelles. We will delete the word “tunneling” and replace it with transfer and re-distribution as they represent our results.

What we think is re-distribution is shown in Figure 1H and I in which the calcium released after GPN and nigericin are enhanced after TG addition. Of note is that there is no experimental evidence that supports the regulation of calcium entry by store depletion (PMID: 24867952), and we do not think that the enhanced response is due to calcium entry.

Figure 4G and H show that knocking down SERCA reduces significantly the response to GPN. Fig 5I shows that the mitochondrial calcium uptake is reduced after the addition of GPN in the knockdown mutant. Fig 2B shows that SERCA can take up calcium at 55 nM calcium while mitochondrial uptake needs higher concentrations (Fig 5B-C). However, higher calcium concentrations could be reached at the microdomains formed around MCS between the ER and mitochondrion. Figure 5E shows that the mitochondrion is not responsive to an increase of cytosolic calcium. This is also shown for the apicoplast in Fig. 7 E and F of the Li et al, Nat Commun 2021 paper.

Reviewer #2 (Public review):

The role of the endoplasmic reticulum (ER) calcium pump TgSERCA in sequestering and redistributing calcium to other intracellular organelles following influx at the plasma membrane.

T. gondii transitions through life cycle stages within and exterior to the host cells, with very different exposures to calcium, adds significance to the current investigation of the role of the ER in redistributing calcium following exposure to physiological levels of extracellular calcium.

They also use a conditional knockout of TgSERCA to investigate its role in ER calcium store-filling and the ability of other subcellular organelles to sequester and release calcium. These knockout experiments provide important evidence that ER calcium uptake plays a significant role in maintaining the filling state of other intracellular compartments.

We thank the reviewer.

While it is clearly demonstrated, and not surprising, that the addition of 1.8 mM extracellular CaCl2 to intact T. gondii parasites preincubated with EGTA leads to an increase in cytosolic calcium and subsequent enhanced loading of the ER and other intracellular compartments, there is a caveat to the quantitation of these increases in calcium loading. The authors rely on the amplitude of cytosolic free calcium increases in response to thapsigargin, GPN, nigericin, and CCCP, all measured with fura2. This likely overestimates the changes in calcium pool sizes because the buffering of free calcium in the cytosol is nonlinear, and fura2 (with a Kd of 100-200 nM) is a substantial, if not predominant, cytosolic calcium buffer. Indeed, the increases in signal noise at higher cytosolic calcium levels (e.g. peak calcium in Figure 1C) are indicative of fura2 ratio calculations approaching saturation of the indicator dye.

We agree about the limitations of using Fura2 but according to the literature (PMID:3838314, fig. 3) Fura2 is suitable for measurements between 100 nM and 1 mM calcium.  The responses in our experiments were within its linear range and the experiments with the SERCA mutant and mitochondrial GCaMPs supports the conclusions of our work.

We agree that the experiment shown in Fig 1C shows a response close to the limit of the linear range of Fura2 and we can provide a more representative trace in the final article. We can include new quantifications and comparisons.

Another caveat, not addressed, is that loading of fura2/AM can result in compartmentalized fura2, which might modify free calcium levels and calcium storage capacity in intracellular organelles.

We are aware of this issue and because of that we have modified our protocol to minimize compartmentalization. We load cells for 26 min at room temperature and keep cells in ice and do not use them for longer that 2-3 hours because we do see evidence of compartmentalization. One evidence of compartmentalization is the increase in the resting calcium concentration.

The finding that the SERCA inhibitor cyclopiazonic acid (CPA) only mobilizes a fraction of the thapsigargin-sensitive calcium stores in T. gondii coincides with previously published work in another apicomplexan parasite, P. falciparum, showing that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools (Borges-Pereira et al., 2020, DOI: 10.1074/jbc.RA120.014906). It would be valuable to determine whether this reflects the off-target effects of thapsigargin or the differential sensitivity of TgSERCA to the two inhibitors.

This is an interesting observation, and we will discuss the result considering the Plasmodium study and include the citation. We will add inhibition curves using the MagFluo protocol and compare CPA and TG.

Figure S1 suggests differential sensitivity, and it shows that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools in T. gondii. Also important is that we used 1 µM TG as we are aware that TG has shown off-target effects at higher concentrations. 

The authors interpret the residual calcium mobilization response to Zaprinast observed after ATc knockdown of TgSERCA (Figures 4E, 4F) as indicative of a target calcium pool in addition to the ER. While this may well be correct, it appears from the description of this experiment that it was carried out using the same conditions as Figure 4A where TgSERCA activity was only reduced by about 50%.

We partially agree as pointed by the reviewer knock down of TgSERCA by only 50% means that the ER still could be targeted by zaprinast and no evidence of another target calcium pool. From the MagFLuo4 experiment (although we are aware that the fluorescence of mag Fluo4 is not linear to calcium), there is SERCA activity after 24 hr of ATc treatment.  However, when adding Zaprinast after TG we see a significant release of calcium which is true for both wild type and conditional knockdowns. Because of this result we proposed that there could be another large neutral calcium pool than the one mobilized by TG. We will address these possibilities in the discussion and interpretation of the result.

The data in Figures 4A vs 4G and Figures 4B vs 4H indicate that the size of the response to GPN is similar to that with thapsigargin in both the presence and absence of extracellular calcium. This raises the question of whether GPN is only releasing calcium from acidic compartments or whether it acts on the ER calcium stores, as previously suggested by Atakpa et al. 2019 DOI: 10.1242/jcs.223883. Nonetheless, Figure 1H shows that there is a robust calcium response to GPN after the addition of thapsigargin.

The results of the experiments did not exclude the possibility that GPN can also mobilize some calcium from the ER besides acidic organelles. We don’t have any evidence to support that GPN can mobilize calcium from the ER either. Based on our unpublished work, we think GPN mainly release calcium from the PLVAC. We will include the mentioned citation and discuss the result considering the possibility that GPN may be acting on the ER.

An important advance in the current work is the use of state-of-the-art approaches with targeted genetically encoded calcium indicators (GECIs) to monitor calcium in important subcellular compartments. The authors have previously done this with the apicoplast, but now add the mitochondria to their repertoire. Despite the absence of a canonical mitochondrial calcium uniporter (MCU) in the Toxoplasma genome, the authors demonstrate the ability of T. gondii mitochondrial to accumulate calcium, albeit at high calcium concentrations. Although the calcium concentrations here are higher than needed for mammalian mitochondrial calcium uptake, there too calcium uptake requires calcium levels higher than those typically attained in the bulk cytosolic compartment. And just like in mammalian mitochondria, the current work shows that ER calcium release can elicit mitochondrial calcium loading even when other sources of elevated cytosolic calcium are ineffective, suggesting a role for ER-mitochondrial membrane contact sites. With these new tools in hand, it will be of great value to elucidate the bioenergetics and transport pathways associated with mitochondrial calcium accumulation in T. gondii.

We thank this reviewer for his/her positive comment. Studies of bioenergetics and transport pathways associated with mitochondrial calcium accumulation is part of our future plans.

The current studies of calcium pools and their interactions with the ER and dependence on SERCA activity in T. gondi are complemented by super-resolution microscopy and electron microscopy that do indeed demonstrate the presence of close appositions between the ER and other organelles (see also videos). Thus, the work presented provides good evidence for the ER acting as the orchestrating organelle delivering calcium to other subcellular compartments through contact sites in T. gondi, as has become increasingly clear from work in other organisms.

Thank you

Reviewer #3 (Public review):

This manuscript describes an investigation of how intracellular calcium stores are regulated and provides evidence that is in line with the role of the SERCA-Ca2+-ATPase in this important homeostasis pathway. Calcium uptake by mitochondria is further investigated and the authors suggest that ER-mitochondria membrane contact sites may be involved in mediating this, as demonstrated in other organisms.

The significance of the findings is in shedding light on key elements within the mechanism of calcium storage and regulation/homeostasis in the medically important parasite Toxoplasma gondii whose ability to infect and cause disease critically relies on calcium signalling. An important strength is that despite its importance, calcium homeostasis in Toxoplasma is understudied and not well understood.

We agree with the reviewer. Thank you

A difficulty in the field, and a weakness of the work, is that following calcium in the cell is technically challenging and thus requires reliance on artificial conditions. In this context, the main weakness of the manuscript is the extrapolation of data. The language used could be more careful, especially considering that the way to measure the ER calcium is highly artificial - for example utilising permeabilization and over-loading the experiment with calcium. Measures are also indirect - for example, when the response to ionomycin treatment was not fully in line with the suggested model the authors hypothesise that the result is likely affected by other storage, but there is no direct support for that.

The MagFluo protocol has been amply used in mammalian cells, DT40 cells and other cells for the characterization of the IP3 receptor response to IP3. We will include and discuss more citations in the revised article. The scheme at the top of the figure shows the protocol used. There is no overloading with calcium because the cells are permeabilized and the concentrations of calcium used are physiological and all experiments were performed at 220 nm calcium which is within the cytosolic levels tolerated by cells. The experiment was done with permeabilized cells because permeabilization allows the indicator to become diluted, the substrate MgATP to reach the membrane of the ER and in addition allows for the exposure to precise concentrations of calcium. MagFluo4 loading is intended for its compartmentalization to all intracellular compartments and the uptake stimulated by MgATP exclusively occurs in the compartment occupied by SERCA. IO is an ionophore that causes calcium release from other stores in addition to the ER and it is expected that will result in a larger release. We must clarify that the experiment shown in Fig. 2 was done to characterize the activity of SERCA and was not aimed at the characterization of the role of SERCA in the parasite. We will explain this result better in the revised version of the article.

Below we provide some suggestions to improve controls, however, even with those included, we would still be in favour of revising the language and trying to avoid making strong and definitive conclusions. For example, in the discussion perhaps replace "showed" with "provide evidence that are consistent with..."; replace or remove words like "efficiently" and "impressive"; revise the definitive language used in the last few lines of the abstract (lines 13-17); etc. Importantly we recommend reconsidering whether the data is sufficiently direct and unambiguous to justify the model proposed in Figure 7 (we are in favour of removing this figure at this early point of our understanding of the calcium dynamic between organelles in Toxoplasma).

We thank the reviewer for the suggestions and will modify the language as suggested.

Fig 7 is only a model and as all models could be incorrect. However, considering this reviewer’s criticism we will replace the model for a simpler one that is less speculative.

Another important weakness is poor referencing of previous work in the field. Lines 248-250 read almost as if the authors originally hypothesised the idea that calcium is shuttled between ER and mitochondria via membrane contact sites (MCS) - but there is extensive literature on other eukaryotes which should be first cited and discussed in this context. Likewise, the discussion of MCS in Toxoplasma does not include the body of work already published on this parasite by several groups. It is informative to discuss observations in light of what is already known.

We added a citation following the sentence mentioned by the reviewer in lines 248-250 (corrected preprint) and will include more in the revised article. We cite several pertinent articles that describe MCS in Toxoplasma (lines 378-380, very few actually). We will make sure not to miss any new articles that could have been recently published. Note that our work is not about describing the presence of MCSs. We are showing transfer of calcium between the ER and mitochondria and we present evidence that supports that it happens through MCSs.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1:

- Summary: 

Recordings were made from the dentate nucleus of two monkeys during a decision-making task. Correlates of stimulus position and stimulus information were found to varying degrees in the neuronal activities. 

We agree with this summary.

- Strengths: 

A difficult decision-making task was examined in two monkeys.

We agree with this statement.

- Weaknesses: 

One of the monkeys did not fully learn the task. The manuscript lacked a coherent hypothesis to be tested, and no attempt was made to consider the possibility that this part of the brain may have little to do with the task that was being studied. 

We understand the reviewers concern. It is correct that one of the monkeys (Mi) did not perform at a high level, but it should be noted that both monkeys learned significantly above chance level. Therefore, we would argue that both monkeys in fact did learn the task but Mi’s performance was suboptimal. This difference in the performance levels gave us a rare opportunity to dive deeper into the reasons why some animals perform better than the others and we show that Mi (the lower performing monkey) paid more attention to the outcome of the previous trial – this is evident from our behavioural and decoding models.

We tested the overall hypothesis that neurons of the nucleus dentate can dynamically modulate their activity during a visual attention task, comprising not only sensorimotor but also cognitive attentional components. Many neurons in the dentate are multimodal (Figure 3C-D) which was something that was theorized. One of the specific hypotheses that we tested is that the dentate cells can be direction-selective for both the sensorimotor and cognitive component. Given that many of the recorded cells showed direction-selectivity in their firing rate modulation for gap directions and/or stimulus directions, we provide strong evidence that this hypothesis is correct. We have now spelled out this hypothesis more explicitly in the introduction of the revised version. We now also explain better why we tested this specific hypothesis. Indeed, earlier studies in primates such as those by Herzfeld and colleagues (2018, Nat. Neuro.) and van Es and colleagues (2019, Current Biol) have indicated that direction-selectivity of cerebellar activity may occur in various sensorimotor domains.

We also appreciate the comment of this Reviewer that in our original submission we did not show our attempt to consider the possibility that this part of the brain may have little to do with the task that was being studied. We in fact did consider this possibility in that we successfully injected 3 ml of muscimol (5 μg/ml, Sigma Aldrich) into the dentate nucleus in vivo in one of the monkeys (Mo). This application resulted in a reduction of more than 10% in correct responses of the covert attention task after 45 minutes, whereas the performance remained the same following saline injections. Unfortunately, due to the timing of the experiments and Covid19-related laboratory restrictions we were unable to perform these experiments in the other monkey or repeat them in Mo. We aim to replicate this in future experiments and publish it when we have full datasets of at least two monkeys available. For this paper we have prioritized our tracing experiments, highlighting the connections of the dentate nucleus with attention related areas in brainstem and cortex in both monkeys, following perfusion.

- Perhaps the large differences in performance between the two subjects can be used as a way to interpret the neural data's relationship to behavior, as it provided a source of variance. This is what we would hypothesize if we believed that this area of the brain is playing a significant role in the task. If one animal learns much more poorly, and this region of the brain is important for that behavior, then shouldn't there be clear, interpretable differences in the neural data? 

We thank the Reviewer for this comment. We have added a new Supplementary Figure 2, in which we present the data for both monkeys separately in the revised manuscript. Comparing the two datasets however, we see more commonalities related to the significant learning in both monkeys than differences that might be related to their different levels of learning. We have therefore decided to show the different datasets transparently in the new Supplementary Figure 2, but to stay on the conservative side in our interpretations.

- How should we look for these differences? A number of recent papers in mice have uncovered a large body of data showing that during the deliberation period, when the animal is interpreting a sensory stimulus (often using the whisker system), there is ramping activity in a principal component space among neurons that contribute to the decision. This ramping activity is present (in the PCA space) in the motor areas of the cortex, as well as in the medial and lateral cerebellar nuclei. Perhaps a similar computational approach would benefit the current manuscript. 

We also appreciate this point. We have done the principal component analysis accordingly, and we indeed do find the ramping activity in several components of the dentate activity of both monkeys (Mi and Mo). We have now added a new Supplementary Figure 3 with the first three components of both correct and incorrect trials for Mi and Mo, highlighting their potential contribution.

- What is the hypothesis that is being tested? That is, what do you think might be the function of this region of the cerebellum in this task? It seems to me that we are not entirely in the dark, as previous literature on mice decision-making tasks has produced a reasonable framework: the deliberation period coincides with ramping activity in many regions of the frontal lobe and the cerebellum. Indeed, the ramp in the cerebellum appears to be a necessary condition for the ramp to be present in the frontal lobe. Thus, we should see such ramping activity in this task in the dentate. When the monkey makes the wrong choice, the ramp should predict it. If you don't see the ramping activity, then it is possible that the hypothesis is wrong, or that you are not recording from the right place. 

It is indeed one of our specific hypotheses that the dentate cells can be direction-selective for the preparing cognitive component and/or sensorimotor response. We provide evidence that this hypothesis may be correct when we analyze the regular time response curves (see Figure 2 and the new Supplementary Figure 2 where the data of both monkeys are now presented separately). Moreover, we have now verified this by analysing the ramping curves of PCA space (new Supplementary Figure 3) and firing frequency of DN neurons that modulated upon presentation of the C-stimulus (new Supplementary Figure 4). These figures and findings are now referred to in the main text.

- As this is a difficult task that depends on the ability of the animals to understand the meaning of the cues, it is quite concerning that one of the monkeys performed poorly, particularly in the early sessions. Notably, the disparity between the two subjects is rather large: one monkey at the start of the recordings achieved a performance that was much better than the second monkey did at the end of the recording sessions. You highlighted the differences in performance in Figure 1D and mentioned that you started recording once the animals reached 60% performance. However, this did not make sense to me as the performance of Mi even after the final day of recording did not reach the performance of Mo on the first day of recording. Thus, in contrast to Mo, Mi appeared to be not ready for the task when the recording began.

We understand this point. However, please note that the learning performance of the monkeys concerned retraining sessions after they had had several weeks of vacation. So, even though it is correct that one of the two monkeys had a very good consolidation and started already at a relatively high level on the first retraining session, the other one also started and ended at a level above chance level (the y-axis starts at 0.5). We now highlight this point better in the Results section.

- One objective of having two monkeys is to illustrate that what is true in one animal is also true in the other. In some figures, you show that the neural data are significantly different, while in others you combine them into one. Thus, are you confident that the neural data across the animals should be combined, as you have done in Figure 2? Perhaps you can use the large differences in performance as a source of variance to find meaning in the neural data. 

This is a valid question; as highlighted above, we have now addressed this point in the new Supplementary Figure 2, where the data for both monkeys are presented separately. Given the sample sizes and level of variances, it is in general difficult to draw conclusions about the potential differences and contributions, but the data are sufficiently transparent to observe common trends. With regard to linking differences in the neural data to the differences in performance level, please also consider Figure 4, the new Supplementary Figure 3 (with the ramping PCA component) and new Supplementary Figure 4 (with the additional analysis of the ramping activity of DN neurons that modulated upon presentation of the C-stimulus), which suggests that the ramping stage of Mo starts before that of Mi. This difference highlights the possibility that injecting accelerations of the simple spike modulations of Purkinje cells in the cerebellar hemispheres into the complex of cerebellar nuclei may be instrumental in improving the performance of responses to covert attention, akin to what has been shown for the impact of Purkinje cells of the vestibulocerebellum on eye movement responses to vestibular stimulation (De Zeeuw et al. 1995, J Neurophysiol). This possibility is now also raised in the Discussion.

- How do we know that these neurons, or even this region of the brain, contribute to this task? When a new task is introduced, the contributions of the region of the brain that is being studied are usually established via some form of manipulation. This question is particularly relevant here because the two subjects differed markedly in their performance, yet in Figure 3 you find that a similar percentage of neurons are responding to the various elements of the task.

We appreciate this question. As highlighted above, we are refraining from showing our muscimol manipulation (3 ml of 5 μg/ml muscimol, Sigma Aldrich), as it only concerns 1 successful dataset and 1 control experiment. We hope to replicate this reversible lesion experiment in the future and publish it when we have full new datasets of at least two monkeys available. As explained above, for this paper we have sacrificed both monkeys following a timed perfusion, so as to have similar survival times for the transport of the neuro-anatomical tracer involved.  

- Behavior in both animals was better when the gap direction was up/down vs. left/right. Is this difference in behavior encoded during the time that the animal is making a decision? Are the dentate neurons better at differentiating the direction of the cue when the gap direction is up/right vs. left/right? 

These data have now been included in the new Supplementary Figure 2; we did not observe any significant differences in this respect.

Reviewer #2:

- The authors trained monkeys to discriminate peripheral visual cues and associate them with planning future saccades of an indicated direction. At the same time, the authors recorded single-unit neural activity in the cerebellar dentate nucleus. They demonstrated that substantial fractions of DN cells exhibited sustained modulation of spike rates spanning task epochs and carrying information about stimulus, response, and trial outcome. Finally, tracer injections demonstrated this region of the DN projects to a large number of targets including several known to interconnect the visual attention network. The data compellingly demonstrate the authors' central claims, and the analyses are well-suited to support the conclusions. Importantly, the study demonstrates that DN cells convey many motor and nonmotor variables related to task execution, event sequencing, visual attention, and arguably decision-making/working memory. 

