Author response:

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

Reviewer #1 (Public review):

This work focuses on the connection strength of the corticostriatal projections, without considering the involvement of synaptic plasticity in sensory integration.

Thank you for raising this point. Indeed, sensory integration is a complex process with a multitude of factors beyond connectivity patterns and synaptic strength. In addition, it is true that both connectivity levels and synaptic strength can be modified by plasticity. 

We modified our conclusion as follows, line 354: 

“Since the inputs to a single SPN represent only a limited subset of whisker columns, a complete representation of whiskers could emerge at the population level, with each SPN’s representation complementing those of its neighbors (Fig. 7). These observations raise the hypothesis of a selective or competitive process underlying the formation of corticostriatal synapses. The degree of input convergence onto SPNs could be modulated by plasticity, potentially enabling experience-driven reconfiguration of S1 corticostriatal coupling. “

Reviewer #2 (Public review):

A few minor changes to the figures and text could be made to improve clarity.

We thank you for having taken the time to indicate where changes could benefit the paper. We followed your recommendations. 

Reviewer #3 (Public review):

(1) Several factors may contribute to an underestimation of barrel cortex inputs to SPNs (and thus an overestimate of the input heterogeneity among SPNs). First, by virtue of the experiments being performed in an acute slice prep, it is probable that portions of recorded SPN dendritic trees have been dissected (in an operationally consistent anatomical orientation). If afferents happen to systematically target the rostral/caudal projections of SPN dendritic fields, these inputs could be missed. Similarly, the dendritic locations of presynaptic cortical inputs remain unknown (e.g., do some inputs preferentially target distal vs proximal dendritic positions?). As synaptic connectivity was inferred from somatic recordings, it's likely that inputs targeting the proximal dendritic arbor are the ones most efficiently detected. Mapping the dendritic organization of synapses is beyond the scope of this work, but these points could be broached in the text.

Thank you for this analysis. The positions of S1 spines have been mapped on the SPN dendritic arbor by the group of Margolis (B.D. Sanabria et al., ENeuro 2024,10.1523/ENEURO.0503-23.2023). They observed that S1 spines were at 80 % on dendrites but with a specific distribution, on average rather close to the soma.  In this study, S1 spines did not exhibit a specific distribution that would systematically hinder their detection in a slice. But, it remains that the position in the dendritic arbor where an S1 input is received does indeed impact its detection in somatic recordings. We modified the discussion as follows, line 275:

“The LSPS combined with glutamate uncaging mapped projections contained in the slice, intact from the presynaptic cell bodies to the SPN dendrites. Some cortical inputs targeting distal SPN dendrites may have gone undetected, either due to attenuation of synaptic events recorded at the soma or because distal dendritic branches were lost during slice preparation. Indeed, about 80 % of S1 synaptic contacts are distributed along dendrites (Sanabria et al., 2024). However, synapses located distally are proportionally rare (Sanabria et al., 2024), and our estimates suggest that the loss of S1 input was minimal (see Methods). More significantly, our mapping only included projections from neuronal somata located within the S1 barrel field in the slice: projections from cortical columns outside the slice were not stimulated. For this reason, our study characterized connectivity patterns rather than the full extent of connectivity with the barrel cortex.”

We explain our estimation of truncated S1 contacts in the Methods, line 434:

“To estimate the loss of S1 synaptic contacts caused by slice preparation, we modeled the SPN dendritic field as a sphere centered on the soma. S1 synapses were at 80 % distributed radially along dendrites, according to the specific distribution described by Sanabria et al. (2024). The simulation also incorporated the known distribution of SPN dendritic length as a function of distance from the soma (Gertler et al., 2008). Finally, it assumed that synapse placement was isotropic, with equal probability in all directions from the soma. Truncation was simulated by removing a spherical cap at one pole of the sphere, reflecting the depth of our recordings (beyond 80 μm). Based on this simulation, the loss of S1 inputs was < 10 %.”

(2) In general, how specific (or generalizable) is the observed SPN-specific convergence of cortical barrel cortex projections in the dorsolateral striatum? In other words, does a similar cortical stimulation protocol targeted to a non-barrel sensory (or motor) cortex region produce similar SPN-specific innervation patterns in the dorsolateral striatum?

This is an interesting question that could be addressed using the LSPS approach in areas for which ex vivo preparations have been designed to maintain the integrity of the corticostriatal projections, such as A1, M1 and S2.  

We included this point in the discussion, line 299: 

” The speckled connectivity pattern of individual SPNs, arising from the abundant and diffuse cortical innervation in the DLS, suggests that somatosensory corticostriatal synapses are established through a selective and/or competitive process. It is important to determine whether this sparse innervation of SPNs by S1 is a characteristic shared with other projections. In particular, it will be interesting to test this hypothesis on the auditory projections targeting the posterior striatum, where neurons exhibit clear tone frequency selectivity (Guo et al., 2018).”

(3) In general, some of the figure legends are extremely brief, making many details difficult to infer. Similarly, some statistical analyses were either not carried out or not consistently reported.

We thank you for having taken the time to indicate where changes could benefit the paper. We have followed your recommendations. 

Reviewer #1 (Recommendations for the authors):

A few limitations should be discussed in the manuscript:

(1) The manuscript should mention that most corticostriatal synapses are formed at the dendritic spines of the SPNs, not their cell bodies. This is particularly important regarding the analysis and interpretation of the data in Figure 4.

Thank you for this comment. This characteristic is important with regards to a limitation of electrophysiological recordings. This is now discussed:

Line 275:

“The LSPS combined with glutamate uncaging mapped projections contained in the slice, intact from the presynaptic cell bodies to the SPN dendrites. Some cortical inputs targeting distal SPN dendrites may have gone undetected, either due to attenuation of synaptic events recorded at the soma or because distal dendritic branches were lost during slice preparation. Indeed, about 80 % of S1 synaptic contacts are distributed along dendrites (Sanabria et al., 2024). However, synapses located distally are proportionally rare (Sanabria et al., 2024), and our estimates suggest that the loss of S1 input was minimal (see Methods).“

Line 313:

[...],, we found that overlaps between the connectivity maps of SPNs were rare and, when present, involved only a small fraction of the connected sites. This indicates that neighboring SPNs predominantly integrated distinct inputs from the barrel cortex, although it is possible that overlapping inputs received in distal dendrites were not all detected”

(1) SPNs show up- and down-states in vivo, which were not mimicked by the present study since all cells were held at - 80 mV (Line 364) and recorded at room temperature (Line 368). It should be discussed how the conclusion of the present work may be affected by the up/down states of SPNs in vivo.

Thank you for raising this point. Indeed, our experimental conditions were not designed to capture the effects of network oscillatory activity. Instead, LSPS conditions were optimized to reveal monosynaptic connectivity between neurons in S1 and their postsynaptic targets. These optimizations include the use of a high concentration of extracellular divalents (4 mM Ca²⁺ and Mg²⁺) to generate robust yet moderate and spatially-restricted stimulations of cortical cells and reliable neurotransmitter release (Shepherd, Pologruto and Svoboda, Neuron 2003; 10.1016/s0896-6273(03)00152-1; in our study, see Fig. 1D  and Suppl Fig. 2). Investigating the pre- and postsynaptic modulations of the corticostriatal coupling by up- and down-states would require specific conditions. 

The conclusion now acknowledges that functional connectivity is subject to plasticity in general, line 358:

“The degree of input convergence onto SPNs could be modulated by plasticity, potentially enabling experience-driven reconfiguration of S1 corticostriatal coupling.”

(2) In addition to population-level integration (Line 337), sensory integration is likely to involve synaptic plasticity (like via NMDARs), which was not studied in the present work

Thank you for raising this point. Indeed, we agree that sensory integration is a complex process with a multitude of factors beyond connectivity patterns and synaptic strength. We also agree that both connectivity levels and synaptic strength can be modified by plasticity. 

We modified our conclusion as follows, line 354:

“Since the inputs to a single SPN represent only a limited subset of whisker columns, a complete representation of whiskers could emerge at the population level, with each SPN’s representation complementing those of its neighbors (Fig. 7). These observations raise the hypothesis of a selective or competitive process underlying the formation of corticostriatal synapses. The degree of input convergence onto SPNs could be modulated by plasticity, potentially enabling experience-driven reconfiguration of S1 corticostriatal coupling. “

(3) The potential corticostriatal connectivity may be underestimated due to loss of axonal branches during slice resection, and this might contribute to the conclusion of "sparse connectivity". Whether the author has considered performing LSPS studies within the striatum (i.e., stimulating ChR2-expressing cortical axon terminals) and whether this experiment may consolidate the conclusion of the present work.

We appreciate the suggestion to employ Subcellular Channelrhodopsin-2-Assisted Circuit Mapping (sCRACM) to study the density of S1 spines on SPNs dendritic arbor. If ChR2 is broadly expressed in S1, this approach would likely increase spine detection, as spines contacted by presynaptic neurons located inside and outside the slice would now be activated. If ChR2 expression could be restricted to the whisker columns present in our preparation, enhanced detection could still occur, but in this case, it would reflect the activation of spines contacted by specific ChR2⁺ axonal branches that exit and re-enter the slice to form synapses on the recorded SPN. The anatomy of corticostriatal axonal arbors suggest convoluted axonal trajectories could be relatively rare (T. Zheng and C.J. Wilson, J Neurophysiol. 2001; 10.1152/jn.00519.2001; M. Lévesque et al., Brain Res. 1996; 10.1016/0006-8993(95)01333-4).  

Moreover, it is important to remember that sCRACM does not generate connectivity maps between 2 structures, but maps of spines on dendritic arbors (Petreanu L.T. et al., Nature 2009; 10.1038/nature07709.). Precise localization of presynaptic cell bodies was key for the present study, as it enabled distinguishing between different connectivity patterns and between different degrees of convergence of inputs from adjacent S1 cortical columns present in the slice (schematized in Fig. 1). Distinguishing these inputs using the stimulation of axon terminals would require the possibility to express one distinct opsin in each whisker column (or each cortical layer, depending on the axis of investigation). This is an exciting perspective but the technology is not yet available to our knowledge. 

To emphasize our reasons for using LSPS, we revised the final paragraph of the Introduction, line 69: 

“LSPS enabled precise mapping of corticostriatal functional connectivity by identifying cortical sites where stimulation evoked synaptic currents in the recorded SPNs, thereby localizing the cell bodies of their presynaptic neurons. This approach allowed us to determine both the cortical column and layer of origin within the barrel field in the slice for each SPN input.”

Reviewer #2 (Recommendations for the authors):

(1)  Figure 2F: SPN and cortical regions - both are shown in green. The distinction between the two would be clearer if SPNs were made a different color.

Done

(2)  Figure 2H: Based on their data, the authors conclude that since EPSCs in SPNs had small amplitudes (~40pA), only one or a few presynaptic cortical neurons (< 5) were activated by uncaging. It is not clear how this number was estimated. Either this statement should be qualified with data or citations provided to support it.

We thank you for noticing it. We modified this part as follows, line 105:

“Based on known amplitudes of spontaneous and miniature EPSCs in SPNs (10-20 pA on average; Kreitzer and Malenka, 2007; Cepeda et al., 2008; Dehorter et al., 2011; Peixoto et al., 2016), this finding is consistent with the presence of only one or a few presynaptic cells (≤ 5) at each connected site of the map.”

(3) Figure 2I: The top graph is difficult to understand without already seeing the lower plot. Moving it below or to the side would help the reader follow the data more easily.

done

(4) Figure 3D: In Line 162, the authors state, " Furthermore, SPNs receiving input from a single column were often located near others receiving input from multiple ones (Figure 3D), reinforcing that the low functional connectivity with barrel columns in the slice was genuine in these cases." However, Figure 3D does not show spatial information about SPNs relative to each other. This data should be added or the statement adjusted to reflect what is shown in the panel.

Corrected as follows, line 167:

“Furthermore, SPNs receiving input from a single column were often located in slices where other cells received input from multiple ones (Fig. 3D), reinforcing that the low functional connectivity with barrel columns in the slice was genuine in these cases.”

(5) Figure 3F: Are the authors attempting to show how cluster number, cluster width, and connectivity gaps contribute to input field width? If so, this could be clarified by flipping the x- and y-axes so that the input field width is the y-axis in each case. Additionally, the difference between black and white points should be stated (or, if there is no difference, made to be the same). The significance of the dotted red line vs. the solid red lines should also be stated in the figure legend.

These plots illustrate how cluster number, cluster width, and ratio of connectivity gaps over total length vary as a function of input field width. As expected, wider input fields contain more clusters (top). However, the overall density of connected sites does not increase with input field width, as indicated by a higher ratio of connectivity gaps over total length (bottom).

This suggests the presence of a mechanism that regulates the connectivity level of individual SPNs (mentioned in the discussion). We prefer this orientation because the flipped one makes a cluttered panel due to different X axis labels. Symbols and lines were corrected. The correlation coefficients and statistics are now indicated in the panels and in the legend.

(6) Figure 3H: The schematic is very useful for highlighting the core conclusions and is greatly appreciated. The pie charts are a bit hard to see and could be replaced with the percentages stated simply as text within the figure. It would also help to label the panel as "Summary," so readers can quickly identify its purpose.

Done

(7) Figures 4B-D: To clarify the overall percentage, the maximum for the y-axis should be set to 100% in each panel.

Done

Reviewer #3 (Recommendations for the authors):

(1) Though mostly minor, several sentences/statements in the manuscript are confusing or overstated. For example:

a. Lines 62-63: "Studies have found that inputs received by D1 SPNs were stronger than those received by D2 SPNs" is a broad statement that should be qualified.

We changed this sentence for: 

“Electrophysiological studies have found that inputs received by D1 SPNs were stronger than those received by D2 SPNs, both in vivo and ex vivo (Reig and Silberberg, 2014 ; Filipović et al., 2019 ; Kress et al., 2013 ; Parker et al., 2016).”

b. Lines 118-119: "EPSCs evoked with stimulations in L2/3 to L5b had similar amplitudes (Figure 2H), suggesting that L5a dominated these other layers thanks to a greater connectivity with SPNs principally." Here, the word "connectivity" is vague and could easily be misunderstood. Connectivity could refer to the amplitude of corticostriatal EPSCs, which the authors stated are not different between L2/3-L5b. Presumably, connectivity here refers to % of connected SPNs, but for the sake of clarity, the authors should be more explicit, e.g,. "...L5a dominated the other layers because a larger fraction of SPNs received connections from L5a, rather than because L5a synapses were stronger."

We changed the sentence for (line 122): 

“EPSCs evoked with stimulations in L2/3 to L5b had similar amplitudes (Fig. 2H), suggesting that L5a dominance over these other layers is primarily due to a higher likelihood of SPNs being connected to it, rather than to stronger synaptic inputs.”

c. In the Figure 4 legend, (A) says "Four example slices with 2 to 4 recordings. Same as in Figure 2A." Did the authors mean Figure 3A?

Done

d.Line 184: Should Figure 4B, C actually be Figure 4D?

Done

(2) Line 32: typo in Sippy et al. reference.

Done

(3) In Figure 2I, the label "dSPN" is confusing, as in the literature, dSPN often refers to the direct pathway SPN.

Done

(4) The y-axes in Figure 3C should be better labeled/explained.

Fig.3C. Median (red) and 25-75th percentiles (box) of cluster width and spacing, expressed in µm (left Y axis) and number of cortical columns (right Y axis). Labels have been changed in the figure.

(5)  Lines 150-152: "...45 % of the input fields with several clusters produced no synaptic response upon stimulation." This wording is confusing. It can be inferred that the authors mean "no synaptic response in the gaps between clusters." However, their phrasing omits this crucial detail and reads as though those input fields produce no response at all.

We changed this sentence for (line 154):

“Strikingly, regions lacking evoked synaptic responses (i.e., connectivity gaps) made up an average of 45 % of the length of input fields with multiple clusters (maps collapsed along the vertical axis; Fig. 3F, bottom). “

(6)  Lines 184-186: "DLS SPNs could receive inputs from the same domain in the barrel cortex and yet have patterns of cortical innervation without or little redundancy." This should be rephrased to "with little to no redundancy."

Done

(7)  Lines 186-187: "They support a connectivity model in which synaptic connections on each SPNs..." should be revised to "connections to each SPN...".

Done

eLife Assessment

In this manuscript, the authors describe a software package for automatic differentiation of action potentials generated by excitatory and inhibitory neurons, acquired using high-density microelectrode arrays. The work is valuable as it offers a tool with the potential to automatically identify these neuron types in vitro. It is solid, as it provides a tool to identify putative excitatory and inhibitory neurons on high-density electrode arrays, which can be used in conjunction with other existing spike sorting pipelines.

Reviewer #1 (Public review):

Summary:

The authors note that while many software packages exist for spike sorting, these do not automatically differentiate with known accuracy between excitatory and inhibitory neurons. Moreover, most existing spike sorting packages are for in vivo use, where the majority of electrodes are separated from each other by several hundred microns or more. There is a need for spike sorting packages that can take advantage of high-density electrode arrays where all electrodes are within a few tens of microns from other electrodes. Here, the authors offer such a software package with SpikeMAP, and they validate its performance in identifying parvalbumin interneurons that were optogenetically stimulated.

Strengths:

The main strength of this work is that the authors use ground truth measures to show that SpikeMAP can take features of spike shapes to correctly identify known parvalbumin interneurons against a background of other neuron types. They use spike width and peak to peak distance as the key features for distinguishing between neuron types, a method that has been around for many years (Barthó, Peter, et al. "Characterization of neocortical principal cells and interneurons by network interactions and extracellular features." Journal of neurophysiology 92.1 (2004): 600-608.), but whose performance has not been validated in the context of high-density electrode arrays.

Another strength of this approach is that it is automated - a necessity if your electrode array has 4096 electrodes. Hand-sorting or even checking such a large number of channels is something even the cruellest advisor would not wish upon a graduate student. With such large channel counts, it is essential to have automated methods that are known to work accurately. Hence, the combination of validation and automation is an important advance.

A nice feature of this work is that with high-density electrode arrays, the spike waveforms appear on multiple nearby electrodes simultaneously. And since spike amplitudes fall off with distance, this allows triangulation of neuron locations within the regular electrode array. Thus, spike correlations between neuron types, or within neuron types, can be plotted as a function of distance. While SpikeMAP is not the first to do this (Peyrache, Adrien, et al. "Spatiotemporal dynamics of neocortical excitation and inhibition during human sleep." Proceedings of the national academy of sciences 109.5 (2012): 1731-1736.), it is a welcome capability of this package.

It is also good that the code for this package is open-source, allowing a community of people (I expect in vitro labs will especially want to use this) to use the code and further improve it.

Weaknesses:

As this code was developed for use with a 4096-electrode array, it is important to be aware of double counting neurons across the many electrodes. I understand that there are ways within the code to ensure that this does not happen, but care must be taken in two key areas: First, action potentials traveling down axons will exhibit a triphasic waveform that is different from the biphasic waveform that appears near the cell body, but these two signals will still be from the same neuron (for example, see Litke et al., 2004 "What does the eye tell the brain: Development of a System for the Large-Scale Recording of Retinal Output Activity"; figure 14). I did not see anything that would directly address this situation, so it might be something for you to consider in updated versions of the code. Second, spike shapes are known to change when firing rates are high, like in bursting neurons (Harris, K.D., Hirase, H., Leinekugel, X., Henze, D.A. & Buzsáki, G. Temporal interaction between single spikes and complex spike bursts in hippocampal pyramidal cells. Neuron 32, 141-149 (2001)). I did not see this addressed in the present version of the manuscript.