We thank the Reviewer for this positive and constructive feedback.

- The study is solid and I do not have major concerns, but only points for possible improvement. 

We thank the Reviewer for this positive feedback.

- A key feature of this data is the extended changes/ramps in DN output across epochs (Figure 2). Crudely, this presents a challenge for the view that DN output mainly drives motor effectors, as the saccade itself lasts only a tiny fraction of the overall task. Some discussion of this dichotomy in thinking about the function(s) of the cerebellum, vis a vis the multifarious DN targets the authors demonstrate here, etc., would be helpful. 

We agree with the Reviewer and we have expanded our Discussion on this point, also now highlighting the outcome of the new PCA analysis recommended by Reviewer 1 (see the new Supplementary figure Figure 3).

- A high-level suggestion on the data: the presentation of the data focuses (sensibly) on the representation of the stimulus and response epochs (Figures 2-3). Yet, the authors then show that from decoding, it is, in fact, a trial outcome that is best represented in the population (Figure 4). While there is nothing 'wrong' with this, it reads slightly incongruously, and the reader does a bit of a "double take" back to the previous figures to see if they missed examples of the trial-outcome signals, but the previous presentations only show correct trials. Consider adding somewhere in the first 3 main figures some neural data showing comparisons with incorrect trials. This way, the reader develops prior expectations for the outcome decoding result and frame of reference for interpreting it. On a related note, the text contains an earlier introduction of this issue (p24 last sentence) and p25 paragraph 1 cites Figure 3D and 3E for signals "related to the absence of reward" - but the caption says this includes only correct trials? 

We thank the Reviewer for bringing up these points. We have addressed the textual suggestions. Moreover, we have done the PCA analysis suggested by Reviewer 1 for both the correct and incorrect trials (see Supplementary material).

- P29: The discrepancy in retrograde labeling between monkeys (2 orders of magnitude): I realize the authors can't really do anything about this, but the difference is large enough to warrant concerns in the interpretation (how did the tracer spread over the drastically larger area? Isotropically? Could it cross more "hard boundaries" and incorporate qualitatively different inputs/outputs?). A small discussion of possible caveats in interpreting the outcomes would be helpful. 

We fully agree with this comment. As highlighted in the text, in both monkeys we first identified the optimal points for injection in the dentate nucleus electrophysiologically and we used the same pump with the same settings to carry out the injections, but even so the differences are substantial. We suspect that the larger injection might have been caused by an air bubble trapped in the syringe or a deviation in the stock solution, but we can never be sure of that. We have added a potential explanation for the caveat that might have played a role.

- And a list of quick points: 

We have addressed all points listed below; we want to thank the Reviewer for bringing them up.

P3 paragraph 2 needs comma "in daily life,". 

P4 paragraph 2 "C-gap" terminology not previously defined. 

P4 paragraph 2 "animals employed different behavioral strategies". Grammatically, you should probably say "each animal employed a different behavioral strategy," but also scientifically the paragraph doesn't connect this claim to anything about the DN (whereas, e.g., the abstract does make this connection clear). 

P5 paragraph 1 "theca" should be "the". 

P6 paragraph 1 problem with ignashenkova citation insert. 

P10 paragraph 1 I think the spike rate "difference between highest and lowest" is not exactly the same as "variance," you might want to change the terminology. 

P10 paragraph 1 should probably say "To determine if a cell preferentially modulated". 

P10 paragraph 1 last sentence the last clause could be clearer. 

P17 paragraph 2 should be something like "as well as those by Carpenter and..."? 

P20 caption: consider "...directionality in the task: only one C-stim...". 

P20 caption: consider "to the left and right in the [L/R] task...to the top/bottom in the [U/D] task". 

Fig1E and S1 - is there a physical meaning of the "weight" unit, and if none, can this be transformed into a more meaningful unit? 

P21 paragraph 1 consider "activity was recorded for 304 DN neurons...". 

P21 paragraph 1 "correlations with the temporal windows" it's not clear how activity can "correlate" with a time window, consider rephrasing (activity levels changed during these time epochs, depending on stimulus identity). 

P21 paragraph 1 should be "by comparing the number of spikes in a bin...". 

P22 paragraph 2 "when we aligned the neurons to the time of maximum change" needs clarification. The maximum change of what? And per neuron? Across the population? 

P22 paragraph 2 "than that of the facilitating" should be "than did the facilitating units". 

P24 paragraph 1 needs a comma and rewording "Within each direction, trials are sorted by the time of saccade onset". 

P24 paragraph 1 should probably say "Same as in G, but for suppressed cells". 

P24 paragraph 2 should say "more than one task event" not "events". 

P24 paragraph 2 needs a comma "To fully characterize the neural responses, we fitted". 

P25 paragraph 1 should probably say "we sampled from similar populations of DN". 

P34 paragraph 3 consider rephrasing the sentence that contains both "dissociation" and "dissociate". 

P37 last line: consider "coordination of cerebellum and cerebral cortex *in* higher order mental..."? 

P38 paragraph 1 citation needed for "kinematics of goal-directed hand actions of others"? 

P38 paragraph 1 commas probably not needed "map visual input, from high-level visual regions, onto..." 

References

- Herzfeld D.J., Kojima Y, Soetedjo R, Shadmehr R (2018) Encoding of error and learning to correct that error by the Purkinje cells of the cerebellum. Nat Neurosci 21:736–743.

- van Es, D.M., van der Zwaag W., and Knapen T. (2019) Topographic Maps of Visual Space in the Human Cerebellum. Current Biol Volume 29, Issue 10p1689-1694.e3May 20.

- De Zeeuw CI, Wylie DR, Stahl JS, Simpson JI. (1995) Phase relations of Purkinje cells in the rabbit flocculus during compensatory eye movements. J Neurophysiol. Nov;74(5):2051-64. doi: 10.1152/jn.1995.74.5.2051.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Summary:

The pituitary gonadotropins, FSH and LH, are critical regulators of reproduction. In mammals, synthesis and secretion of FSH and LH by gonadotrope cells are controlled by the hypothalamic peptide, GnRH. As FSH and LH are made in the same cells in mammals, variation in the nature of GnRH secretion is thought to contribute to the differential regulation of the two hormones. In contrast, in fish, FSH and LH are produced in distinct gonadotrope populations and may be less (or differently) dependent on GnRH than in mammals. In the present manuscript, the authors endeavored to determine whether FSH may be independently controlled by a distinct peptide, cholecystokinin (CCK), in zebrafish.

Strengths:

The authors demonstrated that the CCK receptor is enriched in FSH-producing relative to LH-producing gonadotropes, and that genetic deletion of the receptor leads to dramatic decreases in gonadotropin production and gonadal development in zebrafish. Also, using innovative in vivo and ex vivo calcium imaging approaches, they show that LH- and FSH-producing gonadotropes preferentially respond to GnRH and CCK, respectively. Exogenous CCK also preferentially stimulated FSH secretion ex vivo and in vivo.

Weaknesses:

The concept that there may be a distinct FSH-releasing hormone (FSHRH) has been debated for decades. As the authors suggest that CCK is the long-sought FSHRH (at least in fish), they must provide data that convincingly leads to such a conclusion. In my estimation, they have not yet met this burden. In particular, they show that CCK is sufficient to activate FSH-producing cells, but have not yet demonstrated its necessity. Their one attempt to do so was using fish in which they inactivated the CCK receptor using CRISPR-Cas9. While this manipulation led to a reduction in FSH, LH was affected to a similar extent. As a result, they have not shown that CCK is a selective regulator of FSH.

Our conclusion regarding the necessity of CCK signaling for FSH secretion is based on the following evidence:

(1) CCK-like receptors are expressed in the pituitary gland predominantly on FSH cells.

(2) Application of CCK to pituitaries elicits FSH cell activation and to a much lesser degree activation of LH cells.  (calcium imaging assays)

(3) Application of CCK to pituitaries and by injections in-vivo significantly increased only FSH release.

(4) Mutating the FSH-specific CCK receptor in a different species of fish (medaka) also causes a complete shutdown of FSH production and phenocopies a fsh-mutant phenotype (Uehara, Nishiike et al. 2023).

Taken together, we believe that this data strongly supports the conclusion that CCK is necessary for FSH production and release from the fish pituitary. Admittedly, the overlapping effects of CCK on both FSH and LH cells in zebrafish (evident in both our calcium imaging experiments and especially in the KO phenotype) complicates the interpretation of the phenotype. We speculate that the effect of CCK on LH cells in zebrafish can be caused either by paracrine signaling within the gland or by the effects of CCK on GnRH neurons that were shown to express CCK receptors .

In the current version, we emphasize that CCK also induces LH secretion. Although it does not affect LH to the same extent as FSH, an overlap does exist. This is mentioned in the abstract and discussion.

Moreover, they do not yet demonstrate that the effects observed reflect the loss of the receptor's function in gonadotropes, as opposed to other cell types.

Although there is evidence for the expression of CCK receptor in other tissues, we do show a direct decrease of FSH and LH expression in the gonadotrophs of the pituitary of the mutant fish; taken together with its significant expression in FSH cells compared to the rest of the cells of the pituitary in the cell specific transcriptomic, it is the most reasonable explanation for the mutant phenotype.

Unfortunately, unlike in mice, technologies for conditional knockout of genes in specific cell types are not yet available for our model and cell types. Additional tissue distribution of the three receptors types of CCK was added in supplementary figure 1, from this tissue distribution it can be appreciated how in the pituitary only CCKBRA (our identified CCK receptor) is expressed, while in other tissues it is either not expressed or expressed with the additional CCK receptors that can compensate its activity.

It also is not clear whether the phenotypes of the fish reflect perturbations in pituitary development vs. a loss of CCK receptor function in the pituitary later in life. Ideally, the authors would attempt to block CCK signaling in adult fish that develop normally. For example, if CCK receptor antagonists are available, they could be used to treat fish and see whether and how this affects FSH vs. LH secretion.

While the observed gonadal phenotype of the KO (sex inversed fish) should have a developmental origin since it requires a long time to manifest, the effect of the KO on FSH and LH cells is probably more acute. Unfortunately a specific antagonist that affect only CCKRBA and not the other CCK receptors wasn’t identified yet.

In the Discussion, the authors suggest that CCK, as a satiety factor, may provide a link between metabolism and reproduction. This is an interesting idea, but it is not supported by the data presented. That is, none of the results shown link metabolic state to CCK regulation of FSH and fertility. Absent such data, the lengthy Discussion of the link is speculative and not fully merited.

In the revised manuscript, we provided data to link cck with metabolic status in supplementary figure 1 and modified the discussion to tone down the link between metabolic status to and reproductive state.

Also in the Discussion, the authors argue that "CCK directly controls FSH cells by innervating the pituitary gland and binding to specific receptors that are particularly abundant in FSH gonadotrophs." However, their imaging does not demonstrate innervation of FSH cells by CCK terminals (e.g., at the EM level).

Innervation of the fish pituitary does not imply a synaptic-like connection between axon terminals and endocrine cells. In fact, such connections are extremely rare, and their functionality is unclear. Instead, the mode of regulation between hypothalamic terminals and endocrine cells in the fish pituitary is more similar to "volume transmission" in the CNS, i.e. peptides are released into the tissue and carried to their endocrine cell targets by the circulation or via diffusion. A short explanation was added in lines 395-398 in the discussion

Moreover, they have not demonstrated the binding of CCK to these cells. Indeed, no CCK receptor protein data are shown.

Our revised manuscript  includes detailed experiments showing the activation of the receptor by its homologous ligand, supplementary Figure 1 includes a transactivation  assay of CCK to its receptor and the effect of the different mutants on the activation of the receptor. Unfortunately, no antibody is available against this fish specific receptor (one of the caveats of working with fish models); therefore, we cannot present receptor protein data.

The calcium responses of FSH cells to exogenous CCK certainly suggest the presence of functional CCK receptors therein; but, the nature of the preparations (with all pituitary cell types present) does not demonstrate that CCK is acting directly in these cells.

We agree with the reviewer that there are some disadvantages in choosing to work with a whole-tissue preparation. However, we believe that the advantages of working in a more physiological context far outweigh the drawbacks as it reflects the natural dynamics more precisely. Since our transcriptome data, as well as our ISH staining, show that the CCK receptor is exclusively expressed in FSH cells, it is improbable that the observed calcium response is mediated via a different pituitary cell type.

Indeed, the asynchrony in responses of individual FSH cells to CCK (Figure 4) suggests that not all cells may be activated in the same way. Contrast the response of LH cells to GnRH, where the onset of calcium signaling is similar across cells (Figure 3).

The difference between the synchronization levels of LH and FSH cells activity stems from the gap-junction mediated coupling between LH cells that does not exist between FSH cells(Golan, Martin et al. 2016). Therefore, the onset of calcium response in FSH cells is dependent on the irregular diffusion rate of the peptide within the preparation, whereas the tight homotypic coupling between LH cells generates a strong and synchronized calcium rise that propagates quickly throughout the entire population

The differences in connectivity between LH and FSH cells is mentioned in lines 194-195

Finally, as the authors note in the Discussion, the data presented do not enable them to conclude that the endogenous CCK regulating FSH (assuming it does) is from the brain as opposed to other sources (e.g., the gut).

We agree with the reviewer that, for now, we are unable to determine whether hypothalamic or peripheral CCK are the main drivers of FSH cells. While the strong innervation of the gland by CCK-secreting hypothalamic neurons strengthens the notion of a hypothalamic-releasing hormone and also fits with the dogma of the neural control of the pituitary gland in fish (Ball 1981), more experiments are required to resolve this question.

Reviewer #2 (Public Review):

Summary:

This manuscript builds on previous work suggesting that the CCK peptide is the releasing hormone for FSH in fishes, which is different than that observed in mammals where both LH and FSH release are under the control of GnRH. Based on data using calcium imaging as a readout for stimulation of the gonadotrophs, the researchers present data supporting the hypothesis that CCK stimulates FSH-containing cells in the pituitary. In contrast, LH-containing cells show a weak and variable response to CCK but are highly responsive to GnRH. Data are presented that support the role of CCK in the release of FSH. Researchers also state that functional overlap exists in the potency of GnRH to activate FSH cells, thus the two signalling pathways are not separate. The results are of interest to the field because for many years the assumption has been that fishes use the same signalling mechanism. These data present an intriguing variation where a hormone involved in satiation acts in the control of reproduction.

Strengths:

The strengths of the manuscript are that researchers have shed light on different pathways controlling reproduction in fishes.

Weaknesses:

Weaknesses are that it is not clear if multiple ligand/receptors are involved (more than one CCK and more than one receptor?). The imaging of the CCK terminals and CCK receptors needs to be reinforced.

Reviewer consultation summary: 

The data presented establish sufficiency, but not necessity of CCK in FSH regulation. The paper did not show that CCK endogenously regulates FSH in fish. This has not been established yet.

This is a very important comment, also raised by reviewer 1. To avoid repetition, please see our detailed response to the comment above.

The paper presents the pharmacological effects of CCK on ex vivo preparations but does not establish the in vivo physiological function of the peptide. The current evidence for a novel physiological regulatory mechanism is incomplete and would require further physiological experiments. These could include the use of a CCK receptor antagonist in adult fish to see the effects on FSH and LH release, the generation of a CCK knockout, or cell-specific genetic manipulations.

As detailed in the responses to the first reviewer, we cannot conduct conditional, cellspecific gene knockout in our model. However we did conducted KO and show the direct effect on FSH and LH secretion together with physiological characterisation of the mutant.

Zebrafish have two CCK ligands: ccka, cckb and also multiple receptors: cckar, cckbra and cckbrb. There is ambiguity about which CCK receptor and ligand are expressed and which gene was knocked out.

In the revised manuscript, we clarified which of the receptors are expressed (CCKRBA) and which receptor is targeted. We also provided data showing the specificity of the receptors (both WT and mutant) to the ligands. Supplementary 1 shows receptor cross-activation. The method also specifies the exact NCBI ID numbers of the targeted receptor and the antibody used for the immunostaining.

Blocking CCK action in fish (with receptor KO) affects FSH and LH. Therefore, the work did not demonstrate a selective role for CCK in FSH regulation in vivo and any claims to have discovered FSHRH need to be more conservative.

We agree with the reviewer that the overlap in the effect of CCK measured in the calcium activation of cells and in the KO model does not allow us to conclude selectivity. In this context, it is crucial to highlight that CCKRBA exhibits high expression on FSH cells but not on LH cells. Therefore, the effect of CCK on LH cells is likely paracrine or through GnRH neurons that were shown to express CCK receptors. In the current version, we emphasize that CCK also induces LH secretion. Although it does not affect LH to the same extent as FSH, an overlap does exist. This is mentioned in the abstract and discussion.

The labelling of the terminals with anti-CCK looks a lot like the background and the authors did not show a specificity control (e.g. anti-CCK antibody pre-absorbed with the peptide or anti-CCK in morphant/KO animals).

Figures colours had been updated to better visualise the specific staining of the antibody. Also, The same antibody had been previously used to mark CCK-positive cells in the gut of the red drum fish(Webb, Khan et al. 2010) , where a control (pre-absorbed with the peptide) experiment had been conducted.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Abstract:

The authors have not yet established that CCK is the primary regulator of FSH in vivo.

In the new version, we highlight the leading effect of CCK on the reproductive axis, which includes FSH and LH.

Introduction:

The authors need to make clear earlier in the Introduction that fish have two types of gonadotropes. This information comes too late (last paragraph) currently.

Added in line 42

They should discuss relevant data on the differential regulation of FSH and LH in fish, as a rationale for looking for different releasing factors.

This has been discussed in the first paragraph of the introduction

In the last sentence of the penultimate paragraph, the authors assume that it must be a hypothalamic factor that regulates FSH. Why is this necessarily the case? Are there data indicating that a hypothalamic factor is required for FSH production in fish?

This has been mentioned in the discussion, we do not deny that circulating CCK or CCK from other brain areas might affect FSH secretion in the pituitary (line 402-404). However, as the hypothalamus serves as the main gateway from the brain to the pituitary and contains hypophysiotropic CCK neurons it is the most reasonable assumption.

Results:

In the first paragraph, the authors reference three types of CCK receptors, only one of which is expressed in the pituitary. The specific receptor should be named here.

The receptor name and NCBI id had been added in this paragraph.

Figure 1: What specificity controls were used for the ISH in Figure 1?

HCR- The method used to identify RNA expression and developed by Molecular Instruments (https://www.molecularinstruments.com/hcr-rnafish-protocols), do not require specific control as had been previously done with older ISH methods. The use of multiple short probes assure the specificity to the RNA.More over the expression is specific to the targeted cells.

In Figure 1D, the red square is missing in the KO fish (at low magnification).

This was fixed in the updated version.

In Figure 1G, the number of dots does not correspond to the number of animals described in the figure legend. Does each point represent an animal?

Each dot represent a fish. The order of the numbers in the legend didn’t match the order in the graph, this had been fixed in the last version

Figure 2A: It is not clear that all FSH (GFP) cells are double-labeled. Should all double-labeled cells appear white? Many appear as green. Some quantification of the proportion of co-labeling is needed. Also, the scale bars are too small to read. Perhaps add the size of the scale bars to the legend.

They are all double-labeled, as can be seen by the single-color images, since GFP fluorescence is stronger than RCaMP fluorescence, the double-labelling might be seen a green cells; a scale bar was added.

Figure 2C: Is the synchronous activity of LH cells here dependent on endogenous GnRH? Can these events be blocked with a GnRH receptor antagonist?

We currently do not have enough data to support this hypothesis and the in vivo 2 photon system is not optimal to answer these questions since these are spontaneous events which are difficult to predict. This is the main reason we moved to an ex vivo system. The similar response we receive when applying GnRH in the ex vivo system support it is GnRH activation.

Figure 4C: As some LH cells respond to CCK, can the authors really claim that CCK is a selective regulator of FSH? What explains the heterogeneity in the response of LH cells to CCK?

In this version, we highlight that CCK directly activates FSH but it is also affecting LH to some extent. However it is clear that the effect on FSH cells is more significant.

Figures 5A and B: With larger Ns, some of the trends might be significant (e.g., GnRH stimulated FSH release and CCK stimulated LH release).

Though there is a trend, the values in the Y axis reveal that the trend of response of FSH to GnRH and LH to CCK is lower then the distribution of the basal response (the before) in all of the graphs. Hence we do not believe a larger N will affect those results. We added the range of the secreted hormones concentrations in the result description to emphasize the difference in values,

Figures 5C and D: What explains the lack of an increase in LH secretion following GnRH treatment?

We did not measure LH Secretion in the plasma as we didn’t have enough blood, we do see an increase in LH transcription (see supplementary figure 5 – figure supplement 1)

Also, as mRNA levels were measured (in C), reference should be made to expression rather than transcription. Not all changes in mRNA levels reflect changes in transcription.Also, remove transcription from the legend. Reference to supplementary Figure 4 in the legend should be supplementary Figure 6. Finally, in C and D, distinguish males from females (as in 5A and B).

Modifications had been done according to the reviewer suggestions.

Figure legends:

The figure legends are very long. One way to shorten them is to remove descriptions of the results. The legends should indicate what is in each figure, not the results of the experiments.

Modifications had been done according to the reviewer suggestions.

Sample sizes should be spelled out in the legends, as they are not in the M&M.

We made sure all sample sizes are mentioned in the legend

Materials and Methods:

Section 1.1 can be removed as it repeats content presented elsewhere.

This section was removed

Section 1.5: It is unclear what this means: "blinding was not applied to ensure tractability" Please clarify.

This section was removed

Reviewer #2 (Recommendations For The Authors):

It appears that zebrafish have two ligands: ccka, cckb. Also multiple receptors: cckar, cckbra and cckbrb. Authors need to discuss this and clearly state which ligand and which receptor they are referring to in the manuscript.

We discussed the receptor type in the first paragraph of the results, the exact synthetic peptide used is described in the methods. The 8 amino acids of the mature CCK peptide are the same between CCKa and CCKb. A sentence regarding the specificity of the antibody to the mature CCK peptide was added in line 101.

"to GnRH puff application (300 μl of 30 μg/μl)"; (250 μl of 30 μg/ml CCK)

Please give the final concentration to make it easy on the readers of the data.

The molarity of the final concentration was added.

(2.4) Differential calcium response underlies differential hormone. This section is a bit confusing to read, for example:

"For that, we collected the medium perfused through our ex vivo system (Fig. 2a) and measured LH and FSH levels using a specific ELISA validated for zebrafish [31] while monitoring the calcium activity of the cells."

So the authors did the ELISA while monitoring the activity (?). This sentence does not make sense: please rewrite it.

We modified this sentence  in line 308-311

To functionally validate the importance of CCK signalling we used CRISPR-cas9 to generate loss-of-function (LOF) mutations in the pituitary- CCK receptor gene.

The authors need to clearly state WHICH gene they inactivated: Zebrafish have three CCK-receptors, so "the pituitary receptor gene" needs to be defined.

Was added again in line 107, and is mentioned in the methods

Figure 3 is a crucial figure!

Figure 3B: The data are not very convincing. Please state how thick the sections are in the figure legend (assuming these are adult pituitaries),

Added in the legend (figure 1C in the new version), slice thickness and adult fish.

Please show at least the merged image a high magnification view of the co-localization of the receptor with the cells.

This is figure 1 in the new revision, a magnified figure was added

Please give the scale bar size for 3B.

Scales for all images were added

Figure 3C: the co-localization of the terminals of the CCK and FSH cells shows very few cells expressing close to terminals.

Important: Because the labelling of the terminals with anti-CCK looks a lot like the background, it is very important to show the control (anti-CCK antibody pre-absorbed with the peptide). The authors should have these data. The photo needs to have been taken at the same gain (contrast) and the photo showing the terminals.

This is  a commercial antibody that had been previously validated for CCK in fish. The co-localization pattern resembles GnRH innervation in the pituitary. In fish when hypothalamic neurons innervate the pituitary they do not innervate all the cells, as this is an endocrine system, the peptide can travel to neighbouring cells via diffusion or aided blood flow (Golan, Zelinger et al. 2015) ).  The images reveal the direct innervation of CCK in the pituitary and its proximity to FSH cells.

Figure 4c, on right. The text seems to be stretched as if the photo was adjusted without locking the aspect ratio. Please check the original images.

This has been fixed

Can the authors use different pseudo colours? Differentiating a double label of white versus yellow is very difficult, and thus the photo is not very convincing.

This had been changed to green and magenta

What is meant by "CCK-AB" antibody? Perhaps anti-CCK would be a better label

This has been fixed

Figure 5A: increase the magnification of the insets; the structure of the gonads is very difficult to see with clarity in these low mag images. The most obvious way to improve this figure is to reduce or eliminate the pie graph (not really necessary) and show a high magnification (and larger) image of the gonadal structure.

This is figure 1 in the new version, with magnification of the gonad next to each body section.

Discussion:

" Moreover, in the zebrafish, as well as in other species, the functional overlap in gonadotropin signalling pathways is not limited to the pituitary but is also present in the gonad, through the promiscuity of the two gonadotropin receptors"<br /> The reasoning of this sentence is not clear: zebrafish do not use GnRH to control reproduction: they lack GnRH1 through genomic rearrangement (see Whitlock, Postlethwait and Ewer 2019) and KO of GnRH2/GnRH3 does not affect reproduction.

While GnRH KO model indicate a redundancy of GnRH in this axis in zebrafish, there is also ample evidence for its importance in regulating reproduction such as its effect on gonadotropin (Golan, Martin et al. 2016) and its use in spawning inductions in fish (Mizrahi and Levavi-Sivan 2023). We believe it is currently too soon to conclude that GnRH signalling is completely non relevant to reproduction in cyprinids.  

Reviewing Editor (Recommendations For The Authors):

It would be interesting to see calcium imaging experiments in the CCKR receptor mutants to establish a more direct connection between peptide action and activity.

We added a receptor assay that reflect the non-activation of the mutated receptors by CCK (supplementary figure 1) , and compared it to the wild type that is activated. This show that: 1) CCK directly activate our identified receptor in FSH cells. 2) the mutated receptors are non-active.

"all homozygous fish (CCKR+12/+7/-1/ CCKR+12/+7/-1, n=12)"

It may be better to write the genotype of fish separately as CCKR+12/+12, CCKR+7/+7 and CCKR-1/-1, n=12) otherwise it seems as if all alleles occurred together in the same fish.

Modified according to the reviewer request

In Figure 1 scale bar legends are very small. 

Description of the scale bars were added to the all the legends

Figure 1 legend "On the top right of each panel is the gender distribution" - fish have no gender but sex.

Modified according to the reviewer request

The authors should endeavour to improve the presentation of the figures. They should use a sans-serif font and check that text is not cut at the edge of figure panels, that scale bars are uniform and clearly labelled and fonts are of similar size and clearly legible. E.g. labels of the fish brain of Fig3A are very small.

We modified all the figures to adapt the font and the scales, we increased the size of the image in Figure 3a to make the labels clearer.

Please use the elife format to name supplementary figures, as Figure X - Figure Supplement Y (each supplement associated with one of the main figures).

Fixed

Peptide concentrations in the ex vivo experiments should also be given as molar concentrations not only as '250 μl of 30 μg/ml CCK'.

Fixed

"In contrast, FSH cells responded with a very low calcium rise in hormonal secretion in response to GnRH" - a very low rise in hormonal secretion

Fixed

Please clarify why you used a GnRH synthetic agonist and not the native peptide.

It is commonly used for spawning induction in fish (line 245); it has also been shown to directly affect the secretion of LH and FSH (Biran, Golan et al. 2014, Biran, Golan et al. 2014, Mizrahi, Gilon et al. 2019) , added to line 245.

References

Ball, J. (1981). "Hypothalamic control of the pars distalis in fishes, amphibians, and reptiles." General and comparative endocrinology 44(2): 135-170.

Biran, J., M. Golan, N. Mizrahi, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2014). "Direct regulation of gonadotropin release by neurokinin B in tilapia (Oreochromis niloticus)." Endocrinology 155(12): 4831-4842.

Biran, J., M. Golan, N. Mizrahi, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2014). "LPXRFa, the Piscine Ortholog of GnIH, and LPXRF Receptor Positively Regulate Gonadotropin Secretion in Tilapia (Oreochromis niloticus)." Endocrinology 155(11): 4391-4401.

Golan, M., A. O. Martin, P. Mollard and B. Levavi-Sivan (2016). "Anatomical and functional gonadotrope networks in the teleost pituitary." Scientific Reports 6: 23777.

Golan, M., E. Zelinger, Y. Zohar and B. Levavi-Sivan (2015). "Architecture of GnRH-Gonadotrope-Vasculature Reveals a Dual Mode of Gonadotropin Regulation in Fish." Endocrinology 156(11): 4163-4173.

Mizrahi, N., C. Gilon, I. Atre, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2019). "Deciphering Direct and Indirect Effects of Neurokinin B and GnRH in the Brain-Pituitary Axis of Tilapia." Front Endocrinol (Lausanne) 10: 469.

Mizrahi, N. and B. Levavi-Sivan (2023). "A novel agent for induced spawning using a combination of GnRH analog and an FDA-approved dopamine receptor antagonist." Aquaculture 565: 739095.

Uehara, S. K., Y. Nishiike, K. Maeda, T. Karigo, S. Kuraku, K. Okubo and S. Kanda (2023). "Cholecystokinin is the follicle-stimulating hormone (FSH)-releasing hormone." bioRxiv: 2023.2005.2026.542428.

Webb, K. A., Jr., I. A. Khan, B. S. Nunez, I. Rønnestad and G. J. Holt (2010). "Cholecystokinin: molecular cloning and immunohistochemical localization in the gastrointestinal tract of larval red drum, Sciaenops ocellatus (L.)." Gen Comp Endocrinol 166(1): 152-159.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews: 

Reviewer #1 (Public Review):

The authors introduce a computational model that simulates the dendrites of developing neurons in a 2D plane, subject to constraints inspired by known biological mechanisms such as diffusing trophic factors, trafficked resources, and an activity-dependent pruning rule. The resulting arbors are analyzed in terms of their structure, dynamics, and responses to certain manipulations. The authors conclude that 1) their model recapitulates a stereotyped timecourse of neuronal development: outgrowth, overshoot, and pruning 2) Neurons achieve near-optimal wiring lengths, and Such models can be useful to test proposed biological mechanisms- for example, to ask whether a given set of growth rules can explain a given observed phenomenon - as developmental neuroscientists are working to understand the factors that give rise to the intricate structures and functions of the many cell types of our nervous system. 

Overall, my reaction to this work is that this is just one instantiation of many models that the author could have built, given their stated goals. Would other models behave similarly? This question is not well explored, and as a result, claims about interpreting these models and using them to make experimental predictions should be taken warily. I give more detailed and specific comments below.  

We thank the reviewer for the summary of the work. But the criticism “that this is one instantiation of many models [we] could have built” is unfair as it can apply to any model. We chose one of the most minimalistic models which implements known biological mechanisms including activity-independent and -dependent phases of dendritic growth, and constrained parameters based on experimental data. We compare the proposed model to other alternatives in the Discussion section. In the revised manuscript, we additionally investigate the sensitivity of model output to variations of specific parameters, as explained below.

Point 1.1. Line 109. After reading the rest of the manuscript, I worry about the conclusion voiced here, which implies that the model will extrapolate well to manipulations of all the model components. How were the values of model parameters selected? The text implies that these were selected to be biologically plausible, but many seem far off. The density of potential synapses, for example, seems very low in the simulations compared to the density of axons/boutons in the cortex; what constitutes a potential synapse? The perfect correlations between synapses in the activity groups is flawed, even for synapses belonging to the same presynaptic cell. The density of postsynaptic cells is also orders of magnitude of, etc. Ideally, every claim made about the model's output should be supported by a parameter sensitivity study. The authors performed few explorations of parameter sensitivity and many of the choices made seem ad hoc.  

We have performed detailed sensitivity analysis on the model parameters mentioned by the reviewer, including (I) the density of postsynaptic cells (somatas), (II) the density of potential synapses, and (III) the level of correlations between synapses. 

(I) While the density of postsynaptic cells in our baseline model seems a bit low, at least when compared to densities observed in adulthood (Keller et al., 2018), we explored how altering this value affects the model dynamics. We found that the postsynaptic cell density does not affect the timing of dendritic outgrowth, overshoot and synaptic pruning. It only changes the final size of the dendritic arbor and the resulting number of connected synapses. This analysis is now included in Supplementary Figure 3-2.

(II) The density of potential synapses and the density of connected synapses that we used in the manuscript are already in the range of densities that can be found in the literature (Leighton et al., 2024; Ultanir et al., 2007; Glynn et al., 2011; Yang et al., 2014), some of which we already cited in the original submission.

A potential concern might be that the rapid slowing down of growth in the model could be due to a depletion of potential synapses. To illustrate that this is not the case, we showed that the number of available potential synapses over the time course of the simulations remains high (Figure 3, new panel e). Therefore, the initial density of potential synapses is sufficient and does not affect the final density of connected synapses.

To further illustrate the robustness of our model dynamics to longer simulation times, we added a new supplementary figure (Supplementary Figure 3-1).

These new figure additions (Figure 3e, Supplementary Figure 3-1, and Supplementary Figure 3-2) and their implications for the model dynamics are discussed in the Results section of the revised paper:

p.9 line 198, “After the initial overshoot and pruning, dendritic branches in the model stay stable, with mainly small subbranches continuing to be refined (Figure 3-Figure Supplement 1). This stability in the model is achieved despite the number of potential synaptic partners remaining high (Figure 3e), indicating a balance between activity-independent and activitydependent mechanisms. The dendritic growth and synaptic refinement dynamics are independent of the postsynaptic somata densities used in our simulations (Figure 3-Figure Supplement 2). Only the final arbor size and the number of connected synapses decrease with an increase in the density of the somata, while the timing of synaptic growth, overshoot and pruning remains the same (Figure 3-Figure Supplement 2).”

We also added more details to the description of our model in the Methods section:

p.24 line 615, “For all simulations in this study, we distributed nine postsynaptic somata at regular distances in a grid formation on a 2-dimensional 185 × 185 pixel area, representing a cortical sheet (where 1 pixel = 1 micron, Figure 4). This yields a density of around 300 neurons per 𝑚𝑚2 (translating to around 5,000 per 𝑚𝑚3, where for 25 neurons in Figure 3Figure Supplement 2 this would be around 750 neurons per 𝑚𝑚2 or 20,000 per 𝑚𝑚3). The explored densities are a bit lower than compared to neuron densities observed in adulthood (Keller et al., 2018). In the same grid, we randomly distributed 1,500 potential synapses, yielding an initial density of 0.044 potential synapses per 𝜇𝑚2 (Figure 3e). At the end of the simulation time, around 1,000 potential synapses remain, showing that the density of potential synapses is sufficient and does not significantly affect the final density of connected synapses. Thus, the rapid slowing down of growth in our model is not due to a depletion of potential synaptic partners. The resulting density of stably connected synapses is approximately 0.015 synapses per 𝜇𝑚2 (around 60 synapses stabilized per dendritic tree, Figure 3b). This density compares well to experimental findings, where, especially during early development, synaptic densities are described to be within a range similar to the one observed in our model (Leighton et al., 2024; Ultanir et al., 2007; Glynn et al., 2011; Yang et al., 2014; Koshimizu et al., 2009; Tyler and Pozzo-Miller, 2001).”

(III) Lastly, we investigated how the correlation between synapses of the same activity group might affect our conclusions. As correlations in our model mainly arise from patterns of spontaneous activity which are abundant in early postnatal development (retinal waves (Ackman et al., 2012) or endogenous activity in the form of highly synchronized events involving a large fraction of the cells (Siegel et al., 2012), we explored varying the correlations within each activity group, across activity groups and combinations of both. While this analysis supported our previously described intuition on how competition between synaptic activities should drive activity-dependent refinement, recently a study found direct evidence for such subcellular refinement of synaptic inputs specifically dependent on spontaneous activity between retinal ganglion cell axons and retinal waves in the superior colliculus (Matsumoto et al., 2024). The new analysis confirmed our earlier results that the competition between activity groups leads to activity-dependent refinement and yielded further insight into how the studied activity correlations can affect the competition. Those results are presented in a completely new figure (new Figure 5, supported by the Supplementary Figure 5-1 and 5-2) and discussed in the Results section:

p.11 line 249, “Group activity correlations shape synaptic overshoot and selectivity competition across synaptic groups.

Since correlations between synapses emerge from correlated patterns of spontaneous activity abundant during postnatal development (Ackman et al., 2012; Siegel et al., 2012), we explored a wide range of within-group correlations in our model (Figure 5a). Although a change in correlations within the group has only a minor effect on the resulting dendritic lengths (Figure 5b) and overall dynamics, it can change the density of connected synapses and thus also affect the number of connected synapses to which each dendrite converges throughout the simulations (Figure 5c,e). This is due to the change in specific selectivity of each dendrite which is a result of the change in within-group correlations (Figure 5d). While it is easier for perfectly correlated activity groups to coexist within one dendrite (Figure 5-Figure Supplement 1a, 100%), decreasing within-group correlations increases the competition between groups, producing dendrites that are selective for one specific activity group (60%, Figure 5d, Figure 5-Figure Supplement 1a). This selectivity for a particular activity group is maximized at intermediate (approximately 60%) within-group correlations, while the contribution of the second most abundant group generally remains just above random chance levels (Figure 5-Figure Supplement 1a). Further reducing within-group correlations (20%, Figure 5a) causes dendrites to lose their selectivity for specific activity groups due to the increased noise in the activity patterns (20%, Figure 5a). Overall, reducing within-group correlations increases synapse pruning (Figure 5f, bottom), also found experimentally (Matsumoto et al., 2024) as dendrites require an extended period to fine-tune connections aligned with their selectivity biases. This phenomenon accounts for the observed reduction in both the density and number of synapses connected to each dendrite.

In addition to the within-group correlations, developmental spontaneous activity patterns can also change correlations between groups as for example retinal waves propagated in different domains (Feller et al., 1997) (Figure 5-Figure Supplement 2). An increase in between-group correlations in our model intuitively decreases competition between the groups since fully correlated global events synchronize the activity of all groups (Figure 5-Figure Supplement 2). The reduction in competition reduces pruning in the model, which can be recovered by combining cross-group correlations with decreased within-group correlations (Figure 5-Figure Supplement 2). Our simulations show that altering the correlations within activity groups increases competition (by lowering the within-group correlations) or decreases competition (by raising the across-group correlations). Hence, in our model, competition between activity groups due to non-trivially structured correlations is necessary to generate realistic dynamics between activity-independent growth and activity-dependent refinement or pruning.

In sum, our simulations demonstrate that our model can operate under various correlations in the spike trains. We find that the level of competition between synaptic groups is crucial for the activity-dependent mechanisms to either potentiate or depress synapses and is fully consistent with recent experimental evidence showing that the correlation between spontaneous activity in retinal ganglion cells axons and retinal waves in the superior colliculus governs branch addition vs. elimination (Matsumoto et al., 2024)."