Another area for possible improvement would be to build on the excellent validation experiments you have already conducted with parvalbumin interneurons. Although it would take more work, similar experiments could be conducted for somatostatin and vasoactive intestinal peptide neurons against a background of excitatory neurons. These may have different spike profiles, but your success in distinguishing them can only be known if you validate against ground truth, like you did for the PV interneurons.

Appraisal:

This work addresses the need for an automated spike sorting software package for high density electrode arrays. Although no spike sorting software is flawless, the package presented here, SpikeMAP, has been validated on PV interneurons, inspiring a degree of confidence. This is a good start, and further validation on other neuron types could increase that confidence. Groups doing in vitro experiments, where 4096 electrode arrays are more common, could find this system particularly helpful.

Comments on revised version:

I appreciate the dialogue that has occurred over this submission. I have seen how the authors have taken into account the issues that I have raised, as well as those brought up by reviewer 2. I am satisfied that the paper has improved and is now a novel and useful contribution in the area of spike sorting.

Reviewer #2 (Public review):

Summary:

In this paper, entitled "SpikeMAP: An unsupervised spike sorting pipeline for cortical excitatory and inhibitory 2 neurons in high-density multielectrode arrays with ground-truth validation", the authors are presenting spikeMAP, a pipeline for the analysis of large-scale recordings of in vitro cortical activity. According to the authors, spikeMAP not only allows for the detection of spikes produced by single neurons (spike sorting), but also allows for the reliable distinction between genetically determined cell types by utilizing viral and optogenetic strategies as ground-truth validation. While I find that the paper is nicely written, and easy to follow, I find that the algorithmic part of the paper is not really new and should have been more carefully compared to existing solutions. While the GT recordings to assess the possibilities of a spike sorting tool to distinguish properly between excitatory and inhibitory neurons is interesting, spikeMAP does not seem to bring anything new to state of the art solutions, and/or, at least, it would deserve to be properly benchmarked. This is why I would suggest the authors to perform a more intensive comparison with existing spike sorters.

Strengths:

The GT recordings with optogenetic activation of the cells, based on the opsins is interesting and might provide useful data to quantify how good spike sorting pipelines are, in vitro, to discriminate between excitatory and inhibitory neurons. Such an approach can be quite complementary with artificially generated ground truth.

Weaknesses:

The global workflow of spikeMAP, described in Figure 1, seems to be very similar to the one of [Hilgen et al, 2020, 10.1016/j.celrep.2017.02.038.]. Therefore, the first question is what is the rationale of reinventing the wheel, and not using tools that are doing something very similar (as mentioned by the authors themselves). I have a hard time, in general, believing that spikeMAP has something particularly special, given its Methods, compared to state-of-the-art spike sorters. This is why at the very least, the title of the paper is misleading, because it let the reader think that the core of the paper will be about a new spike sorting pipeline. If this is the main message the authors want to convey, then I think that numerous validations/benchmarks are missing to assess first how good spikeMAP is, w.r.t. spike sorting in general, before deciding if this is indeed the right tool to discriminate excitatory vs inhibitory cells. The GT validation, while interesting, is not enough to entirely validate the paper. The details are a bit too scarce to me, or would deserve to be better explained (see other comments after)

Regarding the putative location of the spikes, it has been shown that center of mass, while easy to compute, is not the most accurate solution [Scopin et al, 2024, 10.1016/j.jneumeth.2024.110297]. For example, it has an intrinsic bias for finding positions within the boundaries of the electrodes, while some other methods such as monopolar triangulation or grid-based convolution might have better performances. Can the authors comment on the choice of Center of Mass as a unique way to triangulate the sources?

Still in Figure 1, I am not sure to really see the point of Spline Interpolation. I see the point of such a smoothing, but the authors should demonstrate that it has a key impact on the distinction of Excitatory vs. Inhibitory cells. What's special with the value of 90kHz for a signal recorded at 18kHz? What is the gain with spline enhancement compared to without? Does such a value depend on the sampling rate, or is it a global optimum found by the authors?

Figure 2 is not really clear, especially panel B. The choice of the time scale for the B panel might not be the most appropriate, and the legend filtered/unfiltered with a dot is not clear to me in Bii. In panel E, the authors are making two clusters with PCA projections on single waveforms. Does this mean that the PCA is only applied to the main waveforms, i.e. the ones obtained where the amplitudes are peaking the most? This is not really clear from the methods, but if this is the case, then this approach is a bit simplistic and not really matching state-of-the-art solutions. Spike waveforms are quite often, especially with such high-density arrays, covering multiple channels at once and thus the extracellular patterns triggered by the single units on the MEA are spatio-temporal motifs occurring on several channels. This is why, in modern spike sorters, the information in a local neighbourhood is often kept to be projected, via PCA, on the lower dimensional space before clustering. Information on a single channel only might not be informative enough to disambiguate sources. Can the authors comment on that, and what is the exact spatial resolution of the 3Brain device? The way the authors are performing the SVD should be clarified in the methods section. Is it on a single channel, and/or on multiple channels in a local neighbourhood?

About the isolation of the single units, here again, I think the manuscript lacks some technical details. The authors are saying that they are using a k-means cluster analysis with k=2. This means that the authors are explicitly looking for 2 clusters per electrodes. If so, this is a really strong assumption that should not be held in the context of spike sorting, because since it is a blind source separation technique, one cannot pre-determine in advance how many sources are present in the vicinity of a given electrode. While the illustration on Figure 2E is ok, there is no guarantee that one cannot find more clusters, so why this choice of k=2? Again, this is why most modern spike sorting pipelines are not relying on k-means, to avoid any hard coded number of clusters. Can the authors comment on that?

I'm surprised by the linear decay of the maximal amplitude as a function of the distance from soma, as shown in Figure 2H. Is it really what should be expected? Based on the properties of the extracellular media, shouldn't we expect a power law for the decay of the amplitude? This is strange that up to 100um away from the some, the max amplitude only dropped from 260 to 240 uV. Can the authors comment on that? It would be interesting to plot that for all neurons recorded, in a normed manner V/max(V) as function of distances, to see what the curve looks like

In Figure 3A, it seems that the total number of cells is rather low for such a large number of electrodes. What are the quality criteria that are used to keep these cells? Did the authors exclude some cells from the analysis, and if yes, what are the quality criteria that are used to keep cells? If no criteria are used (because none is mentioned in the Methods), then how come so few cells are detected, and can the authors convince us that these neurons are indeed "clean" units (RPVs, SNRs, ...)

Still in Figure 3A, it looks like there is a bias to find inhibitory cells at the borders, since they do not appear to be uniformly distributed over the MEA. Can the authors comment on that? What would be the explanation for such a behaviour? It would be interesting to see some macroscopic quantities on Excitatory/Inhibitory cells, such as mean firing rates, averaged SNRs, ... Because again, in Figure 3C, it is not clear to me that the firing rates of inhibitory cells is higher than Excitatory ones, while it should be in theory.

For Figure 3 in general, I would have performed an exhaustive comparison of putative cells found by spikeMAP and other sorters. More precisely, I think that to prove the point that spikeMAP is indeed bringing something new to the field of spike sorting, the authors should have compared the performances of various spike sorters to discriminate Exc vs Inh cells based on their ground truth recordings. For example, either using Kilosort [Pachitariu et al, 2024, 10.1038/s41592-024-02232-7], or some other sorters that might be working with such large high-density data [Yger et al, 2018, 10.7554/eLife.34518]

Figure 4 has a big issue, and I guess the panels A and B should be redrawn. I don't understand what the red rectangle is displaying.

I understand that Figure 4 is only one example, but I have a hard time understanding from the manuscript how many slices/mice were used to obtain the GT data? I guess the manuscript could be enhanced by turning the data into an open access dataset, but then some clarification is needed. How many flashes/animals/slices are we talking about. Maybe this should be illustrated in Figure 4, if this figure is devoted to the introduction of the GT data.

While there is no doubt that GT data as the ones recorded here by the authors are the most interesting data from a validation point of view, the pretty low yield of such experiments should not discourage the use of artificially generated recordings such as the ones made in [Buccino et al, 2020, 10.1007/s12021-020-09467-7] or even recently in [Laquitaine et al, 2024, 10.1101/2024.12.04.626805v1]. In these papers, the authors have putative waveforms/firing rates patterns for excitatory and inhibitory cells, and thus the authors could test how good they are in discriminating the two subtypes

Comments on revised version:

While I must thank the authors for their answers, I still think that they miss an important one, and only partially answering some of my concerns.

I truly think that SpikeMAP would benefit with a comparison with a state-of-the-art spike sorting pipeline, for example Kilosort. The authors said that they made the sorter modular enough such that only the E/I classification step can be compared. I think this would be worth it, just to be sure that SpikeMAP spike sorting, which might be more simple than other recent solution (with template matching), is not missing some cells, and thus degrading the E/I classification performances. I know that such a comparison is not straightforward, because there is no clear ground truth, but I would still need to be convinced that the sorting pipelines is bringing something, on its own. While there is no doubt that the E/I classification layer can be interesting, especially given the recordings shared by the authors, I'm still a bit puzzled by the sorting step. Thus maybe either a Table, a figure, or even as Supplementary one. Or the authors could try to generate fake GT data with MEArec for example, with putative E/I cells (discriminated via waveforms and firing rates) and show on such (oversimplified) data that SpikeMAP is performing similarly to modern spike sorters. Otherwise, this is a bit hard to judge...

Author response:

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

Reviewer #1 (Public review)

As this code was developed for use with a 4096 electrode array, it is important to be aware of double-counting neurons across the many electrodes. I understand that there are ways within the code to ensure that this does not happen, but care must be taken in two key areas. Firstly, action potentials traveling down axons will exhibit a triphasic waveform that is different from the biphasic waveform that appears near the cell body, but these two signals will still be from the same neuron (for example, see Litke et al., 2004 "What does the eye tell the brain: Development of a System for the Large-Scale Recording of Retinal Output Activity"; figure 14). I did not see anything that would directly address this situation, so it might be something for you to consider in updated versions of the code.

Thank you for this comment. We have added a routine to the SpikeMAP to remove highly correlated spikes detected within a given spatial radius of each other. The following was added to the main text (line 149):

“As an additional verification step, SpikeMAP allows the computation of spike-count correlations between putative neurons located within a user-defined radius. Signals that exceed a defined threshold of correlation can be rejected as they likely reflect the same underlying cell.”

Secondly, spike shapes are known to change when firing rates are high, like in bursting neurons (Harris, K.D., Hirase, H., Leinekugel, X., Henze, D.A. & Buzsáki, G. Temporal interaction between single spikes and complex spike bursts in hippocampal pyramidal cells. Neuron 32, 141-149 (2001)). I did not see this addressed in the present version of the manuscript.

We have added a routine to SpikeMAP that computes population spike rates to verify stationarity over time. We have also added a routine to identify putative bursting neurons through a Hartigan statistical dip test applied to the inter-spike distribution of individual cells.

We added the following (line 204):

“Further, SpikeMAP contains a routine to perform a Hartigan statistical dip test on the inter-spike distribution of individual cells to detect putative bursting neurons.”

Another area for possible improvement would be to build on the excellent validation experiments you have already conducted with parvalbumin interneurons. Although it would take more work, similar experiments could be conducted for somatostatin and vasoactive intestinal peptide neurons against a background of excitatory neurons. These may have different spike profiles, but your success in distinguishing them can only be known if you validate against ground truth, like you did for the PV interneurons.

We have added the following (line 326):

“future work could include different inhibitory interneurons such as somatostatin (SOM) and vasoactive intestinal polypeptide (VIP) neurons to improve the classification of inhibitory cell types. Another avenue could involve applying SpikeMAP on artificially generated spike data (Buccino & Einevoll 2021; Laquitaine et al., 2024).”

Reviewer #2 (Public review)

Summary:

While I find that the paper is nicely written and easy to follow, I find that the algorithmic part of the paper is not really new and should have been more carefully compared to existing solutions. While the GT recordings to assess the possibilities of a spike sorting tool to distinguish properly between excitatory and inhibitory neurons are interesting, spikeMAP does not seem to bring anything new to state-of-the-art solutions, and/or, at least, it would deserve to be properly benchmarked. I would suggest that the authors perform a more intensive comparison with existing spike sorters.

Thank you for your insightful comment. A full comparison between SpikeMAP and related methods is provided in Table. 1. As can be seen, SpikeMAP is the only method listed that performs E/I sorting on large-scale multielectrodes. Nonetheless, several aspects of SpikeMAP included in the spike sorting pipeline do overlap with existing methods, as these constitute necessary steps prior to performing E/I identification. These steps are not novel to the current work, nor do they constitute rigid options that cannot be substituted by the user. Rather, we aim to offer SpikeMAP users the option to combine E/I identification with preliminary steps performed either through our software or through another package of their choosing. For instance, preliminary spike sorting could be done through Kilosort before importing the spike data into SpikeMAP for E/I identification. To allow greater flexibility, we have now modularized our suite so that E/I identification can be performed as a stand-alone module. We have clarified the text accordingly (line 317):

“While SpikeMAP is the only known method to enable the identification of putative excitatory and inhibitory neurons on high-density multielectrode arrays (Table 1), several aspects of SpikeMAP included in the spike sorting pipeline (Figure 1) overlap with existing methods, as these constitute required steps prior to performing E/I identification. To enable users the ability to integrate SpikeMAP with existing toolboxes, we provide a modularized suite of protocols so that E/I identification can be performed separately from preliminary spike sorting steps. In this way, a user could carry out spike sorting through Kilosort or another package before importing their data to SpikeMAP for E/I identification.”

Weaknesses:

(1) The global workflow of spikeMAP, described in Figure 1, seems to be very similar to that of Hilgen et al. 2020 (10.1016/j.celrep.2017.02.038). Therefore, the first question is what is the rationale of reinventing the wheel, and not using tools that are doing something very similar (as mentioned by the authors themselves). I have a hard time, in general, believing that spikeMAP has something particularly special, given its Methods, compared to state-of-the-art spike sorters.

The paper by Hilgen et al. is reported in Table 1. As seen, while this paper employs optogenetics, it does not target inhibitory (e.g., PV) cells. We have added the following clarification (line 82):

“Despite evidence showing differences in action potential kinetics for distinct cell-types as well as the use of optogenetics (Hilgen et al., 2017), there exists no large-scale validation efforts, to our knowledge, showing that extracellular waveforms can be used to reliably distinguish cell-types.”

This is why, at the very least, the title of the paper is misleading, because it lets the reader think that the core of the paper will be about a new spike sorting pipeline. If this is the main message the authors want to convey, then I think that numerous validations/benchmarks are missing to assess first how good spikeMAP is, with reference to spike sorting in general, before deciding if this is indeed the right tool to discriminate excitatory vs inhibitory cells. The GT validation, while interesting, is not enough to entirely validate the paper. The details are a bit too scarce for me, or would deserve to be better explained (see other comments after).

We thank the reviewer for this comment, and have amended the title as follows:

“SpikeMAP: An unsupervised pipeline for the identification of cortical excitatory and inhibitory neurons in high-density multielectrode arrays with ground-truth validation”

(2) Regarding the putative location of the spikes, it has been shown that the center of mass, while easy to compute, is not the most accurate solution [Scopin et al, 2024, 10.1016/j.jneumeth.2024.110297]. For example, it has an intrinsic bias for finding positions within the boundaries of the electrodes, while some other methods, such as monopolar triangulation or grid-based convolution,n might have better performances. Can the authors comment on the choice of the Center of Mass as a unique way to triangulate the sources?

We agree with the reviewer that the center-of-mass algorithm carries limitations that are addressed by other methods. To address this issue, we have included two additional protocols in SpikeMAP to perform monopolar triangulation and grid-based convolution, offering additional options for users of the package. The text has been clarified as follows (line 429):

“In addition to center-of-mass triangulation, SpikeMAP includes protocols to perform monopolar triangulation and grid-based convolution, offering additional options to estimate putative soma locations based on waveform amplitudes.”

(3) Still in Figure 1, I am not sure I really see the point of Spline Interpolation. I see the point of such a smoothing, but the authors should demonstrate that it has a key impact on the distinction of Excitatory vs. Inhibitory cells. What is special about the value of 90kHz for a signal recorded at 18kHz? What is the gain with spline enhancement compared to without? Does such a value depend on the sampling rate, or is it a global optimum found by the authors?

We clarified the text as follows (line 183):

“While we found that a resolution of 90 kHZ provided a reasonable estimate of spike waveforms, this value can be adjusted as a parameter in SpikeMAP.”

(4) Figure 2 is not really clear, especially panel B. The choice of the time scale for the B panel might not be the most appropriate, and the legend filtered/unfiltered with a dot is not clear to me in Bii.

We apologize for the rendering issues in the Figures that occurred during conversion into PDF format. We have now ensured that all figures are properly displayed.

In panel E, the authors are making two clusters with PCA projections on single waveforms. Does this mean that the PCA is only applied to the main waveforms, i.e. the ones obtained where the amplitudes are peaking the most? This is not really clear from the methods, but if this is the case, then this approach is a bit simplistic and does not really match state-of-the-art solutions. Spike waveforms are quite often, especially with such high-density arrays, covering multiple channels at once, and thus the extracellular patterns triggered by the single units on the MEA are spatio-temporal motifs occurring on several channels. This is why, in modern spike sorters, the information in a local neighbourhood is often kept to be projected, via PCA, on the lower-dimensional space before clustering. Information on a single channel only might not be informative enough to disambiguate sources. Can the authors comment on that, and what is the exact spatial resolution of the 3Brain device? The way the authors are performing the SVD should be clarified in the methods section. Is it on a single channel, and/or on multiple channels in a local neighbourhood?

We agree with the reviewer that it would be useful to have the option of performing PCA on several channels at once, since spikes can occur at several channels at the same time. We have now added a routine to SpikeMAP that allows users to define a radius around individual channels prior to performing PCA. The text was clarified as follows (line 131):

“The SpikeMAP suite also offers a routine to select a radius around individual channels in order to enter groups of adjacent channels in PCA.”

(5) About the isolation of the single units, here again, I think the manuscript lacks some technical details. The authors are saying that they are using a k-means cluster analysis with k=2. This means that the authors are explicitly looking for 2 clusters per electrode? If so, this is a really strong assumption that should not be held in the context of spike sorting, because, since it is a blind source separation technique, one can not pre-determine in advance how many sources are present in the vicinity of a given electrode. While the illustration in Figure 2E is ok, there is no guarantee that one can not find more clusters, so why this choice of k=2? Again, this is why most modern spike sorting pipelines do not rely on k-means, to avoid any hard-coded number of clusters. Can the authors comment on that?

We clarified the text as follows (line 135):

“In SpikeMAP, the optimal number of k-means clusters can be chosen by a Calinski-Harabasz criterion (Calinski and Harabasz, 1974) or pre-selected by the user.”

(6) I'm surprised by the linear decay of the maximal amplitude as a function of the distance from the soma, as shown in Figure 2H. Is it really what should be expected? Based on the properties of the extracellular media, shouldn't we expect a power law for the decay of the amplitude? This is strange that up to 100um away from the soma, the max amplitude only dropped from 260 to 240 uV. Can the authors comment on that? It would be interesting to plot that for all neurons recorded, in a normed manner V/max(V) as function of distances, to see what the curve looks like.

We added Supplemental Figure 1 showing the drop in voltage over all putative somas (N=1,950) of one recording, after excluding somas with an increase voltage away from electrode peak and computing normed values V/max(V). We see a distribution of slopes as well as intercepts across somas, showing some variability across recordings sites. As the reviewer suggests, it is possible that a power-law describes these data better than a linear function, and this would need to be investigated further by quantitatively comparing the fit of these functions.