Precise details on the implementation of the changed activity correlations were added to the Methods section:

p. 25 line 638, “Within-group and across-group activity correlations. For the decreased withingroup correlations, we generated parent spike trains for each individual group with the firing rate 𝑟𝑖𝑛 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ 𝑃𝑖𝑛 (e.g., 𝑃𝑖𝑛 = 100%; 60%; 20%, Figure 5). All the synapses of the same group share the same parent spike train and the remaining spikes for each synapse are uniquely generated with the firing rate 𝑟𝑟𝑒𝑠𝑡 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ (1 − 𝑃𝑖𝑛) (e.g., (1 − 𝑃𝑖𝑛) = 0%; 40%; 80%), resulting in the desired firing rate 𝑟𝑡𝑜𝑡𝑎𝑙 (see Table 1). For the increase in across-group correlations, we generated one master spike train with the firing rate 𝑟𝑐𝑟𝑜𝑠𝑠 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ 𝑃𝑐𝑟𝑜𝑠𝑠 for all the synapses of all groups (e.g., 𝑃𝑐𝑟𝑜𝑠𝑠 = 5%; 10%; 20%, Figure 5-Figure Supplement 2). This master spike train is shared across all groups and then filled up according to the within-group correlation (if not specified differently 𝑃𝑖𝑛 = 1 − 𝑃𝑐𝑟𝑜𝑠𝑠 to maintain the rate 𝑟𝑡𝑜𝑡𝑎𝑙). In all the cases, also in those where the change in across-group correlations is combined with the change in within-group correlations, the remaining spikes for each synapse are generated with a firing rate 𝑟𝑟𝑒𝑠𝑡 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ (1 − 𝑃𝑖𝑛 − 𝑃𝑐𝑟𝑜𝑠𝑠) to obtain an overall desired firing rate of 𝑟𝑡𝑜𝑡𝑎𝑙.”

Point 1.2. Many potentially important phenomena seem to be excluded. I realize that no model can be complete, but the choice of which phenomena to include or exclude from this model could bias studies that make use of it and is worth serious discussion. The development of axons is concurrent with dendrite outgrowth, is highly dynamic, and perhaps better understood mechanistically. In this model, the inputs are essentially static. Growing dendrites acquire and lose growth cones that are associated with rapid extension, but these do not seem to be modeled. Postsynaptic firing does not appear to be modeled, which may be critical to activity-dependent plasticity. For example, changes in firing are a potential explanation for the global changes in dendritic pruning that occur following the outgrowth phase.  

Thanks to the reviewer for bringing up these important considerations. We do indeed write in the Introduction (e.g. lines 36-76) which phenomena we include in the model and why. The Discussion also compares our model to others (lines 433-490), pointing out that most models either focus on activity-independent or activity-dependent phases. We include both, combining the influence of both molecular gradients and growth factors as well as activity-dependent connectivity refinements instructed by spontaneous activity. We consider our model a tractable, minimalist mechanistic model which includes both activity-independent and activity-dependent aspects. 

Regarding postsynaptic firing, this is indeed super relevant and an important point to consider. In one of our recent publications (Kirchner and Gjorgjieva, 2021), we studied only an activity-dependent model for the organization of synaptic inputs on non-growing dendrites which have a fixed length. There, we considered the effect of postsynaptic firing (via a back-propagating action potential) and demonstrated that it plays an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron. For example, we showed that it could lead to the emergence of retinotopic maps on the dendritic tree which have been found experimentally (Iacaruso et al., 2017). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree. This is now also discussed in the Discussion section of the revised manuscript:

p. 21 line 491, “Although we did not explicitly model postsynaptic firing, our previous work with static dendrites has shown that it can play an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron (Kirchner and Gjorgjieva, 2021). For example, we showed that it could lead to the emergence of retinotopic maps on the dendritic tree which have been found experimentally (Iacaruso et al., 2017). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree.”

Including the concurrent development of axons in the model is indeed very interesting. In fact, a recent tour-de-force techniques paper found similar to what we assume. Hebbian activity-dependent dynamics of axonal branches of retinal ganglion cells experiencing spontaneous activity in relation to retinal waves in the superior colliculus (Matsumoto et al., 2024). New branches tend to be added at the locations where spontaneous activity of individual branches is more correlated with retinal waves, whereas asynchronous activity is associated with branch elimination. We suspect the same Hebbian activity-dependent dynamics to apply also to dendritic growth. 

To address simultaneous dynamic axons to our growing dendrites, in the revised version of the manuscript, we included a simplified form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, which come from axons of presynaptic partners. We explored different median lifetimes of synapses in combination with several distances with which a synapse can move in the simulated space (new Supplementary Figure 3-3). Our results show that dynamically moving synapses only affect the dynamics and stability of our model when the rate of moving synapses combined with the distance of moving synapses is faster than the dendritic growth. In scenarios in which synapses can move across large distances, dendrites get further destabilized due to synapses transferring from one dendrite to another, perturbing the attractor fields of the potential synapses even in late phases of the simulations. Besides such non-biological scenarios, dynamically moving synapses do not affect the model dynamics too much. Thus, they mostly add additional noise and variability to the growth and pruning without changing the timing and amplitude of the dynamics. These results are discussed in the results section of the revised manuscript:

p.9 line 207, “The development of axons is concurrent with dendritic growth and highly dynamic Matsumoto et al. (2024). To address the impact of simultaneously growing axons, we implemented a simple form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, originating from the axons of presynaptic partners (Figure 3-Figure Supplement 3). When potential synapses can move rapidly (median lifetime of 1.8 hours), the model dynamics are perturbed quite substantially, making it difficult for the dendrites to stabilize completely (Figure 3–Figure Supplement 3c). However, slowly moving potential synapses (median lifetime of 18 hours) still yield comparable results (Figure 3-Figure Supplement 3). The distance of movement significantly influenced results only when potential synaptic lifetimes were short. For extended lifetimes, the moving distance had a minor impact on the dynamics, predominantly affecting the time required for dendrites to stabilize. This was the result of synapses being able to transfer from one dendrite to another, potentially forming new long-lasting connections even at advanced stages of synaptic refinement. In sum, our results show that potential axonal dynamics only affect the stability of our model when these dynamics are much faster than dendritic growth.”

Precise details on the implementation of the dynamically moving synapses and their synaptic lifetimes are now in the Methods section:

p. 25 line 650, “Dynamically moving synapses. For the moving synapses we introduced lifetimes for each synapse, randomly sampled from a log-normal distribution with median 1.8h (for when they move frequently), 4.5h or 18h (for when they move rarely) and variance equal to 1 (Figure 3-Figure Supplement 3b). The lifetime of a synapse decreases only when the synapse is not connected to any of the dendrites (i.e., is a potential synapse). When the lifetime of a synapse expires, the synapse moves to a new location with a new lifetime sampled from the same log-normal distribution. This enables synapses to move multiple times throughout a simulation. The exact locations and distances to which each synapse can move are determined by a binary matrix (dimensions: 𝑝𝑖𝑥𝑒𝑙𝑑𝑖𝑠𝑡𝑎𝑛𝑐𝑒 × 𝑝𝑖𝑥𝑒𝑙𝑑𝑖𝑠𝑡𝑎𝑛𝑐𝑒) representing a ring (annulus) with the inner radius 𝑑/4 and outer radius 𝑑/2 , where the synapse location is at the center of the matrix. All the locations of the matrix within the ring boundaries (between the inner radius and outer radius) are potential locations to which the synapse can move. The synapse then moves randomly to one of the possible locations where no other synapse or dendrite is located. For the movement distances, we chose the ring dimensions 3 × 3, 25 × 25 and 101 × 101, yielding the moving distances (radii) of 1 pixel per movement, 12 pixels per movement and 50 pixels per movement (𝑟 = (𝑑−1)/2). These pixel distances represent small movements, as much as a dendrite can grow in one step (1 micron), and larger movements which are far enough so that the synapse will not attract the same branches again (12 microns) or far enough so that it might attract a completely different dendrite (50 microns, Figure 3-Figure Supplement 3a).”

Point 1.3. Line 167. There are many ways to include activity -independent and -dependent components into a model and not every such model shows stability. A key feature seems to be that larger arbors result in reduced growth and/or increased retraction, but this could be achieved in many ways (whether activity dependent or not). It's not clear that this result is due to the combination of activity-dependent and independent components in the model, or conceptually why that should be the case.

We never argued for model uniqueness. There are always going to be many different models (at different spatial and temporal scales, at different levels of abstraction). We can never study all of them and like any modeling study in systems neuroscience we have chosen one model approach and investigated this approach. We do compare the current model to others in the Discussion. If the reviewers have a specific implementation that we should compare our model to as an alternative, we could try, but not if this means doing a completely separate project.

Point 1.4. Line 183. The explanation of overshoot in terms of the different timescales of synaptic additions versus activity-dependent retractions was not something I had previously encountered and is an interesting proposal. Have these timescales been measured experimentally? To what extent is this a result of fine-tuning of simulation parameters?  

We found that varying the amount of BDNF controls the timescale of the activity-dependent plasticity (see our Figure 6c). Hence, changing the balance between synaptic additions vs. retractions is already explored in Figure 6e and f. Here we show that the overshoot and retraction does not have to be fine-tuned but may be abolished if there is too much activity-dependent plasticity. 

Regarding the relative timescales of synaptic additions vs. retractions: since the first is mainly due to activity-independent factors, and the second due to activity-dependent plasticity, the questions is really about the timescales of the latter two. As we write in the Introduction (lines 61-63), manipulating activity-dependent synaptic transmission has been found to not affect morphology but rather the density and specificity of synaptic connections (Ultanir et al. 2007), supporting the sequential model we have (although we do not impose the sequence, as both activity-independent and activitydependent mechanisms are always “on”; but note that activity-dependent plasticity can only operate on synapses that have already formed).

The described results are robust to parameter variations (performed on the postsynaptic density, potential synapse density, and within- and across-group correlations) as described in the reply to reviewer #1 point 1.1.

Point 1.5. Line 203. This result seems at odds with results that show only a very weak bias in the tuning distribution of inputs to strongly tuned cortical neurons (e.g. work by Arthur Konnerth's group). This discrepancy should be discussed.  

First, we note that the correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter, but is rather a property of correlated spontaneous activity. 

Nonetheless, there is some variability in what the experimental data show. Many studies have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al., 2011; Takahashi et al., 2012; Winnubst et al., 2015; Gökçe et al., 2016; Wilson et al., 2016; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al., 2018; Kerlin et al., 2019; Ju et al., 2020, Hedrick et al., 2022, Hedrick et al., 2024). Interestingly, some in vivo studies have reported lack of fine-scale synaptic organization (Varga et al., 2011; X. Chen et al., 2011; T.-W. Chen et al., 2013; Jia et al., 2010; Jia et al., 2014), while others reported clustering for different stimulus features in different species. For example, dendritic branches in the ferret visual cortex exhibit local clustering of orientation selectivity but do not exhibit global organization of inputs according to spatial location and receptive field properties (Wilson et al. 2016; Scholl et al., 2017). In contrast, synaptic inputs in mouse visual cortex do not cluster locally by orientation, but only by receptive field overlap, and exhibit a global retinotopic organization along the proximal-distal axis (Iacaruso et al., 2017). We proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity similar to the BDNF-proBDNF model that we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021). This is now also discussed in the Discussion section of the revised manuscript:

p. 20 line 471, “The correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter, but is rather a property of spontaneous activity. Nonetheless, there is some variability in what the experimental data show. Many have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al., 2011; Winnubst et al., 2015; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al., 2018; Takahashi et al., 2012; Gökçe et al., 2016; Wilson et al., 2016; Kerlin et al., 2019; Ju et al., 2020; Hedrick et al., 2022, 2024). Other studies have reported lack of fine-scale synaptic organization (Chen et al., 2013; Varga et al., 2011; Chen et al., 2011; Jia et al., 2010, 2014). Interestingly, some of these discrepancies might be explained by different species showing clustering with respect to different stimulus features (orientation or receptive field overlap) (Scholl et al., 2017; Wilson et al., 2016; Iacaruso et al., 2017). Our prior work proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity as we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021).”

Point 1.6. Line 268. How does the large variability in the size of the simulated arbors relate to the relatively consistent size of arbors of cortical cells of a given cell type? This variability suggests to me that these simulations could be sensitive to small changes in parameters (e.g. to the density or layout of presynapses).  

We again thank the reviewer for the detailed explanation and feedback on parameters that should be tested in more detail. We have explored several of the suggested model parameters and believe that we have managed to explain and illustrate their effects on the model's dynamics clearly. The precise changes are explained in the reply to point 1.1 and are now available in the revised version of the manuscript.

Point 1.7. The modeling of dendrites as two-dimensional will likely limit the usefulness of this model. Many phenomena- such as diffusion, random walks, topological properties, etc - fundamentally differ between two and three dimensions.  

Indeed, there are many differences between two and three dimensions. We have ongoing work that extends the current model to 3D but is beyond the scope of the current paper. In systems neuroscience, people have found very interesting results making such simplified geometric assumptions about networks, for instance the one-dimensional ring model has been used to uncover fundamental insights about computations even though highly simplified and abstracted. We are convinced that our model, especially with the new sensitivity analysis, makes interesting and novel contributions and predictions.

Point 1.8. The description of wiring lengths as 'approximately optimal' in this text is problematic. The plotted data show that the wiring lengths are several deviations away from optimal, and the random model is not a valid instantiation of the 2D non-overlapping constraints the authors imposed. A more appropriate null should be considered.  

We appreciate the reviewer’s feedback regarding the use of the term “approximately optimal” in describing wiring lengths. We acknowledge that our initial terminology was imprecise and could be misleading. We had previously referred to the minimal wiring length as the optimal wiring length, which does not fully capture the nuances of neuronal wiring optimization. As noted in prior literature, such as the work by Hermann Cuntz (Cuntz et al., 2010 & 2012), neurons can optimize their wiring beyond simply minimizing dendritic length.

To address this issue, to better capture the balance between wiring minimization and functional constraints, such as conduction delays, we have developed a new modeling approach based on minimum spanning trees with a balancing factor (Cuntz et al., 2010 & 2012). This factor modulates the trade-off between minimizing wiring length and accounting for conduction delays from synapses to the soma. Specifically, the model assumes a balance between minimizing the total dendritic length and minimizing the tree distance between synapses and the site of input integration, typically the soma. This balance is illustrated in Figure 8 (Figure 7 in the original manuscript), where we demonstrate that the deviation from the theoretical minimum length arises because direct paths to synapses often require longer dendrites in our models.

Together with the new result, which we added as the new panels f, g and h to Figure 8 (originally Figure 7), we also adjusted panel a of Figure 8, to now illustrate the difference between random wiring, minimal wiring and minimal conductance delay. The updated Figure 8 and its new findings are discussed in the results section of the revised manuscript:

p.17 line 387, “This deviation is expected given that real dendrites need to balance their growth processes between minimizing wire while reducing conduction delays. The interplay between these two factors emerges from the need to reduce conduction delays, which requires a direct path length from a given synapse to the soma, consequently increasing the total length of the dendritic cable. (Cuntz et al., 2010, 2012; Ferreira Castro et al., 2020).

To investigate this further, we compared the scaling relations of the final morphologies of our models with other synthetic dendritic morphologies generated using a previously described minimum spanning tree (MST) based model. The MST model balances the minimization of total dendritic length and the minimization of conduction delays between synapses and the soma. This balance results in deviations from the theoretical minimum length because direct paths to synapses often require longer dendrites (Cuntz et al., 2008, 2010). The balance in the model is modulated by a balancing factor (𝑏𝑓 ). If 𝑏𝑓 is zero, dendritic trees minimize the cable only, and if 𝑏𝑓 is one, they will try to minimize the conduction delays as much as possible. It is important to note that the MST model does not simulate the developmental process of dendritic growth; it is a phenomenological model designed to generate static morphologies that resemble real cells.

To facilitate the comparison of total lengths between our simulated and MST morphologies, we generated MST models under the same initial conditions (synaptic spatial distribution) as our models and simulated them to match several morphometrics (total length, number of terminals, and surface area) of our grown morphologies. This allowed us to create a corresponding MST tree for each of our synthetic trees. Consequently, we could evaluate whether the branching structures of our models were accurately predicted by minimum spanning trees based on optimal wiring constraints. We found that the best match occurred with a trade-off parameter 𝑏𝑓 = 0.9250 (Figure 8f). Using the morphologies generated by the MST model with the specified trade-off parameter (𝑏𝑓 ), we showed that the square root of the synapse count and the total length (𝐿) in both our model generated trees and the MST trees exhibit a linear scaling relationship (Figure 8g; 𝑅2 = 0.65). The same linear relationship can be observed for the square root of the surface area and the total length 𝐿 of our model trees and the MST trees (Figure 8h; 𝑅2 = 0.73). Overall, these results indicate that our model generate trees are wellfitted by the MST model and follow wire optimization constraints.

We acknowledge that the value of the balancing factor 𝑏𝑓 in our model is higher than the range of balancing factors that is typically observed in the biological dendritic counterparts, which generally ranges between 0.2 and 0.4 (Cuntz et al., 2012; Ferreira Castro et al., 2020; Baltruschat et al., 2020). However, it is still remarkable that our model, which does not explicitly address these two conservation laws, achieves approximately optimal wiring. Why do we observe such a high 𝑏𝑓 value? We reason that two factors may contribute to this. First, in our models, local branches grow directly to the nearest potential synapse, potentially taking longer routes instead of optimally branching to minimize wiring length (Wen and Chklovskii, 2008). Second, the growth process in our models does not explicitly address the tortuosity of the branches, which can increase the total length of the branches used to connect synapses. In the future, it will be interesting to add constraints that take these factors into account. Taken together, combining activity-independent and -dependent dendrite growth produces morphologies that approximate optimal wiring.”

Further details on the fitted MST model and the corresponding analysis were added to the methods section:

p.26 line 669, “Comparison with wiring optimization MST models. To evaluate the wire minimization properties of our model morphologies (n=288), we examined whether the number of connected synapses (N), total length (L), and surface area of the spanning field (S) conformed to the scaling law 𝐿 ≈ 𝜋−1/2 ⋅ 𝑆1/2 ⋅ 𝑁1/2 (Cuntz et al., 2012). Furthermore, to validate that our model dendritic morphologies scale according to optimal wiring principles, we created simplified models of dendritic trees using the MST algorithm with a balancing factor (bf). This balancing factor adjusts between minimizing the total dendritic length and minimizing the tree distance between synapses and the soma (Cost = 𝐿 + 𝑏𝑓 ⋅ 𝑃 𝐿) (MST_tree; best bf = 0.925) (Cuntz et al., 2010); TREES Toolbox http://www.treestoolbox.org).

Initially, we generated MSTs to connect the same distributed synapses as our models. We performed MST simulations that vary the balancing factor between 𝑏𝑓 = 0 and 𝑏𝑓 = 1 in steps of 0.025 while calculating the morphometric agreement by computing the error (Euclidean distance) between the morphologies of our models and those generated by the MST models. The morphometrics used were total length, number of terminals, and surface area occupied by the synthetic morphologies.”

Point 1.9. It's not clear to me what the authors are trying to convey by repeatedly labeling this model as 'mechanistic'. The mechanisms implemented in the model are inspired by biological phenomena, but the implementations have little resemblance to the underlying biophysical mechanisms. Overall my impression is that this is a phenomenological model intended to show under what conditions particular patterns are possible. Line 363, describing another model as computational but not mechanistic, was especially unclear to me in this context.  

What we mean by mechanistic is that we implement equations that model specific mechanisms i.e. we have a set of equations that implement the activity-independent attraction to potential synapses (with parameters such as the density of synapses, their spatial influence, etc) and the activitydependent refinement of synapses (with parameters such as the ratio of BDNF and proBDNF to induce potentiation vs depression, the activity-dependent conversion of one factor to the other, etc). This is a bottom-up approach where we combine multiple elements together to get to neuronal growth and synaptic organization. This approach is in stark contrast to the so-called top-down or normative approaches where the method would involve defining an objective function (e.g. minimal dendritic length) which depends on a set of parameters and then applying a gradient descent or other mathematical optimization technique to get at the parameters that optimize the objective function. This latter approach we would not call mechanistic because it involves an abstract objective function (who could say what a neuron or a circuit should be trying to optimize?) and a mathematical technique for how to optimize the function (we don’t know if neurons can compute gradients of abstract objective functions). 

Hence our model is mechanistic, but it does operate at a particular level of abstraction/simplification. We don’t model individual ion channels, or biophysics of synaptic plasticity (opening and closing of NMDA channels, accumulation of proteins at synapses, protein synthesis). We do, however, provide a biophysical implementation of the plasticity mechanism through the BDNF/proBDNF model which is more than most models of plasticity achieve, because they typically model a phenomenological STDP or Hebbian rule that just uses activity patterns to potentiate or depress synaptic weights, disregarding how it could be implemented. To the best of our understanding, this is what is normally considered mechanistic in the field (in contrast to, for example, biophysical).

Reviewer #2 (Public Review): 

This work combines a model of two-dimensional dendritic growth with attraction and stabilisation by synaptic activity. The authors find that constraining growth models with competition for synaptic inputs produces artificial dendrites that match some key features of real neurons both over development and in terms of final structure. In particular, incorporating distance-dependent competition between synapses of the same dendrite naturally produces distinct phases of dendritic growth (overshoot, pruning, and stabilisation) that are observed biologically and leads to local synaptic organisation with functional relevance. The approach is elegant and well-explained, but makes some significant modelling assumptions that might impact the biological relevance of the results. 

Strengths: 

The main strength of the work is the general concept of combining morphological models of growth with synaptic plasticity and stabilisation. This is an interesting way to bridge two distinct areas of neuroscience in a manner that leads to findings that could be significant for both. The modelling of both dendritic growth and distance-dependent synaptic competition is carefully done, constrained by reasonable biological mechanisms, and well-described in the text. The paper also links its findings, for example in terms of phases of dendritic growth or final morphological structure, to known data well. 

Weaknesses: 

The major weaknesses of the paper are the simplifying modelling assumptions that are likely to have an impact on the results. These assumptions are not discussed in enough detail in the current version of the paper. 

(1) Axonal dynamics. 

A major, and lightly acknowledged, assumption of this paper is that potential synapses, which must come from axons, are fixed in space. This is not realistic for many neural systems, as multiple undifferentiated neurites typically grow from the soma before an axon is specified (Polleux & Snider, 2010). Further, axons are also dynamic structures in early development and, at least in some systems, undergo activity-dependent morphological changes too (O'Leary, 1987; Hall 2000). This paper does not consider the implications of joint pre- and post-synaptic growth and stabilisation.  

We thank the reviewer for the summary of the strengths and weaknesses of the work. While we feel that including a full model of axonal dynamics is beyond the scope of the current manuscript, some aspects of axonal dynamics can be included and are now implemented and tested in the revised manuscript. Since this feedback covers similar aspects of the model that were also pointed out by reviewer #1, we refer here to our detailed reply to their comments 1.1 and 1.2, where we list and discuss all the analyses performed to address the raised issues.

(2) Activity correlations 

On a related note, the synapses in the manuscript display correlated activity, but there is no relationship between the distance between synapses and their correlation. In reality, nearby synapses are far more likely to share the same axon and so display correlated activity. If the input activity is spatially correlated and synaptic plasticity displays distance-dependent competition in the dendrites, there is likely to be a non-trivial interaction between these two features with a major impact on the organisation of synaptic contacts onto each neuron.  

We have explored the amount of correlation (between and within correlated groups) in the revised manuscript (see also our reply to reviewer comment 1.1).

However, previous experimental work, (e.g. Kleindienst et al., 2011) has provided anatomical and functional analyses that it is unlikely that the functional synaptic clustering on dendritic branches is the result of individual axons making more than one synapse (see pg. 1019).

(3) BDNF dynamics 

The models are quite sensitive to the ratio of BDNF to proBDNF (eg Figure 5c). This ratio is also activity-dependent as synaptic activation converts proBDNF into BDNF. The models assume a fixed ratio that is not affected by synaptic activity. There should at least be more justification for this assumption, as there is likely to be a positive feedback relationship between levels of BDNF and synaptic activation.  

The reviewer is correct. We used the BDNF-proBDNF model for synaptic plasticity based on our previous work (Kirchner and Gjorgjieva, 2021).  

There, we explored only the emergence of functionally clustered synapses on static dendrites which do not grow. In the Methods section (Parameters and data fitting) we justify the choice of the ratio of BDNF to proBDNF from published experimental work. We also performed sensitivity analysis (Supplementary Fig. 1) and perturbation simulations (Supplementary Fig. 3), which showed that the ratio is crucial in regulating the overall amount of potentiation and depression of synaptic efficacy, and therefore has a strong impact on the emergence and maintenance of synaptic organization. Since we already performed all this analysis, we expect that the same results will also apply to the current model which includes dendritic growth, as it involves the same activity-dependent mechanism.

A further weakness is in the discussion of how the final morphologies conform to principles of optimal wiring, which is quite imprecise. 'Optimal wiring' in the sense of dendrites and axons (Cajal, 1895; Chklovskii, 2004; Cuntz et al, 2007, Budd et al, 2010) is not usually synonymous with 'shortest wiring' as implied here. Instead, there is assumed to be a balance between minimising total dendritic length and minimising the tree distance (ie Figure 4c here) between synapses and the site of input integration, typically the soma. The level of this balance gives the deviation from the theoretical minimum length as direct paths to synapses typically require longer dendrites. In the model this is generated by the guidance of dendritic growth directly towards the synaptic targets. The interpretation of the deviation in this results section discussing optimal wiring, with hampered diffusion of signalling molecules, does not seem to be correct. 

We agree with this comment. We had wrongly used the term “optimal wiring” as neurons can optimize their wiring not only by minimizing their dendritic length but other factors as noted by the reviewer. In the revised manuscript we replaced the term “optimal wiring” with “minimal wiring” wherever it was incorrectly used. On top of that, we performed further analysis and discussed these differences, as pointed out in the reply to reviewer #1 point 1.8.

To summarize, we want to again thank the reviewer for their in-depth review and all the suggestions that helped us improve the analysis and implementation of our model.

Reviewer #3 (Public Review): 

The authors propose a mechanistic model of how the interplay between activity-independent growth and an activity-dependent synaptic strengthening/weaken model influences the dendrite shape, complexity and distribution of synapses. The authors focus on a model for stellate cells, which have multiple dendrites emerging from a soma. The activity independent component is provided by a random pool of presynaptic sites that represent potential synapses and that release a diffusible signal that promotes dendritic growth. Then a spontaneous activity pattern with some correlation structure is imposed at those presynaptic sites. The strength of these synapses follow a learning rule previously proposed by the lab: synapses strengthen when there is correlated firing across multiple sites, and synapses weaken if there is uncorrelated firing with the relative strength of these processes controlled by available levels of BDNF/proBDNF. Once a synapse is weakened below a threshold, the dendrite branch at that site retracts and loses its sensitivity to the growth signal 

The authors run the simulation and map out how dendrites and synapses evolve and stabilize. They show that dendritic trees growing rapidly and then stabilize by balancing growth and retraction (Figure 2). They also that there is an initial bout of synaptogenesis followed by loss of synapses, reflecting the longer amount of time it takes to weaken a synapse (Figure 3). They analyze how this evolution of dendrites and synapses depends on the correlated firing of synapses (i.e. defined as being in the same "activity group"). They show that in the stabilized phase, synapses that remain connected to a given dendritic branch are likely to be from same activity group (Figure 4). The authors systemically alter the learning rule by changing the available concentration of BDNF, which alters the relative amount of synaptic strengthening, which in turn affects stabilization, density of synapses and interestingly how selective for an activity group one dendrite is (Figure 5). In addition the authors look at how altering the activity-independent factors influences outgrowth (Figure 6). Finally, one of the interesting outcomes is that the resulting dendritic trees represent "optimal wiring" solutions in the sense that dendrites use the shortest distance given the distribution of synapses. They compare this distribute to one published data to see how the model compared to what has been observed experimentally.  

There are many strengths to this study. The consequence of adding the activity-dependent contribution to models of synapto- and dendritogenesis is novel. There is some exploration of parameters space with the motivation of keeping the parameters as well as the generated outcomes close to anatomical data of real dendrites. The paper is also scholarly in its comparison of this approach to previous generative models. This work represented an important advance to our understanding of how learning rules can contribute to dendrite morphogenesis.

We thank the reviewer for the positive evaluation of the work and the suggestions below.

To improve the clarity of the manuscript, we adjusted and fixed some figures and corresponding paragraphs as follows:

(1) We increased the number of ticks and their corresponding numbers in all the figures to make them easier to read and interpret.

(2) In Figure 3 panel d, showing the evolution of synaptic weight, we corrected the upper limit at the yaxis to 1 (from previously 2).

(3) Due to a typo in the implementation of the BDNF concentration, we had to correct the used BDNF concentrations from 49%, 45% and 40%, to 49%, 46.5% and 43% respectively.

(4) The y-axis labels of Figure 6 (old Figure 5) panel e and f were changed to make the plots clearer (e: “morphology change explained (%)” to "effect on morphology (%)", and f: “synapse connection explained (%)” to "effect on connected synapses (%)").

(5) The values for the eta and tau-w in the supplementary Table were corrected. Previously tau-w was falsely 6000 time steps which was corrected to 3000 time steps, and eta was 45% and is now 46.5%.

We believe that all the changes to the manuscript will address the reviewer’s concerns and enhance the clarity and accuracy of the findings described in the manuscript.

Author response:

We thank the reviewers for their thoughtful comments. We are working to revise our manuscript and address each of the reviewers comments. A summary of our planned revisions and responses to some of the reviewers’ major concerns are included below.

Cultivation Density: Reviewers #1 and #2 suggested that additional studies testing the effects of varying bacterial density during animal development (cultivation) would strengthen our findings. While we agree with the reviewers that this is a very interesting experiment, it is not feasible. Indeed, we attempted this experiment but found it nontrivial to maintain stable bacterial density conditions over long timescales as this requires matching the rate of bacterial growth with the rate of bacterial consumption. Despite our best efforts, we have not been able to identify conditions that satisfy these requirements. We will focus our revised manuscript to include only assertions about the effects of recent experiences.

Transfer Method: Reviewers #1 and #2 expressed concern that the stress of transferring animals to a new plate may have resulted in an increased arousal state and thus a greater probability of rejecting patches. We thank the reviewers for this thoughtful remark and plan to conduct additional analyses to address this hypothesis. We did, however, anticipate this possibility and, to mitigate the stress of moving, we used an agar plug method where animals were transferred using the flat surface of small cylinders of agar. Importantly, the use of agar as a medium to transfer animals provides minimal disruption to their environment as all physical properties (e.g. temperature, humidity, surface tension) are maintained. Qualitatively, we observe no marked change in behavior from before to after transfer with the agar plug method, especially as compared to the often drastic changes observed when using a metal or eyelash pick.

Time Parameter: Related to the transfer method, Reviewer #1 expressed concern that the simplest time parameter (time since start of the assay) might better predict animal behavior. We thank the reviewer for pointing out the need to specifically test whether the time-dependent change in explore-exploit decision-making corresponds better with satiety (time off patch) or arousal (time since transfer/start of assay) state. We will conduct additional analyses to address these alternative hypotheses.

Parameter Initialization: Reviewer #1 pointed out an oversight in our methods section regarding the model parameter values used for the first encounter. We plan to clarify the initialization of parameters in the manuscript. In short, for the first patch encounter where k = 1:

● ρk is the relative density of the first patch.

● τs is the duration of time spent off food since the beginning of the recorded experiment. For the first patch, this is equivalent to the total time elapsed.

● ρh is the approximated relative density of the bacterial patch on the acclimation plates (see Assay preparation and recording in Methods). Acclimation plates contained one large 200 µL patch seeded with OD600 = 1 and grown for a total of ~48 hours. As with all patches, the relative density was estimated from experiments using fluorescent bacteria OP50-GFP as described in Bacterial patch density estimation in Methods.

● ρe is equivalent to ρh.

Sensing vs. non-sensing: Reviewer #3 suggested that the term “non-sensing” may not be ethologically accurate. We thank the reviewer for their comment and agree that we do not know for certain whether the animals sensed these patches or were merely non-responsive to them. We are, however, confident that these encounters lack evidence of sensing. Specifically, we note that our analyses used to classify events as sensing or non-sensing examined whether an animal’s slow-down upon patch entry could be distinguished from either that of events where animals exploited or that of encounters with patches lacking bacteria. We found that  “non-sensing” encounters are indeed indistinguishable from encounters with bacteria-free patches where there are no bacteria to be sensed (see Figure 2 - Supplement 7C-D and Patch encounter classification as sensing or non-sensing in Methods). Regardless, we agree with the reviewer that all that can be asserted for certain about these events is that animals do not respond to the bacterial patch in any way that we measured. Therefore, we will replace the term “non-sensing” with “non-responding” to better indicate the ethological interpretation of these events.

Time-dependent changes in sensing vs. non-sensing: Reviewer #1 remarked that the sensation of dilute patches increases with time. We agree with the reviewer that we observe increased responsiveness to dilute patches with time. Although this is interesting, our primary focus was on what decision an animal made given that they clearly sensed the presence of the bacterial patch. Nonetheless, we will add this observation to the discussion as an area of future work to investigate the sensory mechanisms behind this effect.

Classification of sensing vs. non-sensing: Reviewers #2 and #3 expressed concerns about the validity of the two clusters identified using the semi-supervised QDA approach described. We are grateful to the reviewers for pointing out the difficulty in visualizing the clusters and the need for additional clarity in explaining the supervised labeling. We will use additional visualizations and methods to validate the clusters we have discovered. Specifically, we aim to provide additional evidence that the sensing vs. nonsensing data is bi-modal (i.e. a two-cluster classification method fits best). Further, it seems that there may be some confusion as to how we arrived at 3 encounter types (i.e. search, sample, exploit) that we plan to clarify in the manuscript. Specifically, it’s important to note that two methods were used on two different (albeit related) sets of parameters. We first used a two-cluster GMM to classify encounters as explore or exploit. We then used a two-cluster semi-supervised QDA to classify encounters as sensing or non-sensing (to be changed to “non-responding”, see above response) using a different set of parameters. We thus separated the explore cluster into two (sensing and non-sensing exploratory events) resulting in three total encounter types: exploit, sample (explore/sensing), and search (explore/non-sensing). We will clarify this in the text. Additionally, we will clarify the labelling used for “supervising” QDA. Specifically, we made two simple assumptions: 1) animals must have sensed the patch if they exploited it and 2) animals must not have sensed the patch if there were no bacteria to sense. Thus, we labeled encounters as sensing if they were found to be exploitatory as we assume that sensation is prerequisite to exploitation; and we labeled encounters as non-sensing for events where animals encountered patches lacking bacteria (OD600 = 0). All other points were non-labeled prior to learning the model. In this way, our labels were based on the experimental design and results of the GMM, an unsupervised method; rather than any expectations we had about what sensing should look like. The semi-supervised QDA method then used these initial labels to iteratively fit a paraboloid that best separated these clusters, by minimizing the posterior variance of classification.

Accept-reject vs. stay-switch: Reviewers #1 and #2 ask for additional discussion on how the accept-reject decision-making framework differs from the stay-switch framework. We thank the reviewers for alerting us to this gap in our discussion. We intend to clarify that these frameworks ask two different types of questions (i.e. “Do you want to eat it?” versus “If so, how long do you want to eat it for?”). These concepts are well described in canonical foraging theory literature (see Pyke, Pulliam & Charnov 1977 for a review on the subject) and are easily distinguishable for animals that forage using the following framework: 1) search for prey, 2) encounter prey from a distance, 3) identify prey type, 4) decide to pursue (accept-reject decision), 5) pursue and capture the prey, 6) exploit prey, and 7) decide to stop exploiting and start searching again (stay-switch decision). In this case, it is easy to see the distinction between accept-reject and stay-switch decisions. However, in some scenarios, animals must physically encounter prey prior to identification and then must make an accept-reject decision. In these cases where pursuit and capture are not visualized, it is harder to distinguish between accept-reject and stay-switch decisions. In our experiments, we find significant bimodality in encounter duration (see Figure 2H) where short duration (exploratory) encounters appear to represent a lower bound where animals spend the minimum amount of time possible on a patch (less than 2 minutes), which we interpret as a rejection of the patch. On the other hand, exploitatory encounters span a large range of durations from 2 to 60+ minutes which we interpret as an initial acceptance of the patch followed by a series of stay-switch decisions which determine the overall duration of the encounter. While one could certainly model our data using only stay-switch decision-making, we ascertain that an encounter of minimal duration is better interpreted ethologically as a rejection than as an immediate switch decision. We will revise the text to further extrapolate upon our point of view on this somewhat philosophical distinction and what it predicts about C. elegans behavior.

Sensory mutant behavior: Reviewers #1 and #3 ask for further speculation on the observed behavior of osm-6 and mec-4 animals. We will further elaborate on our findings, how they relate to previous studies, and what they suggest about the mechanisms behind these foraging decisions.

Model design: Reviewer #3 suggested several alterations to the behavioral model. While the proposed model seems entirely reasonable and could aid in elucidating the time component of how prior experience affects decision-making, we chose the present model based on our experience with model selection using these data. Indeed, as the reviewer suggested, we did a great number of analyses involving model selection including model selection criteria (AIC, BIC) and optimization with regularization techniques (LASSO and elastic nets). We found that the problem of model selection was compounded by the enormous array of highly correlated variables we had to choose from. Additionally, we found that both interaction terms and non-linear terms of our task variables could be predictive of accept-reject decisions but that the precise set of terms selected depended sensitively on which model selection technique was used and generally made rather small contributions to prediction. The diverse array of results and combinatorial number of predictors to possibly include failed to add anything of interpretable value. We therefore chose to take a different approach to this problem. Rather than trying to determine what the “best” model was we instead asked whether a minimal model could be used to answer a set of core questions. Indeed, our goal was not maximal predictive performance but rather to distinguish between the effects of different influences enough to determine if encounter history had a significant, independent effect on decision making. We thus chose to only include task variables that spanned the most basic components of behavioral mechanisms to ask very specific questions. For example, we selected a time variable that we thought best encapsulated satiety. While we could have included many additional terms, or made different choices about which terms to include, based on our analyses these choices would not have qualitatively changed our results. Further, we sought to validate the parameters we chose with additional studies (i.e. food-deprived and sensory mutant animals). We regard our study as an initial foray into demonstrating accept-reject decision-making in nematodes. The exact mechanisms and, consequently, the best model design is therefore beyond the scope of this study. Lastly, Reviewer #3 criticized the use of only sensed patches in the model. While we acknowledge that we are not certain as to whether the “non-sensing” encounters are truly not sensed, we find qualitatively similar results when including all exploratory patches in our analyses. In fact, when all encounters are used, we find stronger correlations between our task variables and the accept-reject decision. However, we take the position that sensation is necessary for decision-making and thus believe that while our model’s predictive performance may be better using all encounters, the interpretation of our findings is stronger when we only include sensing events.

Author response:

First of all, I'd like to express my heartfelt thanks to you for your meticulous and professional review comments. Your feedback is very important to our work. It not only helps us identify the shortcomings in the paper, but also provides valuable guidance for improving the quality of the paper.

We carefully read every suggestion you made and were deeply inspired. Please rest assured that we will carefully consider and revise each opinion to ensure that our research work is more rigorous and clear. We promise to revise the manuscript accordingly to meet the standards of the journal and enhance the credibility and influence of the research.

The main modifications include the experiment of A Mid1 supplementation experiment in Mid1 knockout micesupplementing Mid1 in Mid1 knockout mice; Detection of kinases such as CaMKII, PKA and ERK1/2; Supplementary references; Supplement the behavioral experiment of new object recognition; Electrophysiological measurement experiment of supplementing LTP; Supplementary neuron-specific immunohistochemical staining experiment; Supplementing the information of knockout mice used in the study; Modify the language expression of the article and the problem of too few pictures.

Thank you again for your valuable time and professional advice. We look forward to submitting the revised manuscript to you for further review.