(7) In Figure 3A, it seems that the total number of cells is rather low for such a large number of electrodes. What are the quality criteria that are used to keep these cells? Did the authors exclude some cells from the analysis, and if yes, what are the quality criteria that are used to keep cells? If no criteria are used (because none are mentioned in the Methods), then how come so few cells are detected, and can the authors convince us that these neurons are indeed "clean" units (RPVs, SNRs, ...)?

The reviewer is correct to point out that a number of stringent criteria were employed to exclude some putative cells. We now outline these criteria directly in the text (line 161):

“ At different steps in the process, conditions for rejecting spikes can be tailored by applying: (1) a stringent threshold to filtered voltages; (2) a minimal cut-off on the signal-to-noise ratio of voltages (see Supplemental Figure 2); (3) an LDA for cluster separability; (4) a minimal spike rate to putative neurons; (5) a Hartigan statistical dip test to detect spike bursting; (6) a decrease in voltage away from putative somas; and (7) a maximum spike-count correlation for nearby channels. Together, these criteria allow SpikeMAP users the ability to precisely control parameters relevant to automated spike sorting.”

Further, we provide SNRs of individual channels (Supplemental Figure 2), and added to the SpikeMAP software the ability to apply a minimal criterion based on SNR.

(8) Still in Figure 3A, it looks like there is a bias to find inhibitory cells at the borders, since they do not appear to be uniformly distributed over the MEA. Can the authors comment on that? What would be the explanation for such a behaviour? It would be interesting to see some macroscopic quantities on Excitatory/Inhibitory cells, such as mean firing rates, averaged SNRs... Because again, in Figure 3C, it is not clear to me that the firing rates of inhibitory cells are higher than Excitatory ones, whilst they should be in theory.

We have added figures showing the distribution of E and I firing rates across a population of N=1,950 putative cells (Supplemental Figure 3). Firing rates of inhibitory neurons are marginally higher than excitatory neurons, and both E and I follow an approximately exponential distribution of rates.

Reviewer may be right that there are more I neurons at borders in Fig.3B because injections were done in medial prefrontal cortex, so this may reflect an experimental artefact related to a high probability of activating I neurons in locations where the opsin was activated. We added a sentence to the text to clarify this point (line 201):

“It is possible that the spatial location of putative I cells reflects the site of injection of the opsin in medial prefrontal cortex.”

(9) For Figure 3 in general, I would have performed an exhaustive comparison of putative cells found by spikeMAP and other sorters. More precisely, I think that to prove the point that spikeMAP is indeed bringing something new to the field of spike sorting, the authors should have compared the performances of various spike sorters to discriminate Exc vs Inh cells based on their ground truth recordings. For example, either using Kilosort [Pachitariu et al, 2024, 10.1038/s41592-024-02232-7], or some other sorters that might be working with such large high-density data [Yger et al, 2018, 10.7554/eLife.34518].

The reviewer is correct to point out that our the spike-sorting portion of our pipeline shares similarities with related approaches. Other aspects, however, are unique to SpikeMAP. We have clarified the text accordingly:

“In sum, SpikeMAP provides an end-to-end pipeline to perform spike-sorting on high-density multielectrode arrays. Some elements of this pipeline are similar to related approaches (Table 1), including the use of voltage filtering, PCA, and k-means clustering. Other elements are novel, including the use of spline interpolation, LDA, and the ability to identify putative excitatory and inhibitory cells.”

(10) Figure 4 has a big issue, and I guess the panels A and B should be redrawn. I don't understand what the red rectangle is displaying.

Again, we apologize for the rendering issues in the Figures that occurred during conversion into PDF format. We have now ensured that all figures are properly displayed.

(11) I understand that Figure 4 is only one example, but I have a hard time understanding from the manuscript how many slices/mices were used to obtain the GT data? I guess the manuscript could be enhanced by turning the data into an open-access dataset, but then some clarification is needed. How many flashes/animals/slices are we talking about? Maybe this should be illustrated in Figure 4, if this figure is devoted to the introduction of the GT data.

Details of the open access data are now provided in Supplemental Table 1. We also clarified Figure 5B:

“Quantification of change in firing rate following optogenetic stimulation. Average firing rates are taken over four recordings obtained from 3 mice.”

(12) While there is no doubt that GT data as the ones recorded here by the authors are the most interesting data from a validation point of view, the pretty low yield of such experiments should not discourage the use of artificially generated recordings such as the ones made in [Buccino et al, 2020, 10.1007/s12021-020-09467-7] or even recently in [Laquitaine et al, 2024, 10.1101/2024.12.04.626805v1]. In these papers, the authors have putative waveforms/firing rate patterns for excitatory and inhibitory cells, and thus, the authors could test how good they are in discriminating the two subtypes.

We agree with the reviewer that it would be worthwhile for future work to apply SpikeMAP to artificially generated spike trains, and have added the following (line 328):

“Another avenue could involve applying SpikeMAP on artificially generated spike data (Buccino & Einevoll 2021; Laquitaine et al., 2024).”

Reviewer #1 (Recommendations for the authors):

(1) Line 154 seems to include a parenthetical expression left over from editing: "sensitive to noise (contamination? Better than noise?) generated by the signal of proximal units." See also line 186: "use (reliance?) of light-sensitive" and line 245: "In the absence of synaptic blockers (right?)," and line 270: "the size of the data prevents manual intervention (curation?)." Check carefully for all parentheses like that, which should be removed.

Thank you for pointing this out. We have revised the text and removed parenthetical expressions left over from editing.

(2) In lines 285-286, you state that: "k-mean clustering of spike waveform properties best differentiated the two principal classes of cells..." But I could not find where you compared k-means clustering to other methods. I think you just argued that k-means seemed to work well, but not better than, another method. If that is so, then you should probably rephrase those lines.

The reviewer is correct that direct comparisons are not performed here, hence we removed this sentence.

(3) Methods section, E/I classification, lines 396-405: You give us figures on what fraction was E and I (PV subtype) (94.75% and 5.25%), but there is more that you could have said. First of all, what is the expected fraction of parvalbumin-sensitive interneurons in the cortex - is it near 5%?

We clarified the text as follows (line 444): “This number is close to the expected percentage of PV interneurons in cortex (4-6%) (Markram et al. 2004).”

Second, how would these percentages change if you altered the threshold from 3 s.d. to something lower, like 2 s.d.? Giving us some idea of how the threshold affects the fraction of PV interneurons could give us an idea of whether this method agrees with our expectations or not.

While SpikeMAP offers the flexibility to set the voltage threshold manually, we opted for a stringent threshold to demonstrate the capabilities of the software. As seen in Figure 2D, at 2 and 3 s.d., the signal is largely accounted for by Gaussian noise, while deviation from noise arises around 4 s.d. We clarified the text as follows (line 120):

“At a threshold of -3 , the signal could be largely accounted for by Gaussian noise, while a separation between signal and noise began around a threshold of -4 ”

Third, did the inhibitory neurons identified by this optogenetic method also have narrow spike widths at half amplitude? Could you do a scatterplot of all the spike widths and inter-peak distances that had color-coded dots for E and I based on your optogenetic method?

We have added a scatterplot (Supplemental Figure 5).

(4) Can you compare your methods with others now widely in use, like, for example, Spiking Circus or Kilosort? You do that in Table 1 in terms of features, but not in terms of performance. For example, you could have applied Kilosort4 to your data from the 4096 electrode array and seen how often it sorted the same neurons that SpikeMAP did. I realize this could not give you a comparison of how many were E/I, but it could tell you how close your numbers of neurons agreed with their numbers. Were your numbers within 5% of each other? This would be helpful for groups who are already using Kilosort4.

As mentioned ealier, packages listed in Table 1 do not provide an identification of putative E/I neurons on high-density electrode arrays. To facilitation the integration of SpikeMAP with other spike sorting packages, our suite now provides a stand-alone module to perform E/I identification. This is now mentioned in the text (see earlier comment).

Reviewer #2 (Recommendations for the authors):

I would encourage the authors to decide what the paper is about: is it about a new sorting method (and if yes, more tests/benchmarks are needed to explain the pros and the cons of the pipelines, and the Methods need to be expanded). Or is it about the new data for Ground Truth validation, and again, if yes, then maybe explain more what they are, how many slices/mice/cells, ... Maybe also consider making the data available online as an open dataset.

We agree with the reviewer that the paper is best slated toward ground truth validation of E/I identification. We now specify how many slices/mice/cells etc. (see Supplemental Table 1) and make the data available online as open source.

eLife Assessment

This is a valuable computational study of odor responses in the early olfactory system of insects and vertebrates. The study addresses the question of how information about odor concentration is encoded by second-order neurons in the invertebrate and vertebrate olfactory system; it offers insights into the transformation of neural signals from receptors to second-order neurons. While reanalysis of published data presents solid evidence supporting compression of concentration information, incomplete analysis is provided to resolve how this observation could be reconciled with the need to preserve information about changes in stimulus intensity. This work will be of interest to neuroscientists studying sensory processing broadly and olfaction specifically.

Reviewer #1 (Public review):

Summary

This article is about the neural representation of odors in the early olfactory system of insects, fish, and rodents. Specifically, it regards the transformation that occurs between the olfactory sensory cells and the second-order neurons (projection neurons in insects, mitral/tufted cells in vertebrates). The central question is how the nervous system can encode both the identity of an odor and its concentration over many log units. The authors reanalyze data from experimental studies of odor responses in primary and secondary neurons, and test a range of computational models as to whether they match the observed transformation. They focus on two aspects of the second-order neuron response to odor concentration: the average activity across all neurons varies only a little with odor concentration, and different neurons have concentration-response curves with different shapes. They conclude that a model of divisive normalization can account for these effects, whereas two alternative models fail the test. A second observation is that tufted cells in the rodent system seem to undergo less normalization than mitral cells, and some reasons for this difference are proposed.

Strengths:

(1) The work compares different models for normalization, rather than simply reporting success with one.

(2) The analysis is applied to very diverse species, potentially revealing a common principle of olfactory processing.

Weaknesses:

(1) It is unclear that animals actually have a need to represent odor concentration over many log units in support of olfactory behaviors.

(2) The stimuli used in the chosen experiments, and the measure of neural response, are only weakly related to any ecological need, e.g., during odor tracking.

(3) Some of the comparisons between receptors and second-order neurons also compare across evolutionarily distant insect species that may not use the same coding principles.

(4) The analysis ignores the dynamics of odor responses, which figure prominently in previous answers to the question of identity/intensity coding.

(5) There is considerable prior consensus in the literature on the importance of normalization from primary to secondary neurons.

Elaboration of my comments:

(1) Motivation

The article starts from the premise that animals need to know the absolute concentration of an odor over many log units, but the need for this isn't obvious. The introduction cites an analogy to vision and audition. These are cases where we know for a fact that the absolute intensity of the stimulus is not relevant. Instead, sensory perception relies on processing small differences in intensity across space or time. And to maintain that sensitivity to small differences, the system discards the stimulus baseline. Humans are notoriously bad at judging the absolute light level. That information gets discarded even before light reaches the retina, namely through contraction of the pupil. Similarly, it seems plausible that a behavior like olfactory tracking relies on sensing small gradients across time (when weaving back and forth across the track) or space (across nostrils). It is important that the system function over many log units of concentration (e.g., far and close to a source) but not that it accurately represents what that current concentration is [see e.g., Wachowiak et al, 2025 Recalibrating Olfactory Neuroscience..].

Still, many experiments in olfactory research have delivered square pulses of odor at concentrations spanning many log units, rather than the sorts of stimuli an animal might encounter during tracking. Even within that framework, though, it doesn't seem mysterious anymore how odor identity and odor concentration are represented differently. For example, Stopfer et al 2003 showed that the population response of locust PNs traces a dynamic trajectory. Trajectories for a given odor form a manifold, within which trajectories for different concentrations are distinct by their excursions on the manifold. To see this, one must recognize that the PN responds to an odor pulse with a time-varying firing rate, that different PNs have different dynamics, and that the dynamics can change with concentration. This is also well recognized in the mammalian systems. Much has been written about the topic of dynamic coding of identity and intensity - see the reviews of Laurent (2002) and Uchida (2014).

(2) Conceptual

Given the above comments on the dynamics of odor responses in first- and second-order neurons, it seems insufficient to capture the response of a neuron with a single number. Even if one somehow had to use a single number, the mean firing rate during the odor pulse may not be the best choice. For example, the rodent mitral cells fire in rhythm with the animal's sniffing cycle, and certain odors will just shift the phase of the rhythm without changing the total number of spikes (see e.g., Fantana et al, 2008). During olfactory search or tracking, the sub-second movements of the animal in the odor landscape get superposed on the sniffing cycle. Given all this, it seems unlikely that the total number of spikes from a neuron in a 4-second period is going to be a relevant variable for neural processing downstream.

Much of the analysis focuses on the mean activity of the entire population. Why is this an interesting quantity? Apparently, the mean stays similar because some neurons increase and others decrease their firing rate. It would be more revealing, perhaps, to show the distribution of firing rates at different concentrations and see how that distribution is predicted by different models of normalization. This could provide a stronger test than just the mean.

The question "if concentration information is discarded in second-order neurons, which exclusively transmit odor information to the rest of the brain, how does the brain support olfactory behaviors, such as tracking and navigation?" is really not an open question anymore. For example, reference 23 reports in the abstract that "Odorant concentration had no systematic effect on spike counts, indicating that rate cannot encode intensity. Instead, odor intensity can be encoded by temporal features of the population response. We found a subpopulation of rapid, largely concentration-invariant responses was followed by another population of responses whose latencies systematically decreased at higher concentrations."

(3) Methods

It would be useful to state early in the manuscript what kinds of stimuli are being considered and how the response of a neuron is summarized by one number. There are many alternative ways to treat both stimuli and responses.

"The change in response across consecutive concentration levels may not be robust due to experimental noise and the somewhat limited range of concentrations sampled": Yes, a number of the curves just look like "no response". It would help the reader to show some examples of raw data, e.g. the time course of one neuron's firing rate to 4 concentrations, and for the authors to illustrate how they compress those responses into single numbers.

"We then calculated the angle between these two slopes for each neuron and plotted a polar histogram of these angles." The methods suggest that this angle is the arctan of the ratio of the two slopes in the response curve. A ratio of 2 would result from a slope change from 0.0001 to 0.0002 (i.e., virtually no change in slope) or from 1 to 2 (a huge change). Those are completely different response curves. Is it reasonable to lump them into the same bin of the polar plot? This seems an unusual way to illustrate the diversity of response curve shapes.

The Drosophila OSN data are passed through normalization models and then compared to locust PN data. This seems dangerous, as flies and locusts are separated by about 300 M years of evolution, and we don't know that fly PNs act like locust PNs. Their antennal lobe anatomy differs in many ways, as does the olfactory physiology. To draw any conclusions about a change in neural representation, it would be preferable to have OSN and PN data from the same species.

(4) Models of normalization

One conclusion is that divisive normalization could account for some of the change in responses from receptors to 2nd order neurons. This seems to be well appreciated already [e.g., Olsen 2010, Papadopoulou 2011, minireview in Hong & Wilson 2013].

Another claim is that subtractive normalization cannot perform that function. What model was used for subtractive normalization is unclear (there is an error in the Methods). It would be interesting if there were a categorical difference between divisive and subtractive normalization.

Looking closer at the divisive normalization model, it really has two components: (a) the "lateral inhibition" by which a neuron gets suppressed if other neurons fire (here scaled by the parameter k) , and (b) a nonlinear sigmoid transformation (determined by the parameters n and sigma). Both lateral inhibition and nonlinearity are known to contribute to decorrelation in a neural population (e.g., Pitkow 2012). The "intraglomerular gain control" contains only the nonlinearity. The "subtractive normalization" we don't know. But if one wanted to put divisive and subtractive inhibition on the same footing, one should add a sigmoid nonlinearity in both cases.

The response models could be made more realistic in other ways. For example, in both locusts and fish, the 2nd order neurons get inputs from multiple receptor types; presumably, that will affect their response functions. Also, lateral inhibition can take quite different forms. In locusts, the inhibitory neurons seem to collect from many glomeruli. But in rats, the inhibition by short axon cells may originate from just a few sparse glomeruli, and those might be different for every mitral cell (Fantana 2008).

(5) Tufted cells

There are questions raised by the following statements: "traded-off energy for faster and finer concentration discrimination" and "an additional type of second-order neuron (tufted cells) that has evolved in land vertebrates and that outperforms mitral cells in concentration encoding" and later "These results suggest a trade-off between concentration decoding and normalization processes, which prevent saturation and reduce energy consumption.". Are the tufted cells inferior to the mitral cells in any respect? Do they suffer from saturation at high concentration? And do they then fail in their postulated role for odor tracking? If not, then what was the evolutionary driver for normalization in the mitral cell pathway? Certainly not lower energy consumption (50,000 mitral cells = 1% of rod photoreceptors, each of which consumes way more energy than a mitral cell).

Reviewer #2 (Public review):

Summary:

The main goal of this study is to examine how information about odor concentration is encoded by second-order neurons in the invertebrate and vertebrate olfactory system. In many animal models, the overall mean firing rates across the second-order neurons appear to be relatively flat or near constant with increasing odor intensity. While such compression of concentration information could aid in achieving concentration invariant recognition of odor identity, how this observation could be reconciled with the need to preserve information about the changes in stimulus intensity is a major focus of the study. The authors show that second-order neurons have 'diverse' dose-response curves and that the combinations of neurons activated (particularly the rank-order) differ with concentration. Further, they argue that a single circuit-level computation, termed 'divisive normalization,' where the individual neural response is normalized by the total activity across all neurons, could help explain the coding properties of neurons at this stage of processing in all model organisms examined. They present approaches to read out the concentration information using spike rates or timing-based approaches. Finally, the authors reveal that tufted cells in the mouse olfactory bulb provide an exception to this coding approach and encode concentration information with a monotonic increase in firing rates.

Strengths:

(1) Comparative analysis of odor intensity coding across four different species, revealing the common features in encoding stimulus-driven features, is highly valuable.

(2) Showing how mitral and tufted cells differ in encoding odor intensity is potentially very important to the field.

(3) How to preserve concentration information while compressing the same with divisive normalization is also a novel and important problem in the field of sensory coding.

Weaknesses:

(1) The encoding problem:

The main premise that divisive normalization generates this diversity of dose-response curves in the second-order neurons is a little problematic. The authors acknowledge this as part of their analysis in Figure 3.

"Therefore, divisive normalization mostly does not alter the relative contribution (rank order) of each neuron in the ensemble." (Page 4, last paragraph, lines 6-8).

The analysis in this figure indicates that divisive normalization does what it is supposed to do, i.e., compresses concentration information and not alter the rank-order of neurons or the combinatorial patterns. Changes in the combinations of neurons activated with intensity arise directly from the fact that the first-order neurons did not have monotonic responses with odor intensity (i.e., crossovers). This was the necessary condition, and not the divisive normalization for changes in the combinatorial code.

There seems to be a confusion/urge to attribute all coding properties found in the second-order neurons to 'divisive normalization.' If the input from sensory neurons is monotonic (i.e., no crossovers), then divisive normalization did not change the rank order, and the same combinations of neurons are activated in a similar fashion (same vector direction or combinatorial profile) to encode for different odor intensities. Concentration invariance is achieved, and concentration information is lost. However, when the first-order neurons are non-monotonic (i.e., with crossovers), that causes the second-order neurons to have different rank orders with different concentrations. Divisive normalization compresses information about concentrations, and rank-order differences preserve information about the odor concentration. Does this not mean that the non-monotonicity of sensory neuron response is vital for robustly maintaining information about odor concentration?

Naturally, the question that arises is whether many of the important features of the second-order neuron's response simply seem to follow the input. Or is my understanding of the figures and the write-up flawed, and are there more ways in which divisive normalization contributes to reshaping the second-order neural response? This must be clarified.

Lastly, the tufted cells in the mouse OB are also driven by this sensory input with crossovers. How does the OB circuit convert the input with crossovers into one that is monotonic with concentration? I think that is an important question that this computational effort could clarify.

(2) The decoding problem.

The way the decoding results and analysis are presented does not add a lot of information to what has already been presented. For example, based on the differences in rank-order with concentration, I would expect the combinatorial code to be different. Hence, a very simple classifier based on cosine or correlation distance would work well. However, since divisive normalization (DN) is applied, I would expect a simple classification scheme that uses the Euclidean distance metric to work equally as well after DN. Is this the case?<br /> Leave-one-trial/sample-out seems too conservative. How robust are the combinatorial patterns across trials? Would just one or two training trials suffice for creating templates for robust classification? Based on my prior experience (https://elifesciences.org/reviewed-preprints/89330), I do expect that the combinatorial patterns would be more robust to adaptation and hence also allow robust recognition of odor intensity across repeated encounters.

Lastly, in the simulated data, since the affinity of the first-order sensory neurons to odorants is expected to be constant across concentration, and "Jaccard similarity between the sets of highest-affinity neurons for each pair of concentration levels was > 0.96," why would the rank-order change across concentration? DN should not alter the rank order.

If the set of early responders does change, how will the decoder need to change, and what precise predictions can be made that can be tested experimentally? The lack of exploration of this aspect of the results seems like a missed opportunity.

(3) Analysis of existing data.

I had a couple of issues related to the presentation and analysis of prior results.

i) Based on the methods, for Figures 1 and 2, it appears the responses across time, trials, and odorants were averaged to get a single data point per neuron for each concentration. Would this averaging not severely dilute trends in the data? The one that particularly concerns me is the averaging across different odorants. If you do odor-by-odor analysis, is the flattening of second-order neural responses still observable? Because some odorants activate more globally and some locally, I would expect a wide variety of dose-response relationships that vary with odor identity (more compressed in second-order neurons, of course). It would be good to show some representative neural responses and show how the extracted values for each neuron are a faithful/good representation of its response variation across intensities.

ii) A lot of neurons seem to have responses that flat line closer to zero (both firing rate and dF/F in Figure 1). Are these responsive neurons? The mean dF/F also seems to hover not significantly above zero. Hence, I was wondering if the number of neurons is reducing the trend in the data significantly.

iii) I did not fully understand the need to show the increase in the odor response across concentrations as a polar plot. I see potential issues with the same. For example, the following dose-response trend at four intensities (C4 being the highest concentration and C1 the lowest): response at C3 > response at C1 and response at C4 > response at C2. But response at C3 < response at C2. Hence, it will be in the top right segment of the polar plot. However, the responses are not monotonic with concentrations. So, I am not convinced that the polar plot is the right way to characterize the dose-response curves. Just my 2 cents.

(4) Simulated vs. Actual data.

In many analyses, simulated data were used (Figures 3 and 4). However, there is no comparison of how well the simulated data fit the experimental data. For example, the Simulated 1st order neuron in Figure 3D does not show a change in rank-order for the first-order neuron. In Figure 3E, temporal response patterns in second-order neurons look unrealistic. Some objective comparison of simulated and experimental data would help bolster confidence in these results.

Reviewer #3 (Public review):

Summary:

In their study, Shen et al. examine how first- and second-order neurons of early olfactory circuits among invertebrates and vertebrates alike respond to and encode odor identity and concentration. Previously published electrophysiological and imaging data are re-analyzed and complemented with computational simulations. The authors explore multiple potential circuit computations by which odor concentration-dependent increases in first-order neuron responses transform into concentration-invariant responses on average across the second-order neuron population, and report that divisive normalization exceeds subtractive normalization and intraglomerular gain control in accounting for this transformation. The authors then explore how either rate- or timing-based schemes in third-order neurons may decode odor identity and concentration information from such concentration-invariant mean responses across the second-order neuron population. Finally, the results of their study of second-order neurons (invertebrate projection neurons and vertebrate mitral cells) are contrasted with the concentration-variant responses of second-order projection tufted cells in mammals. Overall, through a combination of neural data re-analysis, computational simulation, and conceptual theory, this study provides important new understanding of how aspects of sensory information are encoded through the actions of distinct components of early olfactory circuits.

Strengths:

Consideration of multiple evolutionarily disparate olfactory circuits, as well as re-analysis of previously published neural data sets combined with novel simulations guided by those sets, lends considerable robustness to some key findings of this study. In particular, the finding that divisive normalization - with direct inspiration from established circuit components in the form of glomerular layer short-axon cells - accounts more thoroughly for the average concentration invariance of second-order olfactory neurons at a population level than other forms of normalization is compelling. Likewise, demonstration of the required 'crossover' of first-order neuron concentration sensitivity for divisive normalization to achieve such flattening of concentration variance across the second-order population is notable, with simulations providing important insight into experimentally observed patterns of first-order neuron responses. Limited clarity in other aspects of the study, in particular related to the consideration of neural response latencies and enumerated below, temper the overall strength of the study.

Weaknesses:

(1) While the authors focus on concentration-dependent increases in first-order neuron activity, reflecting the majority of observed responses, recent work from the Imai group shows that odorants can also lead to direct first-order neuron inhibition (i.e., reduction in spontaneous activity), and within this subset, increasing odorant concentration tends to increase the degree of inhibition. Some discussion of these findings and how they may complement divisive normalization to contribute to the diverse second-order neuron concentration-dependence would be of interest and help expand the context of the current results.

(2) Related to the above point, odorant-evoked inhibition of second-order neurons is widespread in mammalian mitral cells and significantly contributes to the flattened concentration-dependence of mitral cells at the population level. Such responses are clearly seen in Figure 1D. Some discussion of how odorant-evoked mitral cell inhibition may complement divisive normalization, and likewise relate to comparatively lower levels of odorant-evoked inhibition among tufted cells, would further expand the context of the current results. Toward this end, replication of analyses in Figures 1D and E following exclusion of mitral cell inhibitory responses would provide insight into the contribution of such inhibition to the flattening of the mitral cell population concentration dependence.

(3) The idea of concentration-dependent crossover responses across the first-order population being required for divisive normalization to generate individually diverse concentration response functions across the second-order population is notable. The intuition of the crossover responses is that first-order neurons that respond most sensitively to any particular odorant (i.e., at the lowest concentration) respond with overall lower activity at higher concentrations than other first-order neurons less sensitively tuned to the odorant. Whether this is a consistent, generalizable property of odorant binding and first-order neuron responsiveness is not addressed by the authors, however. Biologically, one mechanism that may support such crossover events is intraglomerular presynaptic/feedback inhibition, which would be expected to increase with increasing first-order neuron activation such that the most-sensitively responding first-order neurons would also recruit the strongest inhibition as concentration increases, enabling other first-order neurons to begin to respond more strongly. Discussion of this and/or other biological mechanisms (e.g., first-order neuron depolarization block) supporting such crossover responses would strengthen these results.

(4) It is unclear to what degree the latency analysis considered in Figures 4D-H works with the overall framework of divisive normalization, which in Figure 3 we see depends on first-order neuron crossover in concentration response functions. Figure 4D suggests that all first-order neurons respond with the same response amplitude (R in eq. 3), even though this is supposed to be pulled from a distribution. It's possible that Figure 4D is plotting normalized response functions to highlight the difference in latency, but this is not clear from the plot or caption. If response amplitudes are all the same, and the response curves are, as plotted in Figure 4D, identical except for their time to half-max, then it seems somewhat trivial that the resulting second-order neuron activation will follow the same latency ranking, regardless of whether divisive normalization exists or not. However, there is some small jitter in these rankings across concentrations (Figure 4G), suggesting there is some randomness to the simulations. It would be helpful if this were clarified (e.g., by showing a non-normalized Figure 4D, with different response amplitudes), and more broadly, it would be extremely helpful in evaluating the latency coding within the broader framework proposed if the authors clarified whether the simulated first-order neuron response timecourses, when factoring in potentially different amplitudes (R) and averaging across the entire response window, reproduces the concentration response crossovers observed experimentally. In summary, in the present manuscript, it remains unclear if concentration crossovers are captured in the latency simulations, and if not, the authors do not clearly address what impact such variation in response amplitudes across concentrations may have on the latency results. It is further unclear to what degree divisive normalization is necessary for the second-order neurons to establish and maintain their latency ranks across concentrations, or to exhibit concentration-dependent changes in latency.

(5) How the authors get from Figure 4G to 4H is not clear. Figure 4G shows second-order neuron response latencies across all latencies, with ordering based on their sorted latency to low concentration. This shows that very few neurons appear to change latency ranks going from low to high concentration, with a change in rank appearing as any deviation in a monotonically increasing trend. Focusing on the high concentration points, there appear to be 2 latency ranks switched in the first 10 responding neurons (reflecting the 1 downward dip in the points around neuron 8), rather than the 7 stated in the text. Across the first 50 responding neurons, I see only ~14 potential switches (reflecting the ~7 downward dips in the points around neurons 8, 20, 32, 33, 41, 44, 50), rather than the 32 stated in the text. It is possible that the unaccounted rank changes reflect fairly minute differences in latencies that are not visible in the plot in Figure 4G. This may be clarified by plotting each neuron's latency at low concentration vs. high concentration (i.e., similar to Figure 4H, but plotting absolute latency, not latency rank) to allow assessment of the absolute changes. If such minute differences are not driving latency rank changes in Fig. 4G, then a trend much closer to the unity line would be expected in Figure 4H. Instead, however, there are many massive deviations from unity, even within the first 50 responding neurons plotted in Figure 4G. These deviations include a jump in latency rank from 2 at low concentration to ~48 at high concentration. Such a jump is simply not seen in Figure 4G.

(6) In the text, the authors state that "Odor identity can be encoded by the set of highest-affinity neurons (which remains invariant across concentrations)." Presumably, this is a restatement of the primacy model and refers to invariance in latency rank (since the authors have not shown that the highest-affinity neurons have invariant response amplitudes across concentration). To what degree this statement holds given the results in Figure 4H, however, which appear to show that some neurons with the earliest latency rank at low concentration jump to much later latency ranks at high concentration, remains unclear. Such changes in latency rank for only a few of the first responding neurons may be negligible for classifying odor identity among a small handful of odorants, but not among 1-2 orders of magnitude more odors, which may feasibly occur in a natural setting. Collectively, these issues with the execution and presentation of the latency analysis make it unclear how robust the latency results are.

(7) Analysis in Figures 4A-C shows that concentration can be decoded from first-order neurons, second-order neurons, or first-order neurons with divisive normalization imposed (i.e., simulating second-order responses). This does not say that divisive normalization is necessary to encode concentration, however. Therefore, for the authors to say that divisive normalization is "a potential mechanism for generating odor-specific subsets of second-order neurons whose combinatorial activity or whose response latencies represent concentration information" seems too strong a conclusion. Divisive normalization is not generating the concentration information, since that can be decoded just as well from the first-order neurons. Rather, divisive normalization can account for the different population patterns in concentration response functions between first- and second-order neurons without discarding concentration-dependent information.

(8) Performing the same polar histogram analysis of tufted vs. mitral cell concentration response functions (Figure 5B) provides a compelling new visualization of how these two cell types differ in their concentration variance. The projected importance of tufted cells to navigation, emerging directly through the inverse relationship between average concentration and distance (Figure 5C), is not surprising, and is largely a conceptual analysis rather than new quantitative analysis per se, but nevertheless, this is an important point to make. Another important consideration absent from this section, however, is whether and how divisive normalization may impact tufted cell activity. Previous work from the authors, as well as from Schoppa, Shipley, and Westbrook labs, has compellingly demonstrated that a major circuit mediating divisive normalization of mitral cells (GABA/DAergic short-axon cells) directly targets external tufted cells, and is thus very likely to also influence projection tufted cells. Such analysis would additionally provide substantially more justification for the Discussion statement "we analyzed an additional type of second-order neuron (tufted cells)", which at present instead reflects fairly minimal analysis.

Author response:

(1) Explore the temporal component of neural responses (instead of collapsing responses to a single number, i.e., the average response over 4s), and determine which of the three models can recapitulate the observed dynamics.

(2) Expand the polar plot visualization to show all three slopes (changes in responses across all three successive concentrations) instead of only two slopes.

(3) Attempt to collect and analyze, from published papers, data of: (a) first-order neuron responses to odors to determine the role of first-order inhibition towards generating non-monotonic responses, and (b) PN responses in Drosophila to properly compare with corresponding first-order neuron responses.

(4) Further discuss: (a) why the brain may need to encode absolute concentration, (b) the distinction between non-monotonic responses and cross-over responses, and (c) potential limitations of the primacy model.

(5) Expand the divisive normalization model by evaluating different values of k and R, and study the effects of divisive normalization on tufted cells.

(6) Add discussion of other potential inhibitory mechanisms that could contribute towards the observed effects.

Reviewer #1:

The article starts from the premise that animals need to know the absolute concentration of an odor over many log units, but the need for this isn't obvious. The introduction cites an analogy to vision and audition. These are cases where we know for a fact that the absolute intensity of the stimulus is not relevant. Instead, sensory perception relies on processing small differences in intensity across space or time. And to maintain that sensitivity to small differences, the system discards the stimulus baseline. Humans are notoriously bad at judging the absolute light level. That information gets discarded even before light reaches the retina, namely through contraction of the pupil. Similarly, it seems plausible that a behavior like olfactory tracking relies on sensing small gradients across time (when weaving back and forth across the track) or space (across nostrils). It is important that the system function over many log units of concentration (e.g., far and close to a source) but not that it accurately represents what that current concentration is [see e.g., Wachowiak et al, 2025 Recalibrating Olfactory Neuroscience..].

We thank the Reviewer for the insightful input and agree that gradients across time and space are important for various olfactory behaviors, such as tracking. At the same time, we think that absolute concentration is also needed for two reasons. First, in order to extract changes in concentration, the absolute concentration needs to be normalized out; i.e., change needs to be encoded with respect to some baseline, which is what divisive normalization computes. Second, while it is true that representing the exact number of odor molecules present is not important, this number directly relates to distance from the odor source, which does provide ethological value (e.g., is the tiger 100m or 1000m away?). Indeed, our decoding experiments focused on discriminating relative, and not on absolute, concentrations by classifying between each pair of concentrations (i.e., relative distances), which is effectively an assessment of the gradient. In our revision, we will make all of these points clearer.

Still, many experiments in olfactory research have delivered square pulses of odor at concentrations spanning many log units, rather than the sorts of stimuli an animal might encounter during tracking. Even within that framework, though, it doesn't seem mysterious anymore how odor identity and odor concentration are represented differently. For example, Stopfer et al 2003 showed that the population response of locust PNs traces a dynamic trajectory. Trajectories for a given odor form a manifold, within which trajectories for different concentrations are distinct by their excursions on the manifold. To see this, one must recognize that the PN responds to an odor pulse with a time-varying firing rate, that different PNs have different dynamics, and that the dynamics can change with concentration. This is also well recognized in the mammalian systems. Much has been written about the topic of dynamic coding of identity and intensity - see the reviews of Laurent (2002) and Uchida (2014).

Given the above comments on the dynamics of odor responses in first- and second-order neurons, it seems insufficient to capture the response of a neuron with a single number. Even if one somehow had to use a single number, the mean firing rate during the odor pulse may not be the best choice. For example, the rodent mitral cells fire in rhythm with the animal's sniffing cycle, and certain odors will just shift the phase of the rhythm without changing the total number of spikes (see e.g., Fantana et al, 2008). During olfactory search or tracking, the sub-second movements of the animal in the odor landscape get superposed on the sniffing cycle. Given all this, it seems unlikely that the total number of spikes from a neuron in a 4-second period is going to be a relevant variable for neural processing downstream.

To our knowledge, it is not well understood how downstream brain regions read out mitral cell responses to guide olfactory behavior. The olfactory bulb projects to more than a dozen brain regions, and different regions could decode signals in different ways. We focused on the mean response because it is a simple, natural construct.

The datasets we analyzed may not include all relevant timing information; for example, the mouse data is from calcium imaging studies that did not track sniff timing. Nonetheless, we plan to address this comment within our framework by binning time into smaller-sized windows (e.g., 0-0.2s, 0.2-0.4s, etc.) and repeating our analysis for each of these windows. Specifically, we will determine how each normalization method fares in recapitulating statistics of the population responses of each window, beyond simply assessing the population mean.

Much of the analysis focuses on the mean activity of the entire population. Why is this an interesting quantity? Apparently, the mean stays similar because some neurons increase and others decrease their firing rate. It would be more revealing, perhaps, to show the distribution of firing rates at different concentrations and see how that distribution is predicted by different models of normalization. This could provide a stronger test than just the mean.

We agree that mean activity is only one measure to summarize a rich data set and will perform the suggested analysis.

The question "if concentration information is discarded in second-order neurons, which exclusively transmit odor information to the rest of the brain, how does the brain support olfactory behaviors, such as tracking and navigation?" is really not an open question anymore. For example, reference 23 reports in the abstract that "Odorant concentration had no systematic effect on spike counts, indicating that rate cannot encode intensity. Instead, odor intensity can be encoded by temporal features of the population response. We found a subpopulation of rapid, largely concentration-invariant responses was followed by another population of responses whose latencies systematically decreased at higher concentrations."

Primacy coding does provide one plausible mechanism to decode concentration. Our manuscript demonstrated how such a code could emerge in second-order neurons with the help of divisive normalization, though it does require maintaining at least partial rank invariance across concentrations, which may not be robust. We also showed how concentration could be decoded via spike rates, even if average rates are constant, which provides an alternative hypothesis to that of ref 23.

Further, ref 23 only considers the piriform cortex, which, as mentioned above, is one of many targets of the olfactory bulb, and it remains unclear what the decoding mechanisms are of each of these targets. In addition, work from the same authors of ref 23 found multiple potential decoding strategies in the piriform cortex itself, including changes in firing rate (see Fig. 2E of ref. 23 - Bolding & Franks, 2017; as well as Fig. 4 in Roland et al., 2017).

It would be useful to state early in the manuscript what kinds of stimuli are being considered and how the response of a neuron is summarized by one number. There are many alternative ways to treat both stimuli and responses.

We will add this explanation to the manuscript.

"The change in response across consecutive concentration levels may not be robust due to experimental noise and the somewhat limited range of concentrations sampled": Yes, a number of the curves just look like "no response". It would help the reader to show some examples of raw data, e.g. the time course of one neuron's firing rate to 4 concentrations, and for the authors to illustrate how they compress those responses into single numbers.

We agree and will add this information to the manuscript.

"We then calculated the angle between these two slopes for each neuron and plotted a polar histogram of these angles." The methods suggest that this angle is the arctan of the ratio of the two slopes in the response curve. A ratio of 2 would result from a slope change from 0.0001 to 0.0002 (i.e., virtually no change in slope) or from 1 to 2 (a huge change). Those are completely different response curves. Is it reasonable to lump them into the same bin of the polar plot? This seems an unusual way to illustrate the diversity of response curve shapes.

We agree that the two changes in the reviewer’s example will be categorized in the same quadrant in our analysis. We did not focus on the absolute changes because our analysis covers many log ratios of concentrations. Instead, we focused on the relative shapes of the concentration response curves, and more specifically, the direction of the change (i.e., the sign of the slope). We will better motivate this style of analysis in the revision. Moreover, in response to comments by Reviewer 2, we will compare response shapes between all three successive levels of concentration changes, as opposed to only two levels.

The Drosophila OSN data are passed through normalization models and then compared to locust PN data. This seems dangerous, as flies and locusts are separated by about 300 M years of evolution, and we don't know that fly PNs act like locust PNs. Their antennal lobe anatomy differs in many ways, as does the olfactory physiology. To draw any conclusions about a change in neural representation, it would be preferable to have OSN and PN data from the same species.