Author response:

Reviewer #1 (Public review):

Summary:

Cesar, Santos & Cogni use a meta-analysis to report on the direction and magnitude of three fundamental fitness components in defensive symbioses. Specifically, the work focuses on interactions between three arthropod host families (Aphididae, Culicidae, Drosophilidae, and others) and common bacterial endosymbionts (Wolbachia, Serratia, Hamiltonella, Spiroplasma, Rickettsia, Regiella X-type and Arsenophonus). The results of the overall analysis confirm common assumptions and previous work on such fitness components, showing that defensive symbionts provide strong protection to hosts and cause detectable costs to both hosts and the enemy. The analysis provides insight into the extent of the cost/benefit tradeoff for hosts, reporting that the cost is six times lower than the protective effect. The confirmation that natural enemies attacking hosts infected with symbionts have a reduction in their fitness is also an interesting one, as this shows that the majority of defensive symbionts provide protection by resisting enemy infection, as opposed to tolerating it. This finding has important consequences for evolutionary counter-responses in the enemy species. Of course, this result has less relevance for certain types of enemies (such as parasitoids) where successful infection is dependent upon host killing.

Interesting results also emerge from the subgroup analysis. For the full dataset, both natural and introduced symbionts were similarly effective in positively influencing the fitness of hosts. However, in the Wolbachia-specific analysis, the artificially introduced symbionts caused costs to the hosts where the natural strain did not. These findings have potentially important ramifications for schemes that use endosymbionts for biocontrol or vector competence, suggesting that (in some cases) natural strains may be the more stable choice for deploying (as they are associated with lower costs).

The analysis draws from an impressively large dataset, but the interpretation of the full impact of the results would be helped by greater detail on the species/strain level systems included, the data extraction approach, and inclusion criteria. Accounting for phylogenetic nonindependence and alternative coding of one of the moderator variables could also strengthen the biological relevance of the models. Suggestions and thoughts are outlined below.

We sincerely thank Reviewer #1 for the time and effort dedicated to reviewing our manuscript. The suggestions provided are highly constructive and will greatly assist us in improving both our analyses and the manuscript overall.

Strengths & Potential Improvements:

An impressively large number of effect sizes (3000) from only 226 studies is collected, robustly confirming common assumptions on the magnitude of fundamental fitness components. However the paper would benefit from a clear breakdown in the main text of the specificities of each system included (e.g. a table at the host species/symbiont strain level, where it is possible). Currently, there is not enough detail for those who want a deep dive to understand what data was extracted for the analysis from these 226 studies, or those who want to understand the underlying diversity in the dataset.

We thank the reviewer for the suggestion, and we will add this information to our revised manuscript.

Currently, when the 'natural enemy group' is tested as a moderator it is coded broadly by type of organism (e.g. virus, bacterium, fungi, parasitoid). But this doesn't adequately capture the mode of killing/fitness reduction by the enemy, which would be the much more biologically relevant categorisation for your questions. For example, parasitoid infection is dependent upon host death (thus host fecundity is not relevant, because the host either survived or did not). Among bacterial and viral pathogens antagonists there is scope for both fecundity and survival to be affected. This in turn may be a very influential factor for the outcome. You could consider recoding this enemy moderator.

We agree, and we will implement this in the analysis to our revised manuscript.

The analysis is restricted to arthropod hosts and defensive symbionts that are also classed as endosymbionts. This focus should be made clear early on in the paper, as there are many systems (that are classed by many as defensive symbioses) that are not part of the analysis.

We agree, and we will implement this to our revised manuscript.

There is fairly minimalistic testing of moderators/sub-groups (which probably has its statistical strengths) but perhaps there are also some missed opportunities for testing other ecological contributors to variance, including coinfection (although perhaps limited by power) and other approaches to coding enemy group (as detail above).

We agree, and we will implement this in the analysis to our revised manuscript.

Looking at the overview of systems included, there's likely a high degree of phylogenetic non-independence in the dataset. Where it is possible, using phylogenetically controlled models could strengthen this analysis.

We thank the reviewer for the suggestion. We will explore the possibility of using phylogenetically controlled models in our analyses, although we recognize the challenges associated with their implementation, particularly in the case of the natural enemies, given the great diversity of distant related groups included in our study - viruses, bacteria, fungi, protozoans, nematodes and parasitoids wasps.

Looking at your included systems (Table S5), you might be able to test the effect of coinfection on the 3 variables of interest. For example, it would be particularly important to see if the effects of two symbionts are additive or not.

We agree, and we will implement this in the analysis to our revised manuscript.

No code for the analysis is provided for review at this stage and full details of the dataset are also not available. This slightly limits the ability to assess the full scope and robustness of the study. It would be helpful to have an extensive table in the supplementary detailing (minimum) the reference, study, experiment, host species, symbiont strain, and a description of the exact data extraction source (e.g.table/figure/in text), and method of extraction.

The code for the analysis and the full raw data with the suggested information are available at https://github.com/cassiasqr/MetaSymbiont (The link is available at the end of the manuscript).

Reviewer #2 (Public review):

Summary:

In this exciting study, Cesar and co-authors perform a meta-analysis on the influence of arthropod symbionts on the fitness of their hosts when they are exposed or not to natural enemies. These so-called defensive symbionts are increasingly recognized as key elements in arthropod survival against natural enemies, with effects that ripple through entire terrestrial ecosystems. The topic is timely, the approach is sound, and the manuscript is well-written. I believe this manuscript will attract the attention of entomologists and of microbiologists interested in symbiosis. This study builds on a previous meta-analysis that I was involved in, which was based on phloem-feeding insects. This novel data set is much larger and includes flies (including the model system Drosophila) and mosquitoes (a group of high medical interest). While the previous metaanalysis considered only parasitoids as natural enemies, this study also includes fungi, bacteria, and viruses.

Strengths:

The authors compile a very large dataset and provide a broad quantitative overview of the effects of defensive symbionts in insects. By measuring symbiont effects in the presence and absence of natural enemies, the authors are able to infer whether a trade-off between defense and the costs of mutualism in the absence of enemy pressure exists. Defensive symbioses are an important research topic that had its initial "momentum" a decade ago, so the timing for such a systematic review is very appropriate.

We sincerely thank Reviewer #2 for dedicating their time and effort to reviewing our manuscript. The suggestions are very insightful and will significantly contribute to improving our manuscript.

Weaknesses:

I think the manuscript could be improved by clarifying several sections, particularly the introduction and methods. The introduction section is too specific and heavily reliant on particular examples. In my view, the theoretical background of the study could be made clearer, and the knowledge gap identified more explicitly. A focus on how widespread defensive symbioses are, along with a brief, up-to-date review of the groups possessing such symbionts, would help. This lack of focus is also observed in the methods section, where more details are needed in many instances to better understand how data was collected and analyzed. Regarding the analyses, the multi-level analysis contains many moderators, but it's unclear why these moderators were included. While this may seem a minor issue, it highlights a disconnection between the analyses, the conceptual background, and the hypotheses tested. 

We thank the reviewer for the suggestions, and we will try to make the introduction and the methods section clearer. 

Another important weakness is that the analyses are too general, and much-hidden information is not immediately apparent. For instance, readers cannot easily identify which species of symbionts are studied (and the effects they have), or which natural enemies are involved. Although this information is found in the supplementary material, including it in the main body would significantly improve the manuscript.

We agree, and we will implement this to our   revised manuscript.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

(1) The technology requires a halo-tagged derivation of the active compound, and the linked position will have a huge impact on the potential "target hits" of the molecules. Given the fact that most of the active molecules lack of structure-activity relationship information, it is very challenging to identify the optimal position of the halo tag linkage.

We appreciate your insightful comment. While finding the optimal position to attach a chemical linker to a small molecule of interest is indeed a challenging but necessary step, this is a common difficulty across all target-ID methods, except for those that are modification-free, as we described in Discussion. However, modification-free approaches such as DARTS, CETSA, and TPP have their own limitations, such as low sensitivity and a high false-positive rate. Additionally, DARTS and SPROX are limited to use with cell lysates. Please refer to the introduction in our manuscript for more details on these approaches. On the other hand, synthesizing HTL derivatives is relatively straightforward compared to other modifications, and we provide helpful guidelines for chemical linker design, provided the optimal chemical moiety has been identified, which is crucial for target identification. We selected dasatinib and HCQ/CQ as model compounds because previous studies offered insights into their derivative synthesis. Our data also show that DH5 retains strong kinase inhibitory activity (Figure 4—figure supplement 2), and DC661-H1 demonstrates potent inhibition of autophagy (Figure 6—figure supplement 1). For novel compounds, conducting a thorough structure-activity relationship (SAR) study is essential to determine the optimal position for HTL derivative synthesis.

(2) Although POST-IT works in zebrafish embryos, there is still a long way to go for the broad application of the technology in other animal models.

Thank you for your constructive comment. Yes, there is still a long way to go in developing the POST-IT system for broader applications in other animal models, especially in mice. However, we hope that our study provides valuable insights and inspiration to scientists and experts for applying the POST-IT system in various models. We are also committed to further improving its applicability.

(3) The authors identified SEPHS2 as a new potential target of dasatinib and further validated the direct binding of dasatinib with this protein. However, considering the super strong activity of dasatinib against c-Src (sub nanomolar IC50 value), it is hard to conclude the contribution of SEPHS2 binding (micromolar potency) to its antitumor activity.

Thank you for your insightful comment. We agree that the anticancer activity of dasatinib primarily results from inhibiting tyrosine kinases such as SRC and ABL. However, SEPHS2 contains an “opal" termination codon, UGA, at the 60th amino acid residue, which codes for selenocysteine. Due to the technical challenge of expressing selenoproteins in E. coli, we mutated it to cysteine for expression in E. coli to avoid premature translation termination, as described in the Materials and Methods section. Although the purified recombinant SEPHS2 shows a Kd of about 10 µM for dasatinib, the binding affinity to endogenous SEPHS2 may be higher since selenocysteine is larger and more electronegative than cysteine. This presents an interesting area for future investigation. Furthermore, our study of dasatinib’s binding to SEPHS2 could help facilitate the development of new SEPHS2 inhibitors, potentially targeting the active site of SEPHS2.

Reviewer #3 (Public review):

(1) Target Specificity: It is crucial for the authors to differentiate between the primary targets of the POST-IT system and those identified as side effects. This distinction is essential for assessing the specificity and utility of the technology.

Thank you for your insightful comment. Drugs inevitably bind to various proteins with differing affinities, which can contribute to both side effects and beneficial outcomes. Typically, the primary targets exhibit high affinities. In this manuscript, we ranked the identified protein targets of DH5 based on affinity from mass spectrometry and p-values (Fig. 5A), and for DC661-H1, we used the SILAC ratio (Fig. 6A). We also individually assessed many drug-protein binding affinities using the MST assay, as well as in vitro and in cellulo assays, demonstrating their specificity. Moreover, we believe it is essential to identify as many protein targets as possible at physiological drug concentrations to better understand the drug’s side effects. Of course, further investigation is required to assess the roles and effects of these target proteins.

(2) In Vivo Target Identification: The manuscript lacks detailed clarity on which specific targets were successfully identified in the in vivo experiments. Expanding on this information would provide a clearer view of the system's effectiveness and scope in complex biological settings.

Thank you for your insightful comment regarding in vivo target identification. In this manuscript, we utilized a cell line as the primary method for in vivo target identification and validation after optimizing our system in test tubes. We successfully validated many of the targets identified using our POST-IT system (Figure 6—figure supplement 3). To demonstrate the proof of principle for in vivo application, we employed zebrafish embryos as an in vivo model, showing that endogenous SRC can be effectively pulled down by DH5 treatment (Fig. 7). While we could have explored the entire proteome to identify endogenous target proteins in zebrafish that bind to DH5 or dasatinib, we felt this would extend beyond our original scope, given that we have already demonstrated POST-IT’s ability to identify target proteins for dasatinib. Specific target identification and validation are crucial when using zebrafish for drug discovery. Additionally, we acknowledge that drugs likely interact with a range of protein targets in living organisms and may undergo metabolism and interactions within the circulatory system, which we address in our discussion.

(3) Reproducibility and Scalability: Discussion on the reproducibility of the POST-IT system across various experimental setups and biological models, as well as its scalability for larger-scale drug discovery programs, would be beneficial.

Thank you for the suggestion. While our system has shown  high reproducibility in our experiments, further improving both reproducibility and scalability would be advantageous. One potential approach to address this is through the generation of stable-expressing cell lines and transgenic zebrafish lines, which we have discussed in the revised manuscript. Establishing stable cell lines with robust POST-IT expression could enhance scalability for drug discovery applications.

(4) Quantitative Analysis: A more detailed quantitative analysis of the protein interactions identified by POST-IT, including statistical significance and comparative data against other technologies, would enhance the manuscript.

Thank you for your suggestion. In our assessment of drug-protein affinity, we included Kd values as quantitative measures using MST assays. The protein targets of dasatinib identified through mass spectrometry are also accompanied by p-values for quantitative analysis (Fig. 5A), and the detailed procedures are described in the Material and methods section. While it is challenging to provide direct comparative data against other technologies, our system successfully identified many known target proteins for dasatinib, as well as SEPHS2 and VPS37C as new targets for dasatinib and for HCQ/CQ, respectively, which were not detected by other methods.

(5) Technological Limitations: The authors should discuss any limitations or potential pitfalls of the POST-IT system, which would be crucial for future users and for guiding subsequent improvements.

Thank you for your insightful suggestion We agree that clearly defining the technological limitations is important. Therefore, we have expanded our original discussion on the limitations of our POST-IT system (Discussion section, paragraph 6).

(6) Long-Term Stability and Activity: Information on the long-term stability and activity of the POST-IT components in different biological environments would ensure the reliability of the system in prolonged experiments.

Yes, this is an important question. We did not notice any stability or toxicity issues with Halo-PafA and Pup substrates in HEK293T cells or zebrafish, which is an important factor for stable cell lines and transgenic zebrafish lines. However, HTL derivatives of the drug could be toxic or unstable due to the nature of the drug or its metabolism, which needs to be taken into account when designing experiments, and we have included this in the Discussion.

(7) Comparison with Existing Technologies: A detailed comparison with existing proximity tagging and target identification technologies would help position POST-IT within the current landscape, highlighting its unique advantages and potential drawbacks.

We appreciate your valuable feedback and agree that such comparisons are crucial. We have included a detailed overview and comparison of existing proximity-tagging systems and their related target identification technologies in the Introduction (lines 78-100) and Discussion (lines 391-412), highlighting their respective pros and cons. Additionally, we have expanded the discussion to further compare these technologies with our POST-IT system, addressing its advantages and limitations (lines 378-390, lines 448-467). We hope this provides sufficient context and information to effectively position POST-IT among the landscape of proximity-tagging target identification technologies.

(8) Concerns Regarding Overexposed Bands: Several figures in the manuscript, specifically Figure 3A, 3B, 3C, 3F, 3G, Figure 4D, and the second panels in Figure 7C as well as some figures in the supplementary file, exhibit overexposed bands.

We appreciate your astute observation regarding the overexposed bands and apologize for any confusion. The “overexposed” bands represent the unpupylated proteins, while the bands above them correspond to the pupylated proteins. We intended to clearly show both pupylated and unpupylated bands, although the latter are generally much weaker. We are currently working on further improving our POST-IT system to enhance pupylation efficiency.

(9) Innovation Concern: There is a previous paper describing a similar approach: Liu Q, Zheng J, Sun W, Huo Y, Zhang L, Hao P, Wang H, Zhuang M. A proximity-tagging system to identify membrane protein-protein interactions. Nat Methods. 2018 Sep;15(9):715-722. doi: 10.1038/s41592-018-0100-5. Epub 2018 Aug 13. PMID: 30104635. It is crucial to explicitly address the novel aspects of POST-IT in contrast to this earlier work.

Thank you for bringing this to our attention. Proximity-tagging systems like BioID, TurboID, NEDDylator, and PafA (Lui Q et al., Nat Methods 2018) were initially developed to study protein-protein interactions or identify protein interactomes, as these applications are of broader interest and generally easier to implement. However, applying proximity-tagging systems for small molecule target identification requires significant optimization. As described in the introduction (lines 78-100), target protein identification systems have since been developed using TurboID and NEDDylator (Tao AJ et al., Nat Commun 2023; Hill ZB et al., J Am Chem Soc 2016). It is conceivable that a PafA-based proximity-tagging system could also be adapted for target-ID, and other groups may pursue this approach in the future. Although the PafA-Pup system shows great promise for target-ID applications, extensive optimization was needed to enable its use for this purpose. Finally, we demonstrate that POST-IT offers distinct advantages over other proximity-tagging-based target-ID systems. For more details, please refer to the introduction and discussion sections.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Figure 1- Figure Supplement 1A: The Pup substrate "HB-Pup" is mentioned, but the main text or figure legend provides no introduction or description.

We appreciate your astute observation. We have added a description in the main text and figure legend as follows: “…and used HB-Pup as a control, which contains 6´His and BCCP at the N terminus of Pup” in the main text (line 142) and “HB, TS, and SBP refer to 6´His and BCCP, twin-STII (Strep-tag II), and streptavidin binding peptide, respectively.” in the Figure 1-figure supplement 1A.

(2) Figure 1 - Figure Supplement 3B: The authors used TS-sPupK61R as a substrate but did not explain why. The main text mentions that mutating sPup alone did not affect polypupylation, raising the question of why TS-sPupK61R was used in this figure. Furthermore, while the authors state that polypupylation becomes evident after 1 hour of incubation (more pronounced after 2 or 3 hours), the reactions here were conducted for only 30 minutes.

Thank you for your question. Figure 1 - Figure Supplement 3B was conducted to test self-pupylation levels in the different Halo-PafA derivatives. For this purpose, we could use any Pup substrate such as SBP-sPup and SBPK4R-sPupK61R, instead of Ts-sPup and TS-sPupK61R, as they do not show any differences in pupylation activity. We chose Ts-sPup and TS-sPupK61R simply because any Pup substrates could be used for this purpose. Similarly, we did not need to incubate the reaction for a longer time to detect polypupylation, as our intention was to test “self-pupylation”. We demonstrated in Figure 1 – figure supplement 2 that polypupylation is dependent on the number or position of lysine residues in Pup substrate or tags. The results clearly showed that self-pupylation was almost completely abolished by the Halo8KR mutation. To clarify this, we added the following description in lines 168-169: “Ts-sPup and TS-sPupK61R were chosen as sPup substrates for this experiment, although any Pup substrates could have been used. The levels of self-pupylation were assessed.”

(3) Line 156: The statement that "the TS-tag completely abolished polypupylation in TS-sPup" is inaccurate. Using TSK8R-sPupK61R as the substrate, several bands appear, which likely represent Halo-PafA with varying degrees of polypupylation. Some bands also appear to correspond to those seen when using TS-sPup as a substrate. The authors should clarify how they distinguish between multipupylation and polypupylation in this case.

We sincerely appreciate your insight into clarifying the distinction between multipupylation and polypupylation. Polypupylation refers to the addition of a new Pup onto a previously linked Pup on the target protein, akin to polyubiquitination. In contrast, multipupylation involves multiple single pupylations at different positions on the target proteins. Since pupylation occurs exclusively at lysine residues in tag-Pup substrates, mutating all lysine residues to arginine, as in TSK48R-sPupK61R, prevents the mutant tag-Pup from linking to another Pup. This means that only single pupylation can proceed with this type of mutant Pup substrate. If multiple pupylated bands are observed with this mutant substrate, it indicates “multipupylation” rather than “polypupylation”, as shown in Figure 1-figure supplement 2D. The same applies to the pupylation bands in Figure 1-figure supplement 2E and F, as sSBP-sPupK61R and SBPK4R-sPupK61R lack lysine residues. By comparing these multipupylation bands, it is also possible to distinguish them from polypupylation bands, which are marked by yellow arrows. However, after 2-3 pupylation bands, higher-order bands become increasingly difficult to distinguish.