We are in the process of requesting PN response data in Drosophila from groups that have collected such data and will repeat the analysis once we get access to the data.

One conclusion is that divisive normalization could account for some of the change in responses from receptors to 2nd order neurons. This seems to be well appreciated already [e.g., Olsen 2010, Papadopoulou 2011, minireview in Hong & Wilson 2013].

While we agree that these manuscripts do study the effects of divisive normalization in insects and fish, here we show that this computation also generalizes to rodents. In addition, these previous studies do not focus on divisive normalization’s role towards concentration encoding/decoding, which is our focus. We will clarify this difference in the revision.

Another claim is that subtractive normalization cannot perform that function. What model was used for subtractive normalization is unclear (there is an error in the Methods). It would be interesting if there were a categorical difference between divisive and subtractive normalization.

We apologize for the mistake in the subtractive normalization equation and will correct it. Thank you for catching it.

Looking closer at the divisive normalization model, it really has two components: (a) the "lateral inhibition" by which a neuron gets suppressed if other neurons fire (here scaled by the parameter k) , and (b) a nonlinear sigmoid transformation (determined by the parameters n and sigma). Both lateral inhibition and nonlinearity are known to contribute to decorrelation in a neural population (e.g., Pitkow 2012). The "intraglomerular gain control" contains only the nonlinearity. The "subtractive normalization" we don't know. But if one wanted to put divisive and subtractive inhibition on the same footing, one should add a sigmoid nonlinearity in both cases.

Our intent was not to place all the methods on the “same footing” but rather to isolate the two primary components of normalization methods – non-linearity and lateral inhibition – and determine which of these, and in which combination, could generate the desired effects. Divisive normalization incorporates both components, whereas intraglomerular gain control and subtractive normalization only incorporate one of these components. We will clarify this reasoning in the revision.

The response models could be made more realistic in other ways. For example, in both locusts and fish, the 2nd order neurons get inputs from multiple receptor types; presumably, that will affect their response functions. Also, lateral inhibition can take quite different forms. In locusts, the inhibitory neurons seem to collect from many glomeruli. But in rats, the inhibition by short axon cells may originate from just a few sparse glomeruli, and those might be different for every mitral cell (Fantana 2008).

We thank the Reviewer for the input. Instead of fixing k for all second-order neurons, we will apply different k values for different neurons. We will also systematically vary the percentage of neurons used for the divisive normalization calculation in the denominator, and determine the regime under which the effects experimentally observed are reproducible. This approach takes into account the scenario that inter-glomerular inhibitory interactions are sparse.

There are questions raised by the following statements: "traded-off energy for faster and finer concentration discrimination" and "an additional type of second-order neuron (tufted cells) that has evolved in land vertebrates and that outperforms mitral cells in concentration encoding" and later "These results suggest a trade-off between concentration decoding and normalization processes, which prevent saturation and reduce energy consumption.". Are the tufted cells inferior to the mitral cells in any respect? Do they suffer from saturation at high concentration? And do they then fail in their postulated role for odor tracking? If not, then what was the evolutionary driver for normalization in the mitral cell pathway? Certainly not lower energy consumption (50,000 mitral cells = 1% of rod photoreceptors, each of which consumes way more energy than a mitral cell).

The question of what mitral cells are “good for”, compared to tufted cells, remains unclear in our view. We speculate that mitral cells provide superior context-dependent processing and are better for determining stimuli-reward contingencies, but this remains far from settled experimentally.

We believe the mitral cell pathway evolved earlier than tufted cells, since the former appear akin to projection neurons in insects. Nonetheless, we agree that differences in energy consumption are unlikely to be the primary distinguishing factor, and in the revision, we will drop this argument.

Reviewer #2:

The main premise that divisive normalization generates this diversity of dose-response curves in the second-order neurons is a little problematic. … The analysis in [Figure 3] indicates that divisive normalization does what it is supposed to do, i.e., compresses concentration information and not alter the rank-order of neurons or the combinatorial patterns. Changes in the combinations of neurons activated with intensity arise directly from the fact that the first-order neurons did not have monotonic responses with odor intensity (i.e., crossovers). This was the necessary condition, and not the divisive normalization for changes in the combinatorial code. There seems to be a confusion/urge to attribute all coding properties found in the second-order neurons to 'divisive normalization.' If the input from sensory neurons is monotonic (i.e., no crossovers), then divisive normalization did not change the rank order, and the same combinations of neurons are activated in a similar fashion (same vector direction or combinatorial profile) to encode for different odor intensities. Concentration invariance is achieved, and concentration information is lost. However, when the first-order neurons are non-monotonic (i.e., with crossovers), that causes the second-order neurons to have different rank orders with different concentrations. Divisive normalization compresses information about concentrations, and rank-order differences preserve information about the odor concentration. Does this not mean that the non-monotonicity of sensory neuron response is vital for robustly maintaining information about odor concentration? Naturally, the question that arises is whether many of the important features of the second-order neuron's response simply seem to follow the input. Or is my understanding of the figures and the write-up flawed, and are there more ways in which divisive normalization contributes to reshaping the second-order neural response? This must be clarified. Lastly, the tufted cells in the mouse OB are also driven by this sensory input with crossovers. How does the OB circuit convert the input with crossovers into one that is monotonic with concentration? I think that is an important question that this computational effort could clarify.

It appears that there is confusion about the definitions of “non-monotonicity” and “crossovers”.  These are two independent concepts – one does not necessarily lead to the other. Non-monotonicity concerns the response of a single neuron to different concentration levels. A neuron’s response is considered non-monotonic if its response goes up then down, or down then up, across increasing concentrations. A “cross-over” is defined based on the responses of multiple neurons. A cross-over occurs when the response of one neuron is lower than another neuron at one concentration, but higher than the other at a different concentration. For example, the responses of both neurons could increase monotonically with increasing concentration, but one neuron might start lower and grow faster, hence creating a cross-over. We will clarify this in the manuscript, which we believe will resolve the questions raised above.

The way the decoding results and analysis are presented does not add a lot of information to what has already been presented. For example, based on the differences in rank-order with concentration, I would expect the combinatorial code to be different. Hence, a very simple classifier based on cosine or correlation distance would work well. However, since divisive normalization (DN) is applied, I would expect a simple classification scheme that uses the Euclidean distance metric to work equally as well after DN. Is this the case?

Yes, we used a simple classification scheme, logistic regression with a linear kernel, which is essentially a Euclidean distance-based classification. This scheme works better for tufted cells because they are more monotonic; i.e., if neuron A and B both increase their responsiveness with concentration, then Euclidean distance would be fine. But if neuron A’s response amplitude goes up and neuron B’s response goes down – as often happens for mitral cells – then Euclidean distance does not work as well. We will add intuition about this in the manuscript.

Leave-one-trial/sample-out seems too conservative. How robust are the combinatorial patterns across trials? Would just one or two training trials suffice for creating templates for robust classification? Based on my prior experience (https://elifesciences.org/reviewed-preprints/89330https://elifesciences.org/reviewed-preprints/89330), I do expect that the combinatorial patterns would be more robust to adaptation and hence also allow robust recognition of odor intensity across repeated encounters.

As suggested, we will compute the correlation coefficient of the similarity of neural responses for each odor (across trials). We will repeat this analysis for both mitral and tufted cells. To determine the effect of adaptation, we will compute correlation coefficients of responses between the 1st and 2nd trials vs the 1st and final trial.

Lastly, in the simulated data, since the affinity of the first-order sensory neurons to odorants is expected to be constant across concentration, and "Jaccard similarity between the sets of highest-affinity neurons for each pair of concentration levels was > 0.96," why would the rank-order change across concentration? DN should not alter the rank order.

We agree that divisive normalization should not alter the rank order, but the rank order may change in first-order neurons, which carries through to second-order neurons. This confusion may be related to the one mentioned above re: cross-overs vs non-monotonicity. Moreover, in the simulated data (Fig. 4D-H), the Jaccard similarity was calculated based on only the 50 neurons with the highest affinity, not the entire population of neurons. As shown in Fig. 4H, most of the rank-order change happens in the remaining 150 neurons.

Note that in response to a comment by Reviewer 3, we will change the presentation of Fig. 4H in the revision.

If the set of early responders does change, how will the decoder need to change, and what precise predictions can be made that can be tested experimentally? The lack of exploration of this aspect of the results seems like a missed opportunity.

In the Discussion, we wrote about how downstream circuits will need to learn which set of neurons are to be associated with each distinct concentration level. We will expand upon this point and include experimentally testable predictions.

Based on the methods, for Figures 1 and 2, it appears the responses across time, trials, and odorants were averaged to get a single data point per neuron for each concentration. Would this averaging not severely dilute trends in the data? The one that particularly concerns me is the averaging across different odorants. If you do odor-by-odor analysis, is the flattening of second-order neural responses still observable? Because some odorants activate more globally and some locally, I would expect a wide variety of dose-response relationships that vary with odor identity (more compressed in second-order neurons, of course). It would be good to show some representative neural responses and show how the extracted values for each neuron are a faithful/good representation of its response variation across intensities.

It appears there is some confusion here; we will clarify in the text and figure captions that we did not average across different odors in our analysis. We will also add figure panels showing some representative neural responses as suggested by the Reviewer.

A lot of neurons seem to have responses that flat line closer to zero (both firing rate and dF/F in Figure 1). Are these responsive neurons? The mean dF/F also seems to hover not significantly above zero. Hence, I was wondering if the number of neurons is reducing the trend in the data significantly.

Yes, if a neuron responds to at least one concentration level in at least 50% of the trials, it is considered responsive. So it is possible that some neurons respond to one concentration level and otherwise flatline near zero.  We will highlight a few example neurons to visualize this scenario.

I did not fully understand the need to show the increase in the odor response across concentrations as a polar plot. I see potential issues with the same. For example, the following dose-response trend at four intensities (C4 being the highest concentration and C1 the lowest): response at C3 > response at C1 and response at C4 > response at C2. But response at C3 < response at C2. Hence, it will be in the top right segment of the polar plot. However, the responses are not monotonic with concentrations. So, I am not convinced that the polar plot is the right way to characterize the dose-response curves. Just my 2 cents.

Your 2 cents are valuable! Thank you for raising this point. Instead of computing two slopes (C1-C3 and C2-C4), we will expand our analysis to include all three slopes (C1-C2, C2-C3, C3-C4). Consequently, there are 2^3 = 8 different response shapes, and we will list them and quantify the fraction of the responses that fall into each shape category.

In many analyses, simulated data were used (Figures 3 and 4). However, there is no comparison of how well the simulated data fit the experimental data. For example, the Simulated 1st order neuron in Figure 3D does not show a change in rank-order for the first-order neuron. In Figure 3E, temporal response patterns in second-order neurons look unrealistic. Some objective comparison of simulated and experimental data would help bolster confidence in these results.

We believe the Reviewer is referring to Figs. 4D and 4E, since Fig. 3D does not show a first-order neuron simulation, and there is no Fig 3E. In Fig. 4D there is no change of rank order because the simulation is for a single odor and single concentration level, and the change of rank-order (i.e., cross-overs) as we define occurs between concentration levels. We will clarify this in the manuscript.

Reviewer #3:

While the authors focus on concentration-dependent increases in first-order neuron activity, reflecting the majority of observed responses, recent work from the Imai group shows that odorants can also lead to direct first-order neuron inhibition (i.e., reduction in spontaneous activity), and within this subset, increasing odorant concentration tends to increase the degree of inhibition. Some discussion of these findings and how they may complement divisive normalization to contribute to the diverse second-order neuron concentration-dependence would be of interest and help expand the context of the current results.

We thank the Reviewer for the suggestion. We will request datasets of first-order neuron responses from the groups who acquired them. We will analyze this data to determine the role of inhibition or antagonistic binding and quantify what percentage of first-order neurons respond less strongly with larger concentrations.

Related to the above point, odorant-evoked inhibition of second-order neurons is widespread in mammalian mitral cells and significantly contributes to the flattened concentration-dependence of mitral cells at the population level. Such responses are clearly seen in Figure 1D. Some discussion of how odorant-evoked mitral cell inhibition may complement divisive normalization, and likewise relate to comparatively lower levels of odorant-evoked inhibition among tufted cells, would further expand the context of the current results. Toward this end, replication of analyses in Figures 1D and E following exclusion of mitral cell inhibitory responses would provide insight into the contribution of such inhibition to the flattening of the mitral cell population concentration dependence.

We will perform the analysis suggested, specifically, we will set the negative mitral cell responses to 0 and assess whether the population mean remains flat.

The idea of concentration-dependent crossover responses across the first-order population being required for divisive normalization to generate individually diverse concentration response functions across the second-order population is notable. The intuition of the crossover responses is that first-order neurons that respond most sensitively to any particular odorant (i.e., at the lowest concentration) respond with overall lower activity at higher concentrations than other first-order neurons less sensitively tuned to the odorant. Whether this is a consistent, generalizable property of odorant binding and first-order neuron responsiveness is not addressed by the authors, however. Biologically, one mechanism that may support such crossover events is intraglomerular presynaptic/feedback inhibition, which would be expected to increase with increasing first-order neuron activation such that the most-sensitively responding first-order neurons would also recruit the strongest inhibition as concentration increases, enabling other first-order neurons to begin to respond more strongly. Discussion of this and/or other biological mechanisms (e.g., first-order neuron depolarization block) supporting such crossover responses would strengthen these results.

We thank the reviewer for providing additional mechanisms to consider. As suggested, we will add discussion of these alternatives to divisive normalization.

It is unclear to what degree the latency analysis considered in Figures 4D-H works with the overall framework of divisive normalization, which in Figure 3 we see depends on first-order neuron crossover in concentration response functions. Figure 4D suggests that all first-order neurons respond with the same response amplitude (R in eq. 3), even though this is supposed to be pulled from a distribution. It's possible that Figure 4D is plotting normalized response functions to highlight the difference in latency, but this is not clear from the plot or caption. If response amplitudes are all the same, and the response curves are, as plotted in Figure 4D, identical except for their time to half-max, then it seems somewhat trivial that the resulting second-order neuron activation will follow the same latency ranking, regardless of whether divisive normalization exists or not. However, there is some small jitter in these rankings across concentrations (Figure 4G), suggesting there is some randomness to the simulations. It would be helpful if this were clarified (e.g., by showing a non-normalized Figure 4D, with different response amplitudes), and more broadly, it would be extremely helpful in evaluating the latency coding within the broader framework proposed if the authors clarified whether the simulated first-order neuron response timecourses, when factoring in potentially different amplitudes (R) and averaging across the entire response window, reproduces the concentration response crossovers observed experimentally. In summary, in the present manuscript, it remains unclear if concentration crossovers are captured in the latency simulations, and if not, the authors do not clearly address what impact such variation in response amplitudes across concentrations may have on the latency results. It is further unclear to what degree divisive normalization is necessary for the second-order neurons to establish and maintain their latency ranks across concentrations, or to exhibit concentration-dependent changes in latency.

As suggested by the Reviewer, we will add another simulation scenario where the response amplitudes (R) are different for different neurons. For each concentration, we will then average each neuron’s response across the entire response window and determine if the simulation reproduces the cross-overs as observed experimentally.

How the authors get from Figure 4G to 4H is not clear. Figure 4G shows second-order neuron response latencies across all latencies, with ordering based on their sorted latency to low concentration. This shows that very few neurons appear to change latency ranks going from low to high concentration, with a change in rank appearing as any deviation in a monotonically increasing trend. Focusing on the high concentration points, there appear to be 2 latency ranks switched in the first 10 responding neurons (reflecting the 1 downward dip in the points around neuron 8), rather than the 7 stated in the text. Across the first 50 responding neurons, I see only ~14 potential switches (reflecting the ~7 downward dips in the points around neurons 8, 20, 32, 33, 41, 44, 50), rather than the 32 stated in the text. It is possible that the unaccounted rank changes reflect fairly minute differences in latencies that are not visible in the plot in Figure 4G. This may be clarified by plotting each neuron's latency at low concentration vs. high concentration (i.e., similar to Figure 4H, but plotting absolute latency, not latency rank) to allow assessment of the absolute changes. If such minute differences are not driving latency rank changes in Fig. 4G, then a trend much closer to the unity line would be expected in Figure 4H. Instead, however, there are many massive deviations from unity, even within the first 50 responding neurons plotted in Figure 4G. These deviations include a jump in latency rank from 2 at low concentration to ~48 at high concentration. Such a jump is simply not seen in Figure 4G.

We apologize that Fig. 4H was a poor choice for visualization. What is plotted in Fig. 4H is the sorted identity of neurons under low and high concentrations, and points on the y=x line indicate that the two corresponding neurons have the same rank under the two concentrations. We will replace this panel with a more intuitive visualization, where the x and y axes are the ranks of the neurons; and deviation from the y=x line indicates how different the ranks are of a neuron to the two concentrations.

In the text, the authors state that "Odor identity can be encoded by the set of highest-affinity neurons (which remains invariant across concentrations)." Presumably, this is a restatement of the primacy model and refers to invariance in latency rank (since the authors have not shown that the highest-affinity neurons have invariant response amplitudes across concentration). To what degree this statement holds given the results in Figure 4H, however, which appear to show that some neurons with the earliest latency rank at low concentration jump to much later latency ranks at high concentration, remains unclear. Such changes in latency rank for only a few of the first responding neurons may be negligible for classifying odor identity among a small handful of odorants, but not among 1-2 orders of magnitude more odors, which may feasibly occur in a natural setting. Collectively, these issues with the execution and presentation of the latency analysis make it unclear how robust the latency results are.

The original primacy model states that the latency of a neuron decreases with increasing concentration, while the ranks of neurons remain unaltered. Our results, on the other hand, suggest that the ranks do at least partially change across concentrations. This leads to two possible decoding mechanisms. First, if the top K responding neurons remain invariant across concentrations (even if their individual ranks change within the top K), then the brain could learn to associate a population of K neurons with a response latency; lower response latency means higher concentration. Second, if the top K responding neurons do not remain invariant across concentrations, then the brain would need to learn to associate a different set of neurons with each concentration level. The latter imposes additional constraints on the robustness of the primacy model and the corresponding read-out mechanism. We will include more discussion of these possibilities in the revision.

Analysis in Figures 4A-C shows that concentration can be decoded from first-order neurons, second-order neurons, or first-order neurons with divisive normalization imposed (i.e., simulating second-order responses). This does not say that divisive normalization is necessary to encode concentration, however. Therefore, for the authors to say that divisive normalization is "a potential mechanism for generating odor-specific subsets of second-order neurons whose combinatorial activity or whose response latencies represent concentration information" seems too strong a conclusion. Divisive normalization is not generating the concentration information, since that can be decoded just as well from the first-order neurons. Rather, divisive normalization can account for the different population patterns in concentration response functions between first- and second-order neurons without discarding concentration-dependent information.

We agree that the word “generating” is faulty. We thank the reviewer for their more precise wording, which we will adopt.

Performing the same polar histogram analysis of tufted vs. mitral cell concentration response functions (Figure 5B) provides a compelling new visualization of how these two cell types differ in their concentration variance. The projected importance of tufted cells to navigation, emerging directly through the inverse relationship between average concentration and distance (Figure 5C), is not surprising, and is largely a conceptual analysis rather than new quantitative analysis per se, but nevertheless, this is an important point to make. Another important consideration absent from this section, however, is whether and how divisive normalization may impact tufted cell activity. Previous work from the authors, as well as from Schoppa, Shipley, and Westbrook labs, has compellingly demonstrated that a major circuit mediating divisive normalization of mitral cells (GABA/DAergic short-axon cells) directly targets external tufted cells, and is thus very likely to also influence projection tufted cells. Such analysis would additionally provide substantially more justification for the Discussion statement "we analyzed an additional type of second-order neuron (tufted cells)", which at present instead reflects fairly minimal analysis.

We agree that tufted cells are subject to divisive normalization as well, albeit probably to a less degree than mitral cells. To determine the effect of this, we will alter the strength (and degree of sparseness of interglomerular interactions) of divisive normalization and determine if there is a regime where response features of tufted cells match those observed experimentally.

eLife Assessment

This study reports important negative results by showing that genetic removal of the RNA-binding protein PTBP1 in astrocytes is not sufficient to induce their conversion into neurons, challenging prior claims in the field. It also provides a systematic and insightful analysis of the role of PTBP1 in regulating astrocyte-specific splicing. The evidence is convincing, as the experiments are technically robust, rigorously controlled, and supported by both imaging and transcriptomic analyses.

Reviewer #1 (Public review):

Summary:

Zhang et al. used a conditional knockout mouse model to re-examine the role of the RNA-binding protein PTBP1 in the transdifferentiation of astroglial cells into neurons. Several earlier studies reported that PTBP1 knockdown can efficiently induce the transdifferentiation of rodent glial cells into neurons, suggesting potential therapeutic applications for neurodegenerative diseases. However, these findings have been contested by subsequent studies, which in turn have been challenged by more recent publications. In their current work, Zhang et al. deleted exon 2 of the Ptbp1 gene using an astrocyte-specific, tamoxifen-inducible Cre line and investigated, using fluorescence imaging and bulk and single-cell RNA-sequencing, whether this manipulation promotes the transdifferentiation of astrocytes into neurons across various brain regions. The data strongly indicate that genetic ablation of PTBP1 is not sufficient to drive efficient conversion of astrocytes into neurons. Interestingly, while PTBP1 loss alters splicing patterns in numerous genes, these changes do not shift the astroglial transcriptome toward a neuronal profile.

Strengths:

Although this is not the first report of PTBP1 ablation in mouse astrocytes in vivo, this study utilizes a distinct knockout strategy and provides novel insights into PTBP1-regulated splicing events in astrocytes. The manuscript is well written, and the experiments are technically sound and properly controlled. I believe this study will be of considerable interest to a broad readership.

Weaknesses:

(1) The primary point that needs to be addressed is a better understanding of the effect of exon 2 deletion on PTBP1 expression. Figure 4D shows successful deletion of exon 2 in knockout astrocytes. However, assuming that the coverage plots are CPM-normalized, the overall PTBP1 mRNA expression level appears unchanged. Figure 6A further supports this observation. This is surprising, as one would expect that the loss of exon 2 would shift the open reading frame and trigger nonsense-mediated decay of the PTBP1 transcript. Given this uncertainty, the authors should confirm the successful elimination of PTBP1 protein in cKO astrocytes using an orthogonal approach, such as Western blotting, in addition to immunofluorescence. They should also discuss possible reasons why PTBP1 mRNA abundance is not detectably affected by the frameshift.

(2) The authors should analyze PTBP1 expression in WT and cKO substantia nigra samples shown in Figure 3 or justify why this analysis is not necessary.

(3) Lines 236-238 and Figure 4E: The authors report an enrichment of CU-rich sequences near PTBP1-regulated exons. To better compare this with previous studies on position-specific splicing regulation by PTBP1, it would be helpful to assess whether the position of such motifs differs between PTBP1-activated and PTBP1-repressed exons.

(4) The analyses in Figure 5 and its supplement strongly suggest that the splicing changes in PTBP1-depleted astrocytes are distinct from those occurring during neuronal differentiation. However, the authors should ensure that these comparisons are not confounded by transcriptome-wide differences in gene expression levels between astrocytes and developing neurons. One way to address this concern would be to compare the new PTBP1 cKO data with publicly available RNA-seq datasets of astrocytes induced to transdifferentiate into neurons using proneural transcription factors (e.g., PMID: 38956165).

Reviewer #2 (Public review):

Summary:

The manuscript by Zhang and colleagues describes a study that investigated whether the deletion of PTBP1 in adult astrocytes in mice led to an astrocyte-to-neuron conversion. The study revisited the hypothesis that reduced PTBP1 expression reprogrammed astrocytes to neurons. More than 10 studies have been published on this subject, with contradicting results. Half of the studies supported the hypothesis while the other half did not. The question being addressed is an important one because if the hypothesis is correct, it can lead to exciting therapeutic applications for treating neurodegenerative diseases such as Parkinson's disease.

In this study, Zhang and colleagues conducted a conditional mouse knockout study to address the question. They used the Cre-LoxP system to specifically delete PTBP1 in adult astrocytes. Through a series of carefully controlled experiments, including cell lineage tracing, the authors found no evidence for the astrocyte-to-neuron conversion.

The authors then carried out a key experiment that none of the previous studies on the subject did: investigating alternative splicing pattern changes in PTBP1-depleted cells using RNA-seq analysis. The idea is to compare the splicing pattern change caused by PTBP1 deletion in astrocytes to what occurs during neurodevelopment. This is an important experiment that will help illuminate whether the astrocyte-to-neuron transition occurred in the system. The result was consistent with that of the cell staining experiments: no significant transition was detected.

These experiments demonstrate that, in this experimental setting, PTBT1 deletion in adult astrocytes did not convert the cells to neurons.

Strengths:

This is a well-designed, elegantly conducted, and clearly described study that addresses an important question. The conclusions provide important information to the field.<br /> To this reviewer, this study provided convincing and solid experimental evidence to support the authors' conclusions.

Weaknesses:

The Discussion in this manuscript is short and can be expanded. Can the authors speculate what led to the contradictory results in the published studies? The current study, in combination with the study published in Cell in 2021 by Wang and colleagues, suggests that observed difference is not caused by the difference of knockdown vs. knockout. Is it possible that other glial cell types are responsible for the transition? If so, what cells? Oligodendrocytes?

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Zhang et al. used a conditional knockout mouse model to re-examine the role of the RNA-binding protein PTBP1 in the transdifferentiation of astroglial cells into neurons. Several earlier studies reported that PTBP1 knockdown can efficiently induce the transdifferentiation of rodent glial cells into neurons, suggesting potential therapeutic applications for neurodegenerative diseases. However, these findings have been contested by subsequent studies, which in turn have been challenged by more recent publications. In their current work, Zhang et al. deleted exon 2 of the Ptbp1 gene using an astrocyte-specific, tamoxifen-inducible Cre line and investigated, using fluorescence imaging and bulk and single-cell RNA-sequencing, whether this manipulation promotes the transdifferentiation of astrocytes into neurons across various brain regions. The data strongly indicate that genetic ablation of PTBP1 is not sufficient to drive efficient conversion of astrocytes into neurons. Interestingly, while PTBP1 loss alters splicing patterns in numerous genes, these changes do not shift the astroglial transcriptome toward a neuronal profile.

Strengths:

Although this is not the first report of PTBP1 ablation in mouse astrocytes in vivo, this study utilizes a distinct knockout strategy and provides novel insights into PTBP1-regulated splicing events in astrocytes. The manuscript is well written, and the experiments are technically sound and properly controlled. I believe this study will be of considerable interest to a broad readership.

Weaknesses:

(1) The primary point that needs to be addressed is a better understanding of the effect of exon 2 deletion on PTBP1 expression. Figure 4D shows successful deletion of exon 2 in knockout astrocytes. However, assuming that the coverage plots are CPM-normalized, the overall PTBP1 mRNA expression level appears unchanged. Figure 6A further supports this observation. This is surprising, as one would expect that the loss of exon 2 would shift the open reading frame and trigger nonsense-mediated decay of the PTBP1 transcript. Given this uncertainty, the authors should confirm the successful elimination of PTBP1 protein in cKO astrocytes using an orthogonal approach, such as Western blotting, in addition to immunofluorescence. They should also discuss possible reasons why PTBP1 mRNA abundance is not detectably affected by the frameshift.

We thank the reviewer for raising this important point. Indeed, the deletion of exon 2 introduces a frameshift that is predicted to disrupt the PTBP1 open reading frame and trigger nonsensemediated decay (NMD). While our CPM-normalized coverage plots (Figure 4D) and gene-level expression analysis (Figure 6A) suggest that PTBP1 mRNA levels remain largely unchanged in cKO astrocytes, we acknowledge that this observation is counterintuitive and merits further clarification.

We suspect that the process of brain tissue dissociation and FACS sorting for bulk or single cell RNA-seq may enrich for nucleic material and thus dilute the NMD signal, which occurs in the cytoplasm. Alternatively, the transcripts (like other genes) may escape NMD for unknown mechanisms. Although a frameshift is a strong indicator for triggering NMD, it does not guarantee NMD will occur in every case. We will include this discussion in the revised manuscript to provide additional context for the apparent discrepancy between mRNA abundance and protein loss.

Regarding the validation of PTBP1 protein depletion in cKO astrocytes by Western blotting, we acknowledge that orthogonal approaches to confirm PTBP1 elimination would address uncertainty around the effect of exon 2 deletion on PTBP1 expression. The low cell yield of cKO astrocytes poses a significant burden on obtaining sufficient samples for immunoblotting detection of PTBP1 depletion. On average 3-5 adult animals per genotype are needed for each biological replicate. Our characterization of this Ptbp1 deletion allele in other contexts show the loss of full length PTBP1 proteins in ESCs and NPCs using Western blotting. Furthermore, germline homozygous mutant mice do not survive beyond embryonic day 6, supporting that it is  a loss of function allele.

(2) The authors should analyze PTBP1 expression in WT and cKO substantia nigra samples shown in Figure 3 or justify why this analysis is not necessary.

We thank the reviewer for pointing out this important question. We used Aldh1l1-CreERT2, which is designed to be active in all the astrocyte throughout mouse brain. Although we have systematically verified PTBP1 elimination in different mouse brain regions (cortex and striatum) at multiple time points (from 4w to 12w after tamoxifen administration), we agree that it remains necessary and important to demonstrate whether the observed lack of astrocyte-to-neuron conversion is indeed associated with sufficient PTBP1 depletion. We will analyze the PTBP1 expression in the substantia nigra, as we did in the cortex and striatum. 

(3) Lines 236-238 and Figure 4E: The authors report an enrichment of CU-rich sequences near PTBP1-regulated exons. To better compare this with previous studies on position-specific splicing regulation by PTBP1, it would be helpful to assess whether the position of such motifs differs between PTBP1-activated and PTBP1-repressed exons.

We thank the reviewer for this insightful comment. We agree that assessing the positional distribution of CU-rich motifs between PTBP1-activated and PTBP1-repressed exons would provide valuable insight into the position-specific regulatory mechanisms of PTBP1. In response, we will perform separate motif enrichment analyses for PTBP1-activated and PTBP1-repressed exons and examine whether their positional patterns differ. This will help clarify whether these exons are differentially regulated by PTBP1 through distinct motif positioning in mature astrocytes.

(4) The analyses in Figure 5 and its supplement strongly suggest that the splicing changes in PTBP1-depleted astrocytes are distinct from those occurring during neuronal differentiation. However, the authors should ensure that these comparisons are not confounded by transcriptome-wide differences in gene expression levels between astrocytes and developing neurons. One way to address this concern would be to compare the new PTBP1 cKO data with publicly available RNA-seq datasets of astrocytes induced to transdifferentiate into neurons using proneural transcription factors (e.g., PMID: 38956165).

We would like to express our gratitude for the thoughtful feedback. We agree that transcriptomewide differences in gene expression between astrocytes and developing neurons could confound the interpretation of splicing differences. To address this concern, we will incorporate publicly available RNA-seq datasets from studies in which astrocytes are reprogrammed into neurons using proneural transcription factors (PMID: 38956165). 

Reviewer #2 (Public review):

Summary:

The manuscript by Zhang and colleagues describes a study that investigated whether the deletion of PTBP1 in adult astrocytes in mice led to an astrocyte-to-neuron conversion. The study revisited the hypothesis that reduced PTBP1 expression reprogrammed astrocytes to neurons. More than 10 studies have been published on this subject, with contradicting results. Half of the studies supported the hypothesis while the other half did not. The question being addressed is an important one because if the hypothesis is correct, it can lead to exciting therapeutic applications for treating neurodegenerative diseases such as Parkinson's disease.

In this study, Zhang and colleagues conducted a conditional mouse knockout study to address the question. They used the Cre-LoxP system to specifically delete PTBP1 in adult astrocytes. Through a series of carefully controlled experiments, including cell lineage tracing, the authors found no evidence for the astrocyte-to-neuron conversion.

The authors then carried out a key experiment that none of the previous studies on the subject did: investigating alternative splicing pattern changes in PTBP1-depleted cells using RNA-seq analysis. The idea is to compare the splicing pattern change caused by PTBP1 deletion in astrocytes to what occurs during neurodevelopment. This is an important experiment that will help illuminate whether the astrocyte-to-neuron transition occurred in the system. The result was consistent with that of the cell staining experiments: no significant transition was detected.

These experiments demonstrate that, in this experimental setting, PTBT1 deletion in adult astrocytes did not convert the cells to neurons.

Strengths:

This is a well-designed, elegantly conducted, and clearly described study that addresses an important question. The conclusions provide important information to the field.

To this reviewer, this study provided convincing and solid experimental evidence to support the authors' conclusions.

Weaknesses:

The Discussion in this manuscript is short and can be expanded. Can the authors speculate what led to the contradictory results in the published studies? The current study, in combination with the study published in Cell in 2021 by Wang and colleagues, suggests that observed difference is not caused by the difference of knockdown vs. knockout. Is it possible that other glial cell types are responsible for the transition? If so, what cells? Oligodendrocytes?

We are grateful for the reviewer’s careful reading and valuable suggestions. These will help us improve the manuscript. We will expand the Discussion. The contradictory results in the previously published studies can be due to the stringency and neuronal leakage of the astrocytespecific GFAP promoter that some investigators chose. Other possibilities include alternative cell origin, increased neuronal resilience, or combinations of as yet unidentified factors.

Reviewer #1 (Public review):

Summary:

This paper presents maRQup, a Python pipeline for automating the quantitative analysis of preclinical cancer immunotherapy experiments using bioluminescent imaging in mice. maRQup processes images to quantify tumor burden over time and across anatomical regions, enabling large-scale analysis of over 1,000 mice. The study uses this tool to compare different CAR-T cell constructs and doses, identifying differences in initial tumor control and relapse rates, particularly noting that CD19.CD28 CAR-T cells show faster initial killing but higher relapse compared to CD19.4-1BB CAR-T cells. Furthermore, maRQup facilitates the spatiotemporal analysis of tumor dynamics, revealing differences in growth patterns based on anatomical location, such as the snout exhibiting more resistance to treatment than bone marrow.

Strengths:

(1) The maRQup pipeline enables the automatic processing of a large dataset of over 1,000 mice, providing investigators with a rapid and efficient method for analyzing extensive bioluminescent tumor image data.

(2) Through image processing steps like tail removal and vertical scaling, maRQup normalizes mouse dimensions to facilitate the alignment of anatomical regions across images. This process enables the reliable demarcation of nine distinct anatomical regions within each mouse image, serving as a basis for spatiotemporal analysis of tumor burden within these consistent regions by quantifying average radiance per pixel.

Weaknesses:

(1) While the pipeline aims to standardize images for regional assessment, the reliance on scaling primarily along the vertical axis after tail removal may introduce limitations to the quantitative robustness of the anatomically defined regions. This approach does not account for potential non-linear growth across dimensions in animals of different ages or sizes, which could result in relative stretching or shrinking of subjects compared to an average reference.

(2) Furthermore, despite excluding severely slanted images, the pipeline does not fully normalize for variations in animal pose during image acquisition (e.g., tucked body, leaning). This pose variability not only impacts the precise relative positioning of internal anatomical regions, potentially making their definition based on relative image coordinates more qualitative than truly quantitative for precise regional analysis, but it also means that the bioluminescent light signal from the tumor will not propagate equally to the camera, as photons will travel differentially through the tissue. This differing light path through tissues due to variable positioning can introduce large variability in the measured radiance that was not accounted for in the analysis algorithm. Achieving more robust anatomical and quantitative normalization might require methods that control animal posture using a rigid structure during imaging.

Reviewer #2 (Public review):

Summary:

The authors developed a method that automatically processes bioluminescent tumor images for quantitative analysis and used it to describe the spatiotemporal distribution of tumor cells in response to CD19-targeting CAR-T cells, comprising CD28 or 4-1BB costimulatory domains. The conclusion highlights the dependence of tumor decay and relapse on the number of injected cells, the type of cells, and the initial growth rate of tumors ( where initial is intended from the first day of therapy). The authors also determined the spatiotemporal analysis of tumor response to CAR T therapy in different regions of the mouse body in a model of acute lymphoblastic leukemia (ALL).

Strengths:

The analysis is based on a large number of images and accounts for many variables. The results of the analysis largely support their claims that the kinetics of tumor decay and relapse are dependent on the CAR T co-stimulatory domain and number of cells injected and tumor growth rates.

Weaknesses:

The study does not specify how a) differences in mouse positioning (and whether they excluded not-aligned mice) and b) tumor spread at the start of therapy influenced their data. The study does not take into account the potential heterogeneity of CAR T cells in terms of CAR T expression or T cell immunophenotype ( differentiation, exhaustion, fitness...).

Reviewer #3 (Public review):

Summary:

The paper "The 1000+ mouse project: large-scale spatiotemporal parametrization and modeling of preclinical cancer immunotherapies" is focused on developing a novel methodology for automatic processing of bioluminescence imaging data. It provides quantitative and statistically robust insights into preclinical experiments that will contribute to optimizing cell-based therapies. There is an enormous demand for such methods and approaches that enable the spatiotemporal evaluation of cell monitoring in large cohorts of experimental animals.

Strengths:

The manuscript is generally well written, and the experiments are scientifically sound. The conclusions reflect the soundness of experimental data. This approach seems to be quite innovative and promising to improve the statistical accuracy of BLI data quantification.

This methodology can be used as a universal quantification tool for BLI data for in vivo assessment of adoptively transferred cells due to the versatility of the technology.

Weaknesses:

No weaknesses were identified by this Reviewer.

eLife Assessment

The authors developed a fundamental computational method, which is intended to automatically process bioluminescence imaging-derived tumour images across anatomical regions and over time. This allows quantitative analysis of such data, and the authors applied it to describe the spatiotemporal distribution of tumour cells in response to CD19-targeted CAR-T cells that contained either CD28 or 4-1BB costimulatory domains. Some operational limitations were identified, which relate to the pipeline's reliance on predefined regions of interest instead of aligning signal sites with anatomical information, scaling, and not taking animal pose into account. Overall, the authors provide compelling evidence for the functionality of their computational approach towards automated analysis of bioluminescence imaging data, while applying it to a current topic of wide interest in cell therapy research.

eLife Assessment

This fundamental work provides solid evidence that advances our understanding of the physical mechanisms underlying bacterial cell division by examining the role of membrane tension and FtsZ condensation in sequential stages of division. The effect of accDA overexpression on membrane tension was carefully characterized. To further enhance rigor, the authors could consider examining orthogonal perturbations to membrane tension, addressing membrane tension vs. fluidity, and addressing the ability of FtsZ to bend membranes in cells.