To clarify the mutation in the TS-tag, we revised the sentence in line 156 from “However, further mutations within the TS-tag completely abolished polypupylation in TS-sPup” to “However, further mutations of two lysine residues within the TS-tag, creating TSK8R-sPupK61R, completely abolished polypupylation in TS-sPup”. Additionally, we have inserted sentences in line 152 to define polypupylation and multipupylation, as described here.

(4) Line 160: Similar to the above concern about line 156, the claim that SBPK4R and sSBP completely prevented polypupylation is unconvincing and requires more supporting evidence.

Thank you for raising this concern. As mentioned above, both SBPK4R and sSBP lack lysine residues required for pupylation. As a result, these mutants can only undergo multiple single pupylations on the lysine residues of the target protein, which leads to “multipupylation”. In Figure 1-figure supplement 2E and F, pupylation bands by sSBP-sPupK61R or SBPK4R-sPupK61R do not display doublet bands (one from multipupylation and the other from polypupylation), as seen with SBP-sPup, marked by yellow arrows. Notably, Halo-PafA containing polypupylated branches migrates more slowly than one with an equal number of multipupylation events. To clarify this point, we have added the phrase “as shown in sSBP-sPupK61R and SBP4KR-sPupK61R” at the end of the sentence in line 160.

(5) Lines 176-177: The authors claim that PafAS126A exhibited reduced polypupylation compared to PafA, but given that PafAS126A may reduce depupylase activity, how could it reduce polypupylation levels? Moreover, it is hard to find any data supporting this conclusion in Figure 1 - Figure Supplement 3B.

We appreciate your insightful comment. At this point, we do not fully understand how the mutation that reduces depupylase activity also decreases polypupylation. It is possible that PafAS126A has a lower preference for pupylated Pup as a prey, which is required for polypupylation, since depupylase activity depends on recognizing pupylated Pup as a prey to remove it. Nonetheless, Halo-PafAS126A shows reduced levels of higher molecular weight bands compared to Halo-PafA, as shown in Figure 1-figure supplement 3B, while exhibiting increased pupylation in lower molecular weight bands, which represent either multipupylation or low-degree polypupylation. Since higher molecular weight bands (> 150 kD) are likely due to polypupylation, this result suggests reduced polypupylation and increased multipupylation in Halo-PafAS126A. To clarify this in the main text, we have added the following description in line 177: “as evidenced by the decreased levels of high molecular weight bands and an increase in low molecular weight bands”

(6) POST-IT system in cellulo validation: The system was developed using the Halo-tag, yet the in-cell validation uses FRB and FKBP instead, without explaining this switch. This inconsistency makes the logic of the experiment unclear.

We appreciate your insightful comment. The interaction between rapamycin and FRB or FKBP is known to be highly specific and robust, making this system useful in various biological contexts. Due to this property, rapamycin can induce interaction between two proteins when one is fused with FRB and the other with FKBP. Before testing or optimizing the POST-IT system in cells, we hypothesized that using the rapamycin-induced interaction between FRB and FKBP could introduce pupylation of the target protein, provided that PafA is fused with FRB or FKBP and the target protein is fused with the other. The results demonstrate that PafA can introduce pupylation of the target protein in a proximity-dependent manner via this chemically induced interaction. To further clarify this in the main text, we modified the original sentence in lines 214-216 as follows: “To mimic drug-target interaction-induced pupylation in live cells and assess the potential of PafA as a proximity-tagging system for target-ID, we incorporated the rapamycin-induced interaction between FRB and FKBP into our PL system, as this interaction between a small molecule and a protein is known to be highly specific and robust (Figure 3—figure supplement 1A).”

(7) Line 209: The authors decided to use the SBP-tag for further studies due to better performance, but in Figure 3 - Figure supplement 1, they still used the unintroduced HB-Pup as the substrate, which is confusing and lacks explanation.

Thank you for raising your question. The SBP-tag is not superior to the TS-tag in terms of pupylation activity. However, the TSK8R mutant cannot bind to Strep-Tactin beads, while the SBP mutants, SBPK4R and sSBP, can bind to streptavidin. Therefore, we chose the SBP-tag instead of the TS-tag for further studies as a Pup substrate in POST-IT system, as we needed to pull down the target proteins. HB-Pup is consistently used as a control throughout various experiments, as it is the original Pup substrate. In Figure 3-figure supplement 1B and C, HB-Pup was used to test chemically induced pupylation by PafA. In these cases, it was not so critical which Pup substrate was chosen. Furthermore, we compared HB-Pup and different SBP-sPup substrates in Figure 3-figure supplement 1D, where HB-Pup was used as a control or for comparison. Although pupylation bands with HB-Pup appear more robust, this substrate contains multiple lysine residues, leading to high levels of polypupylation. To make it clear, we modified the sentence in line 209 to “Therefore, we decided to use the SBP-tag as a Pup substrate in the POST-IT system for further studies.”.

(8) Line 220: Both SBP-sPup and SBPK4R-sPupK61R are described as exhibiting efficient pupylation, but the data show mostly self-pupylation and little to no pupylation of the target protein.

Thank you for your concern. However, pupylation of the target protein is actually quite substantial, as the intensities of the free form and pupylated proteins are relatively similar, as shown in the upper panel of Figure 3-figure supplement 1D. Self-pupylation is always much higher than target pupylation, because PafA constantly pupylates itself, whereas pupylation of the target protein occurs only through interaction. Furthermore, V5-FRB-mKate2-PafA contains many lysine residues, which increases the levels of self-pupylation.

(9) Lines 222-224: The authors chose SBPK4R-sPupK61R to avoid polypupylation, although SBP-sPup did not cause detectable polypupylation. Neither substrate caused pupylation of the target protein, so the rationale behind this choice is unclear.

Thank you for raising your question. Similar to the above comment (#8), please refer to the pupylation bands of the target protein, as shown in the upper panel of Figure 3-figure supplement 1D. The pupylation band of the target protein is quite remarkable, as the intensities of the free form and pupylated proteins are comparable. Additionally, there are no multiple pupylation bands in either case, except for one additional weak multipupylation band, indicating no polypupylation by SBP-sPup, which does not have K-to-R mutations. Of course, SBPK4R-sPupK61R can only undergo single pupylation, as it does not contain lysine residues. Although we did not observe polypupylation by SBP-sPup in this experimental condition, it is possible that SBP-sPup may cause polypupylation under different experimental conditions or with other target proteins. Since SBPK4R-sPupK61R exhibits comparable pupylation of the target protein at least in this experiment setting as SBP-sPup, we selected SBPK4R-sPupK61R as the Pup substrate for POST-IT system to avoid any potential polypupylation that could be caused by SBP-sPup in other cases. We believe that polypupylation can introduce bias into the analysis and hinder the comprehensive discovery of additional target proteins for small molecules.

(10) Line 224: The authors conclude that rapamycin greatly reduced self-pupylation, but the supporting data are unclear.

Thank you for your constructive comments on our manuscript. Please refer to the lower panel of Figure 3-figure supplement 1D. When using either SBPK4R-sPupK61R or SBP-sPup, rapamycin treatment results in reduced levels of self-pupylation compared to the no-treatment control. However, we did not observe this reduction with HB-Pup and do not know the reason. To clarify this in the main text, we added the following description to the end of the sentence: “when using either SBPK4R-sPupK61R or SBP-sPup, as shown in the lower panel of Figure 3—figure supplement 1D”

(11) Line 234: The authors selected an 18-amino acid linker, but given that linkers longer than 10 amino acids enhance labeling, this choice should be explained.

Thank you for raising your question. In fact, a linker of 10 amino acids (aa) or longer is likely to behave similarly. We chose an 18 aa linker instead of a 40 aa linker primarily for the convenience of cloning and to reduce the potential for DNA sequence recombination associated with longer repeats. Additionally, a longer, flexible linker may behave like an intrinsically disordered protein (Harmon et al., 2017), which can lead to unwanted protein-protein interactions or phase separation. To elaborate on this, we added the following sentences after the sentence in line 233-235: “We chose the 18-amino acid linker instead of the 40-amino acid linker for easier cloning and to lower the risk of DNA recombination from longer repeats. Additionally, a longer, flexible linker may behave like an intrinsically disordered protein (Harmon et al., 2017), an unwanted feature for target-ID.”

(12) S126A and K172R mutations: The authors claim that these mutations additively enhanced pupylation under cellular conditions, but in Figure 3B, the band intensities appear similar for the wild-type and mutant versions.

Thank you for raising your concern. Although a single pupylation band appears similar among the three different Halo-PafA proteins, multipupylation bands are slightly but noticeably increased by the S126A and K172R mutations compared to Halo8KR-PafA. Since we used SBPK4R-sPupK61R as a Pup substrate, all higher molecular weight bands result from multipupylation rather than polypupylation. This illustrates why it is preferable to use SBPK4R-sPupK61R over SBP-sPup, as the pupylation bands with SBP-sPup are mixtures of poly- and multipupylation, making it difficult to assess levels of target labeling. To clarify this in the main text, we added the following description after the sentence in line 236: “as the higher molecular weight multipupylation bands are slightly but noticeably increased with these mutations compared to Halo8KR-PafA”

(13) Line 263: The authors selected DH5 for further experiments due to its efficiency, but the data suggest that the performance of DH1 to DH5 is similar.

We appreciate your question about the different dasatinib HTL derivatives. However, our data clearly show that DH2-5 derivatives bind significantly more effectively to Halo-PafA in vitro and in live cells compared to DH1 (Figure 4A and B). Additionally, the DH2-5 derivatives result in dramatically increased pupylation of the target protein in vitro and noticeable enhancement in live cells (Figure 4C and D). Among DH2 to DH5, there is no obvious difference in binding to Halo-PafA or pupylation of the target protein. Therefore, we chose DH5, as we believe that the longer linker in DH5 may facilitate the binding of a more diverse range of target proteins to dasatinib, enabling the discovery of additional target proteins.

(14) Line 309: The authors introduce HCQ and CQ as important drugs but then investigate the mechanism using DC661 without introducing or justifying the choice of this compound.

Thank you for your point. We explained the reason to choose DC661, a dimer form of CQ, instead of CQ for the synthesis of an HTL derivative in line 310. “assuming that a dimer would enhance binding affinity as previously described.” As the dimer forms of a drug or a small molecule such as testosterone dimers, estrogen dimers, and numerous anticancer drug dimers have been often developed to enhance drug effects (Paquin A et., Molecules 2021). Similarly, dimer forms of HCQ/CQ have been introduced and shown to be more potent (Hrycyna CA et al., ACS Chem Biol 2014; Rebecca VW et al., Cancer Discovery 2019). We expected that using a dimer form might offer higher probability to identify target proteins for HCQ/CQ.

(15) The authors suggest that multipupylation levels were enhanced but do not explain whether this might benefit the system or introduce other issues. Clarifying this point would provide valuable insight for potential users of this system.

Thank you for your thoughtful suggestion. Polypupylation likely leads to biased enrichment of a limited set of target proteins, and its levels may not correlate with the binding affinity of target proteins to the small molecule of interest, features that can negatively impact target-ID. In contrast, multipupylation may be correlated with binding affinity or interaction frequency, as we observed increased levels of multipupylation with higher Pup concentrations and longer incubation times. This suggests that target proteins with multiple lysines in proximity to PafA can be sequentially pupylated, starting with the most accessible lysine. However, if a target protein has only one accessible lysine, pupylation will occur only once, regardless of the protein’s affinity to the small molecule. In summary, while polypupylation may be a drawback for target-ID, multipupylation could be useful for both target-ID and understanding binding mode. To elaborate on this, we added the following additional explanation after the sentence in line 152: “, whereas multipupylation is more likely correlated with binding affinity or interaction frequency.”

(16) The author should address whether the Halotag ligand modification of the drug alters the binding properties between the drug and targets. That may be causing artifact binding of the drug and other proteins.

Thank you for your insightful comment. Yes, it is true that chemical modifications of the small molecule of interest, such as linker derivatization (e.g., HTL) or photo-affinity labeling, generally lead to reduced activity or affinity compared to the original molecule. Synthesizing a derivative is a common challenge across all target-ID methods, except for modification-free approaches, as we mentioned in the Discussion. However, modification-free methods like DARTS, CETSA, and TPP have their own limitations, including low sensitivity or high false positive rates. Identifying the optimal position for chemical modification on the small molecule of interest is critical. We chose dasatinib and HCQ/CQ as model compounds, because previous studies provided insights into their derivative synthesis. In addition, our data show that DH5 retains robust kinase inhibitory activity (Figure 4-figure supplement 2), and DC661-H1 exhibits potent autophagy inhibition (Figure 6-figure supplement 1). For novel compounds, a thorough structure-activity relationship study is essential to identify the optimal position for HTL derivative synthesis.

(17) The author stated there is no observable toxicity in zebrafish without providing a detailed analysis or enough data. Further analysis of the expression of Halo-PafA and its substrate sPup influence on toxicity or side effects to the living cells or animals would be needed. It is important for in vivo applications.

Thank you for your constructive suggestion. We have now included additional experimental data in Figure 7-figure supplement 1, showing no toxicity in zebrafish embryos expressing the POST-IT system. We assessed toxicity in two ways: by injecting the POST-IT DNA plasmid into one-cell-stage embryos for acute expression, and by using embryos from transgenic zebrafish expressing POST-IT under a heat-shock inducible promoter. Neither the injection nor the heat-shock activation of POST-IT expression resulted in any noticeable toxicity.

Author response:

The following is the authors’ response to the previous reviews.

eLife Assessment

This important work presents two studies on predictive processes in subjects with and without tinnitus. The evidence supporting the authors' claims is compelling, as their second study serves as an independent replication of the first. Rigorous matching between study groups was performed, especially in the second study, increasing the probability that the identified differences in predictive processing can truly be attributed to the presence of tinnitus. This work will be of interest to researchers, especially neuroscientists, in the tinnitus field.

We thank the editors at elife very much for their favorable assessment of our manuscript. Based upon the comments of the reviewer, we aimed to further improve our manuscript to be a valuable addition to the tinnitus research field.

Public Reviews:

Reviewer #2 (Public review):

Summary:

This study aimed to test experimentally a theoretical framework that aims to explain the perception of tinnitus, i.e., the perception of a phantom sound in the absence of external stimuli, through differences in auditory predictive coding patterns. To this aim, the researchers compared the neural activity preceding and following the perception of a sound using MEG in two different studies. The sounds could be highly predictable or random, depending on the experimental condition. They revealed that individuals with tinnitus and controls had different anticipatory predictions. This finding is a major step in characterizing the top-down mechanisms underlying sound perception in individuals with tinnitus.

Strengths:

This article uses an elegant, well-constructed paradigm to assess the neural dynamics underlying auditory prediction. The findings presented in the first experiment were partially replicated in the second experiment, which included 80 participants. This large number of participants for an MEG study ensures very good statistical power and a strong level of evidence. The authors used advanced analysis techniques - Multivariate Pattern Analysis (MVPA) and classifier weights projection - to determine the neural patterns underlying the anticipation and perception of a sound for individuals with or without tinnitus. The authors evidenced different auditory prediction patterns associated with tinnitus. Overall, the conclusions of this paper are well supported, and the limitations of the study are clearly addressed and discussed.

Weaknesses:

Even though the authors took care of matching the participants in age and sex, the control could be more precise. Tinnitus is associated with various comorbidities, such as hearing loss, anxiety, depression, or sleep disorders. The authors assessed individuals' hearing thresholds with a pure tone audiogram, but they did not take into account the high frequencies (6 kHz to 16 kHz) in the patient/control matching. Moreover, other hearing dysfunctions, such as speech-in-noise deficits or hyperacusis, could have been taken into account to reinforce their claim that the observed predictive pattern was not linked to hearing deficits. Mental health and sleep disorders could also have been considered more precisely, as they were accounted for only indirectly with the score of the 10-item mini-TQ questionnaire evaluating tinnitus distress. Lastly, testing the links between the individuals' scores in auditory prediction and tinnitus characteristics, such as pitch, loudness, duration, and occurrence (how often it is perceived during the day), would have been highly informative.

Thank you very much for your careful evaluation of our manuscript. We agree with you that our study design has some limitations such as the assessment of higher frequencies, comorbidities, and tinnitus characteristics. In our discussion, we aimed to acknowledge these issues for future research to improve this study design and gain more insights into neural tinnitus processes.

See e.g.:

Line 946-949:

“Additionally, we rigorously controlled for hearing loss in Study 2, however, pure-tone audiometric testing was solely performed up to 8kHz and we were therefore not able to draw conclusions regarding hearing impairments in higher frequencies and their influence on the effects.”

Line 949-954:

“Moreover, we did not screen our participants for hyperacusis. This hypersensitivity to mild sounds is widely correlated with the sensation of tinnitus and underlying neural mechanisms are potentially intertwined with tinnitus processes (Schilling et al., 2023; Yukhnovich et al., 2023; Zheng, 2020). Screening for hyperacusis in future work can therefore reveal more details on participant characteristics influencing predictive processing.”

Line 955-958:

“In both studies, tinnitus distress was not correlated with the reported prediction effects. Nevertheless, tinnitus can also be characterized by other features such as its loudness, pitch or duration which were not included in the experimental assessment.”

Line 958-963:

“Additionally, we solely used a short version of the Mini-TQ (Goebel and Hiller, 1992) in Study 2, which did not allow us to relate prediction scores to subscales like sleep disturbances which potentially influence cognitive functioning and thus predictive processing. Next to sleeping disorders and distress, tinnitus is often also accompanied by psychological comorbidities such as depression or anxiety (Langguth, 2011) which are potential confounds of the results.”

Comments on revisions:

Thank you for your responses. There are a few remaining points that, if addressed, could further enhance the manuscript:

- While the manuscript acknowledges the limitation of not matching groups on hearing thresholds in Study 1, a deeper analysis of participants' hearing abilities and their impact on MEG results, similar to that conducted in Study 2, would be valuable. Specifically, including a linear model that considers all frequencies, group membership, and their interactions could highlight differences across groups. Additionally, examining the effect of high-frequency hearing loss on prediction scores, as performed in Study 2, would strengthen the analysis, particularly given the trend noted (line 719). Such an addition could make a significant contribution to the literature by exploring how hearing abilities may influence prediction patterns.

We appreciate your feedback and agree with you that it is a crucial question how hearing abilities influence prediction patterns in tinnitus. However, as hearing status was not assessed in the control group in study 1, we are unfortunately not able to include linear models to investigate differences across groups in this sample. This led us to the implementation of study 2 with a comprehensive hearing assessment to investigate group differences. We highlighted this issue in our methods section.

Line 170-172:

“As pure-tone audiometric testing was not included for the control subjects, group comparisons between hearing thresholds were not feasible.”

- The connection with the hippocampal regions (line 864) remains somewhat unclear. While the inclusion of the Paquette reference appropriately links temporal region activity with tinnitus, it does not fully support the statement: "An increased focus on hippocampal regions, e.g., in fMRI, patient, or animal studies, could be a worthwhile complement to our MEG work, given the outstanding relevance of medial temporal areas in the formation of associations in statistical learning paradigms"

Thank you for your constructive input. This section is purely speculative, and we do not aim to provide strong claims or expected results but solely point out potential future research directions.

- Authors should add a comparison of participants mini-TQ scores on both studies

We appreciate your input and added a comparison of mini TQ-scores between samples. For study 1, all subscales were included, however, we computed the comparison solely based on the items of the mini-TQ to increase comparability. The results were not significant, i.e., tinnitus distress values did not differ between studies.

Line 629-632:

“We additionally compared tinnitus distress values assessed by the mini-TQ (Goebel and Hiller, 1992) between study 1 and study 2 to detect potential differences between the samples, however, results of the Welch’s t-test were not significant with t(30.7)=1.27, p\=.214.”

- Authors should add significant level on Fig 6.B as in Fig 3.C, and a n.s on Fig 6.D

Thank you very much for your input, we added significance levels and a n.s. to the Figures 6B and 6D.