Reviewer #1 (Public review):

In this study, Ramirez-Diaz and coworkers address an important and lingering question in the bacterial cell division field, i.e., whether FtsZ polymers bend the cell membrane inwards, using an elegant and innovative approach. The key cell division protein FtsZ is a homolog of tubulin and forms curved polymers in the presence of GTP. It has long been hypothesized that this curvature provides the force to bend the cell membrane inwards, thereby triggering septal synthesis. Several in vitro studies have shown that purified FtsZ, when attached to the membrane, can indeed deform artificial membranes. However, other studies favor the view that only septal peptidoglycan synthesis drives cell division. Ramirez-Diaz has tried to address the membrane deformation theory in vivo by developing a mutant that synthesizes extra lipids. In this way, the membrane tension is lowered, which would facilitate cell division if deformation of the cell membrane by curved FtsZ polymers is a crucial step in cell division. Surprisingly, they showed that this mutant overcomes the cell division block in a sepF ezrA double mutant. In addition, they carefully characterize the membrane characteristics of the mutant and the effect on FtsZ ring formation. With this work, they have set up a very useful model system to study the role of the cell membrane in cell division, and also a new tool to better study the function of the cell division proteins EzrA and SepF. Overall, this is a very important study for the bacterial cell division field with interesting findings and ideas.

Nevertheless, the authors jump to a conclusion that I cannot yet share. The main issue I have is that they focus on membrane tensions, yet what they seem to modulate is membrane fluidity. Both are clearly related but not the same. I think that it is important to extensively address this issue in the manuscript. They (also) use Laurdan generalized polarization as an indication of membrane tension (Figure 1F), but this method is primarily used in the literature to measure membrane fluidity. In addition, they explain the occurrence of strong local fluorescent membrane signals as the occurrence of double membranes (Figure S1D), whereas others have shown that such fluorescent hot spots can, in theory, also be formed by local accumulation of fluid lipids (PMID: 24603761). The reason why it is so important to distinguish fluidity from tension is that for the attachment of FtsZ polymers, the cell makes use of anchor proteins like FtsA that contain an amphipathic alpha helix, which inserts into the inner leaflet of the lipid bilayer. Importantly, this insertion only works when the fatty acids can be "pushed apart", and this is stimulated by unsaturated and short-chain fatty acids that make the membrane more fluid (PMID: 12676941). If a membrane is "more fluid", then it can more easily accommodate an amphipathic helix. Thus, the production of extra membrane material may increase the fluidity of the cell membrane, as the Laurdan GP measurements indicated, which can then facilitate the attachment of FtsA, including the attached FtsZ polymers, to the membrane. In other words, what the authors have observed may not be a stimulation of Z-ring formation due to lowering membrane tension, but rather because of stimulated binding of FtsZ polymers to the cell membrane. It might be that the attachment of late cell division to the Z-ring, which is all transmembrane proteins, is also facilitated in a more fluid lipid environment. The authors have not excluded the latter (by using a mutant depleted for one of the late cell division proteins).

Finally, the authors performed EM studies to measure septa thickness, and surprisingly, they did not seem to observe deformed septa in a sepF-ezrA double mutant, when overexpressing accDA, while it has been shown before that the absence of SepF leads to strongly deformed septa. Since this finding nuances the mode of action of SepF polymers, it should be discussed.

In conclusion, this is an important and interesting study, but it seems crucial for the interpretation of the findings to include a clear discussion on membrane fluidity and its consequences.

Reviewer #2 (Public review):

Summary:

In this manuscript, Ramirez-Diaz and colleagues set out to examine key physical mechanisms of bacterial cell division, using the Gram-positive model Bacillus subtilis. Specifically, they investigate the hypothesis that condensation of polymers of the master regulator of division FtsZ can deform membranes to initiate division, but that this is limited by membrane tension. They test this by modulating both membrane tension and FtsZ condensation genetically. To modulate membrane tension, they overexpress accDA to increase the rate of phospholipid synthesis and increase the "hidden membrane reservoir", thereby decreasing membrane tension. To modulate FtsZ condensation, they deplete the bundling protein EzrA in a background lacking a second bundling protein, SepF. They confirm the effects of accDA overexpression on membrane tension using two different sensors before assessing the relationship between membrane tension, FtsZ condensation, and division. They demonstrate that cells with excess membrane (reduced membrane tension) can divide with reduced bundling protein abundance, suggesting that FtsZ condensation driven by ZBPs normally serves to overcome membrane tension to initiate division. In addition, they find an inverse relationship between membrane tension and FtsZ ring constriction rate, but no effect of membrane tension on FtsZ treadmilling. Estimation of physical parameters leads them to conclude that very small membrane fluctuations are sufficient to initiate division in unperturbed cells and that the membrane contributes only ~0.1% of the total surface tension strength, maintaining cell shape.

Strengths:

The highly quantitative approach of this work is a strength, as is the rigorous assessment of membrane tension with multiple sensors. The model proposed is largely consistent with existing data and provides a mechanism for further study and validation. The study tackles a major outstanding question in bacterial cell biology, and provides a potential mechanism for a key step in replication with broad implications in other organisms.

Weaknesses:

The authors only use one method (overexpression of accDA) to perturb membrane tension, which could influence division in unanticipated ways (e.g., metabolic adaptations and/or activation of signaling pathways). The proposed model for initiation of division posits that FtsZ condensation bends membranes, which is supported by in vitro evidence, but there is no in vivo evidence that FtsZ condensation can bend membranes in cells. It remains possible that the function of FtsZ condensation is to localize sufficient cell wall synthetic activity to build peptidoglycan that rectifies membrane fluctuations.

eLife Assessment

This important study presents the rational redesign and engineering of interleukin-7. The data from the integrated approach of using computational, biophysical, and cellular experiments are convincing, but this study can further benefit from more quantitative analyses and structural data. This paper is broadly relevant to those studying immunomodulation using biologics.

Reviewer #1 (Public review):

Summary:

This manuscript describes the use of computational tools to design a mimetic of the interleukin-7 (IL-7) cytokine with superior stability and receptor binding activity compared to the naturally occurring molecule. The authors focused their engineering efforts on the loop regions to preserve receptor interfaces while remediating structural irregularities that destabilize the protein. They demonstrated the enhanced thermostability, production yield, and bioactivity of the resulting molecule through biophysical and functional studies. Overall, the manuscript is well written, novel, and of high interest to the fields of molecular engineering, immunology, biophysics, and protein therapeutic design. The experimental methodologies used are convincing; however, the article would benefit from more quantitative comparisons of bioactivity through titrations.

Reviewer #2 (Public review):

Summary:

This manuscript presents the computational design and experimental validation of Neo-7, an engineered variant of interleukin-7 (IL-7) with improved folding efficiency, expression yield, and therapeutic activity. The authors employed a rational protein design approach using Rosetta loop remodeling to reconnect IL-7's functional helices through shorter, more efficient loops, resulting in a protein with superior stability and binding affinity compared to wild-type IL-7. The work demonstrates promising translational potential for cancer immunotherapy applications.

Strengths:

(1) The integration of Rosetta loop remodeling with AlphaFold validation represents an established computational pipeline for rational protein design. The iterative refinement process, using both single-sequence and multimer AlphaFold predictions, is methodologically sound.

(2) The authors provide thorough characterization across multiple platforms (yeast display, bacterial expression, mammalian cell expression) and assays (binding kinetics, thermostability, bioactivity), strengthening the robustness of their findings.

(3) The identification of the critical helix 1 kink stabilized by disulfide bonding and its recreation through G4C/L96C mutations demonstrates deep structural understanding and successful problem-solving.

(4) The MC38 tumor model results show clear therapeutic advantages of Neo-7 variants, with compelling immune profiling data supporting CD8+ T cell-mediated anti-tumor mechanisms.

(5) The transcriptomic profiling provides valuable mechanistic insights into T cell activation states and suggests reduced exhaustion markers, which are clinically relevant.

Weaknesses:

(1) While computational predictions are extensive, the manuscript lacks experimental structural validation of the designed Neo-7 variants. The term "Structural Validation" should not be used in the header.

(2) The authors observe slower on/off-rates for Neo-7 variants compared to wild-type IL-7. Could the authors speculate about the potential biological impacts of the slow off-rate, especially focusing on downstream signaling pathways that might be differentially affected by the altered binding kinetics of Neo-7 variants?

(3) While computational immunogenicity prediction is provided, these methods are very limited.

eLife Assessment

This fundamental study explores a novel cellular mechanism underlying the degeneration of locus coeruleus neurons during chronic restraint stress. The evidence supporting the overexpression of LC neurons after chronic stress is compelling. However, to fully support the broad implications for LC degeneration and Alzheimer's disease, the study would benefit from stronger causal integration and validation in age-relevant models.

Reviewer #1 (Public review):

This study aims to elucidate the mechanisms by which stress-induced α2A-adrenergic receptor (α2A-AR) internalization leads to cytosolic noradrenaline (NA) accumulation and subsequent neuronal dysfunction in the locus coeruleus (LC). While the manuscript presents an interesting but ambitious model involving calcium dynamics, GIRK channel rundown, and autocrine NA signaling, several key limitations undermine the strength of the conclusions.

First, the revision does not include new experiments requested by reviewers to validate core aspects of the mechanism. Specifically, there is no direct measurement of cytosolic NA levels or MAO-A enzymatic activity to support the link between receptor internalization and neurochemical changes. The authors argue that such measurements are either not feasible or beyond the scope of the study, leaving a significant gap in the mechanistic chain of evidence.

Second, the behavioral analysis remains insufficient to support claims of cognitive impairment. The use of a single working memory test following an anxiety test is inadequate to verify memory dysfunction behaviors. Additional cognitive assays, such as the Morris Water Maze or Novel Object Recognition, are recommended but not performed.

Third, concerns regarding the lack of rigor in differential MAO-A expression in fluorescence imaging were not addressed experimentally. Instead of clarifying the issue, the authors moved the figure to supplementary data without providing further evidence (e.g., an enzymatic assay or quantitative reanalysis of Western blot, or re-staining of IF for MAO-A) to support their interpretation.

Fourth, concerns regarding TH staining remain unresolved. In Figure S7, the α2A-AR signal appears to resemble TH staining, and vice versa, raising the possibility of labeling errors. It is recommended that the authors re-examine this issue by either double-checking the raw data or repeating the immunostaining to validate the staining.

Overall, the manuscript offers a potentially interesting framework but falls short in providing the experimental rigor necessary to establish causality. The reliance on indirect reasoning and reorganizing of existing data, rather than generating new evidence, limits the overall impact and interpretability of the study.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the mechanism by which chronic stress induces degeneration of locus coeruleus (LC) neurons. The authors demonstrate that chronic stress leads to the internalization of α2A-adrenergic receptors (α2A-ARs) on LC neurons, causing increased cytosolic noradrenaline (NA) accumulation and subsequent production of the neurotoxic metabolite DOPEGAL via monoamine oxidase A (MAO-A). The study suggests a mechanistic link between stress-induced α2A-AR internalization, disrupted autoinhibition, elevated NA metabolism, activation of asparagine endopeptidase (AEP), and Tau pathology relevant to Alzheimer's disease (AD). The conclusions of this paper are largely well-supported by the data, but some aspects of image acquisition require further examination.

Strengths:

This study clearly demonstrates the effects of chronic stimulation on the excitability of LC neurons using electrophysiological techniques. It also elucidates the role of α2-adrenergic receptor (α2-AR) internalization and the associated upstream and downstream signaling pathways of GIRK-1, using a range of pharmacological agents, highlighting the innovative nature of the work. Additionally, the study identifies the involvement of the MAO-A-DOPEGAL-AEP pathway in this process. The topic is timely, the proposed mechanistic pathway is compelling, and the findings have translational relevance, particularly about therapeutic strategies targeting α2A-AR internalization in neurodegenerative diseases.

Weaknesses:

(1) The manuscript reports that chronic stress for 5 days increases MAO-A levels in LC neurons, leading to the production of DOPEGAL, activation of AEP, and subsequent tau cleavage into the tau N368 fragment, ultimately contributing to neuronal damage. However, the authors used wild-type C57BL/6 mice, and previous literature has indicated that AEP-mediated tau cleavage in wild-type mice is minimal and generally insufficient to cause significant behavioral alterations. Please clarify and discuss this apparent discrepancy.

(2) It is recommended that the authors include additional experiments to examine the effects of different durations and intensities of stress on MAO-A expression and AEP activity. This would strengthen the understanding of stress-induced biochemical changes and their thresholds.

(3) Please clarify the rationale for the inconsistent stress durations used across Figures 3, 4, and 5. In some cases, a 3-day stress protocol is used, while in others, a 5-day protocol is applied. This discrepancy should be addressed to ensure clarity and experimental consistency.

(4) The abbreviation "vMAT2" is incorrectly formatted. It should be "VMAT2," and the full name (vesicular monoamine transporter 2) should be provided at first mention.

Comments on revisions:

The authors have addressed all of the reviewers' comments.

Reviewer #3 (Public review):

Summary:

The authors present a technically impressive data set showing that repeated excitation or restraint stress internalises somatodendritic α2A adrenergic autoreceptors (α2A ARs) in locus coeruleus (LC) neurons. Loss of these receptors weakens GIRK-dependent autoinhibition, raises neuronal excitability, and is accompanied by higher MAO A, DOPEGAL, AEP, and tau N368 levels. The work combines rigorous whole-cell electrophysiology with barbadin-based trafficking assays, qPCR, Western blotting and immunohistochemistry. The final schematic is appealing and in principle, could explain early LC hyperactivity followed by degeneration in ageing and Alzheimer's disease.

Strengths:

Multi-level approach - The study integrates electrophysiology, pharmacology, mRNA quantification, and protein-level analysis.

Use of barbadin to block β-arrestin/AP-2-dependent internalisation is both technically precise and mechanistically informative

Well-executed electrophysiology

translation relevance

converges to a model that peers discussed (scientists can only discuss models - not data!)

Weaknesses:

Nevertheless, the manuscript currently reads as a sequence of discrete experiments rather than a single causal chain

Author response:

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

Reviewer #1 (Public review):

Weaknesses:

(1) The manuscript's logical flow is challenging and hard to follow, and key arguments could be more clearly structured, particularly in transitions between mechanistic components.

We have revised our manuscript so as to make it easy for readers to follow the logical flow in transitions between mechanistic components by adding the descriptions of Figure S1E-J, Figure S2F-K, Figure S3A-H, Figure S4A-F, Figure S5, and Figure S6 in the revised manuscript.

(2) The causality between stress-induced α2A-AR internalization and the enhanced MAO-A remains unclear. Direct experimental evidence is needed to determine whether α2A-AR internalization itself or Ca2+ drives MAO-A activation, and how they activate MAO-A should be considered.

We believe that the causality between stress-induced α2A-AR internalization and the enhancement of MAO-A is clearly demonstrated by our current experiments, while our explanations may be improved by making them easier to understand especially for those who are not expert on electrophysiology.

Firstly, it is well established that autoinhibition in LC neurons is mediated by α2A-AR coupled-GIRK (Arima et al., 1998, J Physiol; Williams et al., 1985, Neuroscience). We found that spike frequency adaptation in LC neurons was also mediated by α2A-AR coupled GIRK-I (Figure 1A-I), and that α2A-AR coupled GIRK-I underwent [Ca²⁺]_i dependent rundown (Figures 2, S1, S2), leading to an abolishment of spike-frequency adaptation (Figures S4). [Ca²⁺]_i dependent rundown of α2A-AR coupled GIRK-I was prevented by barbadin (Figure 2G-J), which prevents the internalization of G-protein coupled receptor (GPCR) channels.

Abolishment of spike frequency adaptation itself, i.e., “increased spike activity” can increase [Ca²⁺]_i because [Ca²⁺]_i is entirely dependent on the spike activity as shown by [Ca²⁺]_i imaging method in Figure S3.

Thus, α2A-AR internalization can increase [Ca²⁺]_i through the abolishment of autoinhibition or spike frequency adaptation, and a [Ca²⁺]_i increase drives MAO-A activation as reported previously (Cao et al., 2007, BMC Neurosci). The mechanism how Ca²⁺ activates MAO-A is beyond the scope of the current study.

Our study just focused on the mechanism how chronic or sever stress can cause persistent overexcitation and how it results in LC degeneration.

(3) The connection between α2A-AR internalization and increased cytosolic NA levels lacks direct quantification, which is necessary to validate the proposed mechanism.

Direct quantification of the relationship between α2A-AR internalization and increased cytosolic NA levels may not be possible, and may not be necessarily needed to be demonstrated as explained below.

The internalization of α2A-AR can increase [Ca²⁺]_i through the abolishment of autoinhibition or spike frequency adaptation, and [Ca²⁺]_i increases can facilitate NA autocrine (Huang et al., 2007), similar to the transmitter release from nerve terminals (Kaeser & Regehr, 2014, Annu Rev Physiol).

Autocrine released NA must be re-uptaken by NAT (NA transporter), which is firmly established (Torres et al., 2003, Nat Rev Neurosci). Re-uptake of NA by NAT is the only source of intracellular NA, and NA re-uptake by NAT should be increased as the internalization of NA biding site (α2A-AR) progresses in association with [Ca²⁺]_i increases (see page 11, lines 334-336).

Thus, the connection between α2A-AR internalization and increased cytosolic NA levels is logically compelling, and the quantification of such connection may not be possible at present (see the response to the comment made by the Reviewer #1 as Recommendations for the authors (2) and beyond the scope of our current study.

(4) The chronic stress model needs further validation, including measurements of stress-induced physiological changes (e.g., corticosterone levels) to rule out systemic effects that may influence LC activity. Additional behavioral assays for spatial memory impairment should also be included, as a single behavioral test is insufficient to confirm memory dysfunction.

It is well established that restraint stress (RS) increases corticosterone levels depending on the period of RS (García-Iglesias et al., 2014, Neuropharmacology), although we are not reluctant to measure the corticosterone levels. In addition, there are numerous reports that showed the increased activity of LC neurons in response to various stresses (Valentino et al., 1983; Valentino and Foote, 1988; Valentino et al., 2001; McCall et al., 2015), as described in the text (page 4, lines 96-98). Measurement of cortisol levels may not be able to rule out systemic effects of CRS on the whole brain.

We had already done another behavioral test using elevated plus maze (EPM) test.By combining the two tests, it may be possible to more accurately evaluate the results of Y-maze test by differentiating the memory impairment from anxiety. However, the results obtained by these behavioral tests are just supplementary to our current aim to elucidate the cellular mechanisms for the accumulation of cytosolic free NA. Therefore, we have softened the implication of anxiety and memory impairment (page 13, lines 397-400 in the revised manuscript).

(5) Beyond b-arrestin binding, the role of alternative internalization pathways (e.g., phosphorylation, ubiquitination) in α2A-AR desensitization should be considered, as current evidence is insufficient to establish a purely Ca²⁺ -dependent mechanism.

We can hardly agree with this comment. 

It was clearly demonstrated that repeated application of NA itself did not cause desensitization of α2A-AR (Figure S1A-D), and that the blockade of b-arrestin binding by barbadin completely suppressed the Ca^2a-dependent downregulation of GIRK (Figure 2G-K). These observations can clearly rule out the possible involvement of phosphorylation or ubiquitination for the desensitization.

Not only the barbadin experiment, but also the immunohistochemistry and western blot method clearly demonstrated the decrease of α2A-AR expression on the cell membrane (Figure 3).

Ca²⁺-dependent mechanism of the rundown of GIRK was convincingly demonstrated by a set of different protocols of voltage-clamp study, in which Ca²⁺ influx was differentially increased. The rundown of GIRK-I was orderly potentiated or accelerated by increasing the number of positive command pulses each of which induces Ca²⁺ influx (compare Figure S1E-J, Figure S2A-E and Figure S2F-K along with Figure 2A-F). The presence or absence of Ca²⁺ currents and the amount of Ca²⁺ currents determined the trend of the rundown of GIRK-I (Figures 2, S1 and S2). Because the same voltage protocol hardly caused the rundown when it did not induce Ca²⁺ currents in the absence of TEA (Figure S1F; compare with Figure 2B), blockade of Ca²⁺ currents by nifedipine would not be so beneficial.