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This article identifies ADGR3 as a candidate GPCR for mediating beige fat development. The authors use human expression data from Human Protein Atlas and Gtex databases and combine this with experiments performed in mice and a murine cell line. They refer to a GPCR bioactivity screening tool PRESTO-Salsa, with which it was found that Hesperetin activates ADGR3. From their experiments, authors conclude that Hesperetin activates ADGR3, inducing a Gs-PKA-CREB axis resulting in adipose thermogenesis.

Strengths:

The authors analyze human data from public databases and perform functional studies in mouse models. They identify a new GPCR with a role in thermogenic activation of adipocytes.

Considerations:

Selection of ADGRA3 as a candidate GPCR relevant for mediating beiging in humans:

The authors identify GPCRs that are expressed more highly in murine iBAT compared to iWAT in response to cold and assess which of these GPCRs are expressed in human subcutaneous or visceral adipocytes. Although this strategy will identify GPCRs that are expressed at higher levels in brown fat compared to beige and thus possibly more active in thermogenic function, the relevance in choosing GPCRs that also are expressed in unstimulated human white adipocytes should be considered. Thermogenic activity is not normally present in human white adipocytes. It would have strengthened the GPCR selection if the authors instead had assessed the intersection with human brown adipocytes that were activated with norepinephrine.

We appreciate your constructive feedback and believe that by adopting this refined strategy, we will strengthen our selection of GPCRs related to adipose thermogenesis in other ongoing studies. We look forward to continuing our research in this area and contributing to the understanding of adipose thermogenesis and its potential therapeutic applications. Thank you once again for your valuable input. 

Strategy to investigate the role of ADGRA3 in WAT beiging:

Having identified ADGRA3 as their candidate receptor, the authors investigated the receptor in mouse models, the murine inguinal adipocyte cell line 3T3 and in human subcutaneous adipose progenitors (HAdsc) differentiated in vitro. Calling the human cells "beige" is a stretch as these cells are derived from a white adipose depot. The authors do observe regulation in UCP1 and abundance of mitochondria following modification of ADGRA3 in the cells. However, in future studies, it should be considered if the receptor rather plays a role in differentiation per se, and perhaps not specifically in thermogenic differentiation/activity.

Regarding the reviewer's suggestion to consider whether ADGRA3 plays a role in differentiation per se, rather than specifically in thermogenic differentiation/activity, we acknowledge that this is an important consideration. Our current studies have focused on the role of ADGRA3 in regulating UCP1 expression and mitochondrial abundance, which are hallmarks of adipose thermogenic activity. However, we recognize that ADGRA3 may also have broader roles in adipocyte differentiation and function that are not limited to thermogenesis.

To address this point, in future studies, we plan to conduct additional experiments to investigate the potential role of ADGRA3 in adipocyte differentiation, including its effects on the expression of markers of adipocyte differentiation and its impact on adipocyte metabolism and function. These studies will provide further insights into the mechanisms by which ADGRA3 regulates adipocyte biology.

According to the Human Protein Atlas and Gtex databases, ADGRA3 is not only expressed in adipocytes, but also in other tissues and cell types. The authors address this by measuring the expression in a panel of these tissues, demonstrating a knockdown not only in the adipose tissue, but also in the liver and less pronounced in the muscle (Figure S2). It should thus be emphasized that the decreased TG levels in serum and liver in the mice might in fact depend on Adgra3 overexpression in the liver. Even though this might not have been the purpose of the experiment, it is important to highlight this as it could serve as hypothesis building for future studies of the function of this receptor.

Thank you for your thoughtful comments and feedback. We appreciate the insight provided by the Human Protein Atlas and Gtex databases regarding the tissue distribution of ADGRA3. We fully acknowledge that the decreased TG levels observed in both the serum and liver of the mice might be linked to the overexpression of Adgra3 in the liver.

Although this was not the primary objective of our experiment, we agree that this observation is worth highlighting as it could serve as a basis for future hypothesis-driven research on the functional role of ADGRA3 in different tissues. In light of your comments, we emphasized this potential link between Adgra3 overexpression in the liver and reduced TG levels in discussion, as follows.

“…the precise mechanisms underlying the influence of on adipose thermogenesis. Furthermore, it is crucial to highlight that the observed decrease in TG levels in both serum and liver (Figure 4-figure supplement 2C-D) might be attributed to the significant increase in Adgra3 expression in the liver, which is a consequence of the nanoparticle-mediated overexpression of Adgra3. While the exact mechanism remains to be fully elucidated, this correlation suggests a potential link between Adgra3 overexpression in the liver and reduced TG levels in the serum. We will employ more sophisticated models in subsequent studies to further…”

Reviewer #3 (Public Review):

Summary:

The manuscript by Zhao et al. explored the function of adhesion G protein-coupled receptor A3 (ADGRA3) in thermogenic fat biology.

Strengths:

Through both in vivo and in vitro studies, the authors found that the gain function of ADGRA3 leads to browning of white fat and ameliorates insulin resistance.

Weaknesses:

There are several lines of weak methodologies such as using 3T3-L1 adipocytes and intraperitoneal(i.p.) injection of virus. Moreover, as the authors stated that ADGRA3 is constitutively active, how could the authors then identify a chemical ligand?

Comments on revised version:

The revised manuscript by Zhao et al. has limited improvement. The authors refused to perform revised experiments using primary cultures even though two reviewers pointed out the same weakness (3T3-L1 adipocytes are unsuitable). Using infrared thermography to measure body temperature is also problematic.

Thanks for your comments. We regret that human adipocytes induced from human adipose-derived stem cells (hADSCs) were not recognized as primary cultures by multiple reviewers. Therefore, we have included relevant experimental results of mouse primary adipocytes induced from stromal vascular fraction (SVF) in Figure 8E-H as a supplement. The thermal imaging device was used to measure the temperature of BAT, while the body temperature was measured at 9:00 using a rectal probe connected to a digital thermometer.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

This paper presents a data processing pipeline to discover causal interactions from time-lapse imaging data, and convicingly illustrates it on a challenging application for the analysis of tumor-on-chip ecosystem data. The core of the discovery module is the original tMIIC method of the authors, which is shown in supplementary material to compare favourably to two state-of-the-art methods on synthetic temporal data on a 15 nodes network.

Strengths:

This paper tackles the problem of learning causal interactions from temporal data which is an open problem in presence of latent variables. The core of the method tMIIC of the authors is nicely presented in connection to Granger- Schreiber causality and to the novel graphical conditions used to infer latent variables and based on a theorem about transfer entropy. tMIIC compares favourably to PC and PCMCI+ methods using different kernels on synthetic datasets generated from a network of 15 nodes. A full application to tumor-onchip cellular ecosystems data including cancer cells, immune cells, cancer-associated fibroblasts, endothelial cells and anti cancer drugs, with convincing inference results with respect to both known and novel effects between those components and their contact.

The code and dataset are available online for the reproducibility of the results.

We thank Reviewer #1 for highlighting the main results and strengths of our paper, as well as, for his/her recommendations below to further improve the manuscript.

Weaknesses:

The references to ”state-of-the-art methods” concerning the inference of causal networks should be more precise by giving citations in the main text, and better discussed in general terms, both in the first section and in the section of presentation of CausalXtract. It is only in the legend of the figures of the supplementary material that we get information. Of course, comparison on our own synthetic datasets can always be criticized but this is rather due to the absence of common benchmark and I would recommend the authors to explicitly propose their datasets as benchmark to the community.

Following Reviewer #1’s suggestion, we now compare tMIIC’s performance to other state-of-the-art causal discovery methods for time series data in the main text and in a new Figure 2. This Figure 2 also highlights the relation between graph-based causal discovery methods for time series data and Granger-Schreiber temporal causality, as discussed in more details in Methods (Theorem 1).

We also agree about the importance of sharing benchmark datasets with the community. This is the reason why we provide the dynamical equations of the 15-node benchmarks in Supplementary Tables 1 & 2, so that anyone can generate equivalent time series datasets of any desired length.

Reviewer #2 (Public review):

Summary:

The authors propose a methodology to perform causal (temporal) discovery. The approach appears to be robust and is tested in the different scenarios: one related with live-cell imaging data, and another one using synthetic (mathematically defined) time series data. They compare the performance of their findings against another well-know method by using metrics like F-score, precision and recall,

Strengths:

Performance, robustness, the text is clear and concise, The authors provide the code to review.

We thank Reviewer #2 for his/her positive assessment of our work and the suggestions below to improve the manuscript.

Weaknesses:

One concern could be the applicability of the method in other areas like climate, economy. For those areas, public data are available and might be interesting to test how the method performs with this kind of data.

While our main expertise concerns the analysis of biological and biomedical data, we agree that tMIIC (which is included in MIIC R package) could in principle be applied to other areas, like climate, economy.

We have not included benchmarks on such diverse types of datasets in the present manuscript, which focuses on CausalXtract’s pipeline for the analysis and causal interpretation of live-cell time-lapse imaging data from complex cellular systems.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to elucidate the diversity and gene expression patterns of marine plankton using innovative collection and sequencing methodologies. Their work investigates the taxonomic and functional profiles of planktonic communities, providing insights into their ecological roles and responses to environmental changes.

Strengths:

The methodology utilized in this study, particularly the combination of single-cell sequencing and advanced bioinformatics techniques, represents a significant advancement in the field of plankton research. The application of the Smart-seq2 protocol for cDNA synthesis, followed by rigorous quality control measures, ensures high-quality data generation. This comprehensive approach not only enhances the resolution of the obtained genetic information but also allows for a more detailed exploration of the diversity and functional potential of the phytoplankton community.

One of the major strengths of this study is the rigorous methodological approach, including precise sampling techniques and robust data analysis protocols, which enhance the reliability of the results. The use of advanced sequencing technologies allows for a comprehensive assessment of gene expression, significantly contributing to our understanding of plankton diversity and its implications for marine ecosystems.

Weaknesses:

While the evidence presented is solid, there are areas where the analysis could be expanded. The authors could further explore the ecological interactions within plankton communities, which would provide a more holistic view of their functional roles. Additionally, a broader discussion of the implications of their findings for marine conservation efforts could enhance the manuscript's impact.

The choice of both the plankton net and filter pore size during the plankton collection process is critical, as these factors directly impact the types of phytoplankton collected. The use of a 25 μm filter paper, in particular, may result in the omission of many eukaryotic phytoplankton species. This limitation, combined with the characteristics of the plankton net, could affect the comprehensiveness and accuracy of the results, potentially influencing the study's conclusions regarding phytoplankton diversity.

The timing of fixation is crucial, as it directly affects whether the measured transcriptome accurately represents the organisms' actual transcriptional state in their native water environment. If fixation occurred a significant time after sample collection, the transcriptomic data may not reflect their true in situ transcriptional activity, which greatly reduces the relevance of this method.

Thank you for your time, effort, and expertise.

We agree that additional analyses could improve our understanding of the plankton communities sampled. We have conducted an array of alternative analyses that were not included in the current manuscript and plan to perform new analyses over the next few months as part of a deeper revision of the manuscript. We are especially interested in “providing a more holistic view of the functions” of individual plankton within the community.

As for the protocol details, the pore size of the filter paper was chosen to focus on ~100 micron-sized organisms as a starting point: they are likely to contain more RNA than smaller organisms, making them well suited for an initial proof of concept of the methodology. That choice, however, is not particularly tightly constrained, therefore smaller plankton could be captured. This is supported by the lack of correlation, in our data, between organismal size and number of detected sequencing reads.

Timing to cell death/fixation is a common question we receive not just in this manuscript but any RNA-Seq from primary samples. In this case, plankton were seen swimming until picking, and after picking each organism was deposited within two seconds into a lysis buffer for fixation. Therefore, we do not have reason to believe that the transcriptional activity sampled in the sequencing reads differs in any major way from the one in living plankton. Nonetheless, a study specifically testing the effect of time between ocean sampling and reverse transcription would provide more quantitative information on this point.

Reviewer #2 (Public review):

Summary:

The paper introduces Ukiyo-e-Seq, a novel method integrating microscopy with single-cell transcriptomics to study individual, uncultured eukaryotic plankton cells. By combining microscopic imaging with transcriptomic analysis, the approach links plankton morphology to gene expression, enabling taxonomic identification and functional protein exploration. Ukiyo-e-Seq was tested on 66 microbial eukaryotic cells, revealing taxonomic diversity across four superkingdoms and allowing analysis of protein complexes and developmental genes in individual species. According to the authors, this method has the potential to advance single-cell marine biodiversity studies by addressing limitations in traditional taxonomy and metatranscriptomics, especially for rare or uncultured organisms.

However, the study's conclusions are often weakly supported by data, particularly given that this is not the first study to combine microscopy and single-cell transcriptomics of eukaryotic plankton using Smart-seq2.

Strengths:

A notable strength is the authors' generation of several single-cell transcriptomes for the diatom Chaetoceros, which could benefit from greater focus rather than broadly addressing eukaryotic single cells.

Weaknesses:

The study lacks comparison with other single-cell transcriptomics studies and it was presented as the first study that combines imaging and single-cell transcriptomics (smart-seq2) of eukaryotic plankton while in fact it is not. The sampling methodology is not replicable as the authors used a tea strainer instead of standard plankton collection equipment to filter larger cells. Terminology throughout the paper is unconventional, such as "public and private contigs," "single-organism genomics," "highly expressed contigs," and "optical methods." Additionally, the authors did not specify which database was used for taxonomic assignments. These issues may stem from the authors' limited background in microbial ecology. Overall, the study has many drawbacks and it could benefit from complete rewriting and focusing mainly on single-cell transcriptomics of diatoms.

Thank you for your time, effort, and expertise.

There might be a bit of confusion between single-cell and single-organism sequencing, likely due to lack of clarity in our initial submission. In particular, in this manuscript no effort was spent trying to dissociate oligocellular plankton into individual cells before sequencing. While probably feasible, we expect that to be technically much harder than single-organism sequencing as performed here. The reviewer does not reference a published paper where combined imaging and RNA-Seq of individual uncultured plankton has been achieved, and we were unable to find one in the scientific literature. As stated in the manuscript, others have already performed some work on cultured plankton and single-organism sequencing (without matching images) of uncultured environmental microorganisms.

The suggestion to focus on a smaller biological niche such as diatoms and adopt language more familiar to that specific community is well received. Indeed, given that organisms as diverse as fish larvae and diatoms could be profiled with Ukiyo-e-Seq, future studies could use the same method to address specific questions with a deeper and more narrow scope. However, this manuscript is demonstrating the feasibility of Ukiyo-e-Seq and its ability to produce usable data for a broad spectrum of organisms: part of the scientific audience might not have a specific interest in diatoms.

The tea strainer was used for coarse pre-filtering: the exact pore size, geometry and factory tolerance on those measurements are inconsequential because each organism is later chosen (or not) based on a high-resolution microscopy image (or multiple, if fluorescence is considered). This really is a strength of Ukiyo-e-Seq over FACS or droplet-based sorters, which can only collect coarse optical information from each organism for (typically) less than 1 millisecond. In Ukiyo-q-Seq, while the actual decision to pick an individual is currently manual (by the operator of the picker), it can be automated in principle. For instance, one could build a machine learning model of plankton taxonomy based on a large collection of labelled images and use predictions from such a model to automatically drive the picker (e.g. focussing on diatoms), increasing throughput. Even in that case, however, the initial filtering stages using tea strainers, plankton nets, filter paper etc. would not be critical for the final selection of individuals as long as they are not too restrictive.

The database used for taxonomic assignment was the NCBI non-redundant nucleotide database, accessed through the reference library provided by Kraken2 (nt).

Reviewer #3 (Public review):

Gatt et al. present a novel take on single-cell RNA-sequencing from complex planktonic samples, introducing an approach they aptly named Ukiyo-e-Seq. This work combines environmental sampling with cell picking, microscopic imaging, and Smart-seq2 single-cell RNA sequencing to profile uncultured eukaryotic plankton. Developing single-cell approaches for such ecosystems is critical, given the poor representation of many planktonic species in cultures and reference databases. This work could help bridge existing technological gaps between morphological and molecular studies of aquatic microeukaryotes

The authors argue that microscopy does not provide information on the biochemistry of species under consideration. At best, it provides taxonomic labeling of species within a sample, yet imaging fails to assess their metabolic state or to disentangle cryptic species. In a standard metatranscriptomic setup, the sequence pool is described by aligning assembled contigs with reference databases to obtain functional and taxonomic information. This complex community-level data is impossible to parse at the single-organism level. Moreover, by relying on reference datasets, a lot of potential information can be missed. The aim of the approach is to combine the strengths of both methods, generating single-cell transcriptomic data linked to individual plankton images.

Strengths:

Ukiyo-e-Seq generated a valuable dataset by combining imaging and transcriptomics for individual planktonic organisms from environmental samples. This multimodal approach has the potential to improve taxonomic predictions and functional insights at the single-organism level. This manuscript demonstrates the technical feasibility of such an approach. Data of this type is rare and thus represents a valuable resource to further advance single-cell sequencing of planktonic species from environmental samples.

Weaknesses:

(1) The merge-split strategy, where single-cell reads are pooled prior to assembly, is counterintuitive. Pooling obscures the single-organism resolution that single-cell methods aim to achieve. The approach might be useful for assembling low-coverage contigs, but risks masking unique expression profiles for transcripts unique to a given well. As an alternative, the authors could assemble each well independently to obtain well-specific transcriptomic bins. Assemblies could then be clustered based on sequence similarity, thereby imposing strict clustering parameters to maintain resolution, to create a common reference for downstream analysis if needed. In my opinion, better results would be obtained by implementing a per-well assembly and read mapping.

(2) The focus on the top five most expressed contigs throughout the manuscripts' data analysis is a limiting choice, as it excludes most contigs. In the preprint, we are presented with a very narrow view of the data. Visualising the entire range of assembled contigs would provide a better picture of the transcriptomic composition and diversity per well. It would be interesting to assess if the full information could be used to preliminary bin transcriptomic sequences from individual wells, for example, by gathering all 'private' contigs with high read coverage in a single well. Does such a set represent a single complete eukaryotic transcriptome?

(3) I missed a verification with (broad-scale) taxonomic assessments based on the associated microscopic images. In their goals, the authors state that a joint approach has the potential to discover new taxonomic biodiversity. I agree, and to me, this is what is exciting about the preprint, yet I miss an example or the right bioinformatic implementation to drive home this claim. Are there organisms in wells where poor taxonomic annotations, based on alignment to a reference database or the LCA approach implemented in Kraken2, would usually result in ignoring the species in classic metatranscriptomics? Can you advance the taxonomic annotation by referring back to the organisms' picture? Can manual assessment of taxonomy advance the results from the LCA approach?

(4) The current use of AlphaFold to predict protein structures does not convincingly add to the study's core objectives.

Overall, Ukiyo-e-Seq presents a promising method for studying single-cell diversity in environmental samples, though the bioinformatic pipeline requires refinement to support some of the claims made by the authors. Additionally, the manuscript would benefit from clarity and additional details in its methods and a more consistent approach to presenting results and summary statistics across all assembled contigs and all sampled wells, rather than focusing on selected wells.

Thank you for your time and effort, and for your expertise on the matter.

The suggestions to conduct additional bioinformatic analyses to explore more fully the criticality and potential of various design choices (e.g. meta-assembly) are well received. We have tried some of those ideas already (e.g. assembling individual wells) and we have considered but not yet conducted or polished others (e.g. a more thorough taxonomic verification). We will endeavour to carry out as many of those analyses as possible during the deeper revision process in the coming months.

AlphaFold 3’s use was designed to demonstrate the ability to investigate protein-protein interactions from individual species. When two peptide sequences are detected within the same well, they are more likely to be potential interacting partners than in a metatranscriptomic study, because the compartmentalisation of reads into tens or hundreds of wells greatly reduces the search space of potential interaction partners (which has a baseline runtime complexity of n squared, where n is the number of peptide sequences identified).

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