We believe the series of voltage-clamp protocols convincingly demonstrated the orderly involvement of [Ca²⁺]_i in accelerating the rundown of GIRK-I.

(6) NA leakage for free NA accumulation is also influenced by NAT or VMAT2. Please discuss the potential role of VMAT2 in NA accumulation within the LC in AD. 

It has been demonstrated that reduced VMAT2 levels increased susceptibility to neuronal damage: VMAT2 heterozygote mice displayed increased vulnerability to MPTP as evidenced by reductions in nigral dopamine cell counts (Takahashi et al, 1997, PNAS). Thus, when the activity of VMAT2 in LC neurons were impaired by chronic restraint stress, cytosolic NA levels in LC neurons would increase. We have added such discussion in the revised manuscript (page 12, lines 381-384).

(7) Since the LC is a small brain region, proper staining is required to differentiate it from surrounding areas. Please provide a detailed explanation of the methodology used to define LC regions and how LC neurons were selected among different cell types in brain slices for whole-cell recordings.

LC neurons were identified immunohistochemically and electrophysiologically as we previously reported (see Fig. 2 in Front. Cell. Neurosci. 16:841239. doi: 10.3389/fncel.2022.841239). We have added this explanation in the method section of the revised manuscript (page 15, lines 474-475). A delayed spiking pattern in response to depolarizing pulses (Figure S10 in the revised manuscript) applied at a hyperpolarized membrane potential was commonly observed in LC neurons in many studies (Masuko et al., 1986; van den Pol et al., 2002; Wagner-Altendorf et al., 2019).

Reviewer #2 (Public review):

Weaknesses:

(1) The manuscript reports that chronic stress for 5 days increases MAO-A levels in LC neurons, leading to the production of DOPEGAL, activation of AEP, and subsequent tau cleavage into the tau N368 fragment, ultimately contributing to neuronal damage. However, the authors used wild-type C57BL/6 mice, and previous literature has indicated that AEP-mediated tau cleavage in wild-type mice is minimal and generally insufficient to cause significant behavioral alterations. Please clarify and discuss this apparent discrepancy.

In our study, normalized relative value of AEP-mediated tau cleavage (Tau N368) was much higher in CRS mice than non-stress wild-type mice. It is not possible to compare AEP-mediated tau cleavage between our non-stress wild type mice and those observed in previous study (Zhang et al., 2014, Nat Med), because band intensity is largely dependent on the exposure time and its numerical value is the normalized relative value. In view of such differences, our apparent band expression might have been intensified to detect small changes.

(2) It is recommended that the authors include additional experiments to examine the effects of different durations and intensities of stress on MAO-A expression and AEP activity. This would strengthen the understanding of stress-induced biochemical changes and their thresholds.

GIRK rundown was almost saturated after 3-day RS and remained the same in 5-day RS mice (Fig. 4A-G), which is consistent with the downregulation of α2A-AR and GIRK1 expression by 3-day RS (Fig. 3C, F and G; Fig. 4J and K). However, we examined the protein levels of MAO-A, pro/active-AEP and Tau N368 only in 5-day RS mice without examining in 3-day RS mice. This is because we considered the possibility that a high [Ca²⁺]_i condition may have to be sustained for some period of time to induce changes in MAO-A, AEP and Tau N368, and therefore 3-day RS may be insufficient to induce such changes. We have added this in the revised manuscript (page 17, lines 521-525).

(3) Please clarify the rationale for the inconsistent stress durations used across Figures 3, 4, and 5. In some cases, a 3-day stress protocol is used, while in others, a 5-day protocol is applied. This discrepancy should be addressed to ensure clarity and experimental consistency.

Please see our response to the comment (2).

(4) The abbreviation "vMAT2" is incorrectly formatted. It should be "VMAT2," and the full name (vesicular monoamine transporter 2) should be provided at first mention.

Thank you for your suggestion. We have revised accordingly.

Reviewer #3 (Public review):

Weaknesses:

Nevertheless, the manuscript currently reads as a sequence of discrete experiments rather than a single causal chain. Below, I outline the key points that should be addressed to make the model convincing.

Please see the responses to the recommendation for the authors made by reviewer #3.

Reviewer #1 (Recommendations for the authors):

(1) Improve the clarity and organization of the manuscript, ensuring smoother transitions between concepts and mechanisms.

Please see the response to the comment raised by Reviewer #1 as Weakness

(2) Adjust any quantifying method for cytosolic NA levels under different conditions to support the link between receptor internalization and NA accumulation.

If fluorescent indicator of cytosolic free NA is available, it would be possible to measure changes in cytosolic NA levels. However, at present, there appeared to be no fluorescence probe to label cytosolic NA. For example, NS521 labels both dopamine and norepinephrine inside neurosecretory vesicles (Hettie & Glass et al., 2014, Chemistry), and BPS3 fluorescence sensor labels NA around cell membrane by anchoring on the cell membrane (Mao et al., 2023, Nat Comm). Furthermore, the method reported in “A Genetically Encoded Fluorescent Sensor for Rapid and Specific In Vivo Detection of Norepinephrine” is limited to detect NA only when α2AR is expressed. In the present study, increases in cytosolic NA levels are caused by internalization of α2AR. Cytosolic NA measurements with GRAB NE photometry may not be applicable in the present study. However, we have discussed the availability of such fluorescent methods to directly prove the increase in cytosolic NA as a limitation of our study (page 14, lines 429-436 in the revised manuscript).

(3) Include validation of the chronic stress model with physiological and behavioral measures (e.g., corticosterone levels and another behavioral test).

Please see the response to the comment raised by Reviewer #1 as Weakness (4).

(4) All supplemental figures should be explicitly explained in the Results section. Specifically, clarify and describe the details of Figure S1G-K, Figure S2F-K, Figure S3A-H, Figure S4A-F, Figure S5, and Figure S6 to ensure all supplementary data are fully integrated into the main text.

We have more explicitly and clearly described the details of Figure S1E-J, Figure S2F-K, Figure S3A-H, Figure S4A-F, Figure S5, and Figure S6 and fully integrated those explanations into the main text in the revised manuscript.

(5) In Figure 3, the morphology of TH-positive cells differs between panels D and E. Additionally, TH is typically expressed in the cytosol, but in the provided images, it appears to be localized only to the membrane. Please clarify this discrepancy and provide a lower-magnification image to display a larger area, not one cell.

In a confocal image, TH is not necessarily expressed homogenously in the cytosol, but is expressed in a ring-shaped pattern inside the plasma membrane, avoiding the cell nucleus and its surrounding Golgi apparatus and endoplasmic reticulum (ER) (Henrich et al., 2018, Acta Neuropathol Commun; see Fig. 4a and 6e), especially when the number of z-stack of confocal images is small. This is presumably because LC neurons are especially enriched with numerous Golgi apparatus and ER (Groves & Wilson, 1980, J Comp Neurol).

In Figure S7, we showed a lower-magnification image of LC and its adjacent area (mesencephalic trigeminal nucleus). In the LC area, there are a variety of LC neurons, which include oval shaped neurons (open arrowhead; similar to Figure 3D) and also rhombus-like shaped neurons (open double arrowheads, similar to Figure 3E). A much lower-magnification image of LC neurons constituting LC nucleus was shown in Figure 5A.

(6) In Figure 5, the difference in MAO-A expression is not clearly visible in the fluorescence images. Enzymatic assays for AEP and MAO-A should be included to demonstrate the increased activity better.

In the current study, we did not elaborate to detect the changes in TH, MAO-A and AEP in terms of immunohistochemical method. Instead, we elaborated to detect such changes in terms of western blot method. The main conclusions in the current study were drawn primarily by electrophysiological techniques as we have expended much effort on electrophysiological experiments. Because the relative quantification of active AEP and Tau N368 proteins by western blotting analysis may accurately reflect changes in those enzyme activities, enzymatic assay may not be necessarily required but is helpful to better demonstrate AEP and MAO-A activity. We have described the necessity of enzymatic assay to better demonstrate the AEP and MAO-A activities (page 10, lines 314-315).

Reviewer #3 (Recommendations for the authors):

(1) Causality across the pathway

Each step (α2A internalisation, GIRK rundown, Ca²⁺ rise, MAO-A/AEP upregulation) is demonstrated separately, but no experiment links them in a single preparation. Consider in vivo Ca²⁺ or GRAB NE photometry during restraint stress while probing α2A levels with i.p. clonidine injection or optogenetic over excitation coupled to biochemical readouts. Such integrated evidence would help to overcome the correlational nature of the manuscript to a more mechanistic study.

It is not possible to measure free cytosolic NA levels with GRAB NE photometry when α2A AR is internalized as described above (see the response to the comment made by reviewer #1 as the recommendation for the authors).

(2) Pharmacology and NE concentration

The use of 100 µM noradrenaline saturates α and β adrenergic receptors alike. Please provide ramp measurements of GIRK current in dose-response at 1-10 µM NE (blocked by atipamezole) to confirm that the rundown really reflects α2A activity rather than mixed receptor effects.

It is true that 100 µM noradrenaline activates both α and β adrenergic receptors alike. However, it was clearly showed that enhancement of GIRK-I by 100 µM noradrenaline was completely antagonized by 10 µM atipamezole and the Ca²⁺ dependent rundown of NA-induced GIRK-I was prevented by 10 µM atipamezole. Considering the Ki values of atipamezole for α2A AR (=1~3 nM) (Vacher et al., 2010, J Med Chem) and β AR (>10 µM) (Virtanen et al., 1989, Arch Int Pharmacodyn Ther), these results really reflect α2A AR activity but not β AR activity (Figure S5). Furthermore, because it is already well established that NA-induced GIRK-I was mediated by α2A AR activity in LC neurons (Arima et al., 1998, J Physiol; Williams et al., 1985, Neuroscience), it is not necessarily need to re-examine 1-10 µM NA on GIRK-I.

(3) Calcium dependence is not yet definitive

The rundown is induced with a TEA-enhanced pulse protocol. Blocking L-type channels with nifedipine (or using Cd²⁺) during this protocol should show whether Ca²⁺ entry is necessary. Without such a control, the Ca²⁺ link remains inferential.

The Ca²⁺ link was precisely demonstrated by a series of voltage clamp experiment, in which Ca²⁺ influx was orderly potentiated by increasing the number of positive voltage pulses (Figures S1 and S2). As the number of positive voltage pulses was increased, the rundown of GIRK-I was accelerated or enhanced more. The relationship between the number of spikes and the Ca²⁺ influx detected as Ca²⁺ transients was well documented in Ca2+ imaging experiments using fura-2 (Figure S3).

The presence or absence of Ca²⁺ currents and the amount of Ca²⁺ currents determined the trend of the rundown of GIRK-I (Figs. 2, S1 and S2). The same voltage protocol hardly caused the rundown when it did not induce Ca²⁺ currents in the absence of TEA (Fig. S1F; compare with Fig. 2B), and the series of voltage-clamp protocols convincingly demonstrated the orderly involvement of [Ca²⁺]_i in accelerating the rundown of GIRK-I. Therefore, blockade of Ca²⁺ currents by nifedipine may not be so beneficial.

(4) Age mismatch and disease claims

All electrophysiology and biochemical data come from juvenile (< P30) mice, yet the conclusions stress Alzheimer-related degeneration. Key endpoints need to be replicated in adult or aged mice, or the manuscript should soften its neurodegenerative scope.

As described in the section of Conclusion, we never stress Alzheimer-related degeneration, but might give such an impression. To avoid such a misunderstanding, we have added a description “However, the present mechanism must be proven to be valid in adult or old mice, to validate its involvement in the pathogenesis of AD.” (page 14, lines 448-450).

(5) Direct evidence for extracellular/cytosolic NE

The proposed rise in reuptake NA is inferred from electrophysiology. Modern fluorescent sensors (GRAB NE, nLight) or fast scan voltammetry could quantify NE overflow and clearance during stress, directly testing the model.

Please see the response to the comment made by Reviewer #1 as the Recommendations for the authors (2) as described above.

(6) Quantitative histology

Figure 5 presents attractive images but no numerical analysis. Please provide ROI-based fluorescence quantification (with n values) or move the images to the supplement and rely on the Western blots.

We have moved the immunohistochemical results in Fig. 5 to the supplement as we believe the quantification of immunohistochemical staining is not necessarily correct.

eLife Assessment

This study examines a valuable question regarding the developmental trajectory of neural mechanisms supporting facial expression processing. Leveraging a rare intracranial EEG (iEEG) dataset including both children and adults, the authors reported that facial expression recognition mainly engaged the posterior superior temporal cortex (pSTC) among children, while both pSTC and the prefrontal cortex were engaged among adults. However, the sample size is relatively small, with analyses appearing incomplete to fully support the primary claims.

Reviewer #1 (Public review):

Summary:

This study investigates how the brain processes facial expressions across development by analyzing intracranial EEG (iEEG) data from children (ages 5-10) and post-childhood individuals (ages 13-55). The researchers used a short film containing emotional facial expressions and applied AI-based models to decode brain responses to facial emotions. They found that in children, facial emotion information is represented primarily in the posterior superior temporal cortex (pSTC) - a sensory processing area - but not in the dorsolateral prefrontal cortex (DLPFC), which is involved in higher-level social cognition. In contrast, post-childhood individuals showed emotion encoding in both regions. Importantly, the complexity of emotions encoded in the pSTC increased with age, particularly for socially nuanced emotions like embarrassment, guilt, and pride. The authors claim that these findings suggest that emotion recognition matures through increasing involvement of the prefrontal cortex, supporting a developmental trajectory where top-down modulation enhances understanding of complex emotions as children grow older.

Strengths:

(1) The inclusion of pediatric iEEG makes this study uniquely positioned to offer high-resolution temporal and spatial insights into neural development compared to non-invasive approaches, e.g., fMRI, scalp EEG, etc.

(2) Using a naturalistic film paradigm enhances ecological validity compared to static image tasks often used in emotion studies.

(3) The idea of using state-of-the-art AI models to extract facial emotion features allows for high-dimensional and dynamic emotion labeling in real time.

Weaknesses:

The study has notable limitations that constrain the generalizability and depth of its conclusions. The sample size was very small, with only nine children included and just two having sufficient electrode coverage in the posterior superior temporal cortex (pSTC), which weakens the reliability and statistical power of the findings, especially for analyses involving age. Electrode coverage was also uneven across brain regions, with not all participants having electrodes in both the dorsolateral prefrontal cortex (DLPFC) and pSTC, and most coverage limited to the left hemisphere-hindering within-subject comparisons and limiting insights into lateralization. The developmental differences observed were based on cross-sectional comparisons rather than longitudinal data, reducing the ability to draw causal conclusions about developmental trajectories. Moreover, the analysis focused narrowly on DLPFC, neglecting other relevant prefrontal areas such as the orbitofrontal cortex (OFC) and anterior cingulate cortex (ACC), which play key roles in emotion and social processing. Although the use of a naturalistic film stimulus enhances ecological validity, it comes at the cost of experimental control, with no behavioral confirmation of the emotions perceived by participants and uncertain model validity for complex emotional expressions in children. A non-facial music block that could have served as a control was available but not analyzed. Generalizability is further limited by the fact that all participants were neurosurgical patients, potentially with neurological conditions such as epilepsy that may influence brain responses. Additionally, the high temporal resolution of intracranial EEG was not fully utilized, as data were downsampled and averaged in 500-ms windows. Finally, the absence of behavioral measures or eye-tracking data makes it difficult to directly link neural activity to emotional understanding or determine which facial features participants attended to.

Reviewer #2 (Public review):

Summary:

In this paper, Fan et al. aim to characterize how neural representations of facial emotions evolve from childhood to adulthood. Using intracranial EEG recordings from participants aged 5 to 55, the authors assess the encoding of emotional content in high-level cortical regions. They report that while both the posterior superior temporal cortex (pSTC) and dorsolateral prefrontal cortex (DLPFC) are involved in representing facial emotions in older individuals, only the pSTC shows significant encoding in children. Moreover, the encoding of complex emotions in the pSTC appears to strengthen with age. These findings lead the authors to suggest that young children rely more on low-level sensory areas and propose a developmental shift from reliance on lower-level sensory areas in early childhood to increased top-down modulation by the prefrontal cortex as individuals mature.

Strengths:

(1) Rare and valuable dataset: The use of intracranial EEG recordings in a developmental sample is highly unusual and provides a unique opportunity to investigate neural dynamics with both high spatial and temporal resolution.

(2) Developmentally relevant design: The broad age range and cross-sectional design are well-suited to explore age-related changes in neural representations.

(3) Ecological validity: The use of naturalistic stimuli (movie clips) increases the ecological relevance of the findings.

(4) Feature-based analysis: The authors employ AI-based tools to extract emotion-related features from naturalistic stimuli, which enables a data-driven approach to decoding neural representations of emotional content. This method allows for a more fine-grained analysis of emotion processing beyond traditional categorical labels.

Weaknesses:

(1) The emotional stimuli included facial expressions embedded in speech or music, making it difficult to isolate neural responses to facial emotion per se from those related to speech content or music-induced emotion.

(2) While the authors leveraged Hume AI to extract facial expression features from the video stimuli, they did not provide any validation of the tool's accuracy or reliability in the context of their dataset. It remains unclear how well the AI-derived emotion ratings align with human perception, particularly given the complexity and variability of naturalistic stimuli. Without such validation, it is difficult to assess the interpretability and robustness of the decoding results based on these features.

(3) Only two children had relevant pSTC coverage, severely limiting the reliability and generalizability of results.

(4) The rationale for focusing exclusively on high-frequency activity for decoding emotion representations is not provided, nor are results from other frequency bands explored.

(5) The hypothesis of developmental emergence of top-down prefrontal modulation is not directly tested. No connectivity or co-activation analyses are reported, and the number of participants with simultaneous coverage of pSTC and DLPFC is not specified.

(6) The "post-childhood" group spans ages 13-55, conflating adolescence, young adulthood, and middle age. Developmental conclusions would benefit from finer age stratification.

(7) The so-called "complex emotions" (e.g., embarrassment, pride, guilt, interest) used in the study often require contextual information, such as speech or narrative cues, for accurate interpretation, and are not typically discernible from facial expressions alone. As such, the observed age-related increase in neural encoding of these emotions may reflect not solely the maturation of facial emotion perception, but rather the development of integrative processing that combines facial, linguistic, and contextual cues. This raises the possibility that the reported effects are driven in part by language comprehension or broader social-cognitive integration, rather than by changes in facial expression processing per se.

eLife Assessment

This work presents a useful investigation of functional and structural brain changes following navigation and verbal memory training. The analyses of whole-brain structural changes are incomplete and would benefit from a more comprehensive approach to support the study's main conclusion regarding the lack of a structural whole-brain plasticity effect. However, some analyses are exhaustive and compelling in demonstrating the presence of longitudinal behavioural effects, the presence of functional activation changes, and the lack of hippocampal volume changes.

Joint Public Review:

Summary:

This study investigates plasticity effects in brain function and structure from training in navigation and verbal memory.

The authors used a longitudinal design with a total of 75 participants across two sites. Participants were randomised to one of three conditions: verbal memory training, navigation training, or a video control condition. The results show behavioural effects in relevant tasks following the training interventions. The central claim of the paper is that network-based measures of task-based activation are affected by the training interventions, but structural brain metrics (T2w-derived volume and diffusion-weighted imaging microstructure) are not impacted by any of the training protocols tested.

Strengths:

(1) This is a well-designed study which uses two training conditions, an active control, and randomisation, as appropriate. It is also notable that the authors combined data acquisition across two sites to reach the needed sample size and accounted for it in their statistical analyses quite thoroughly. In addition, I commend the authors on using pre-registration of the analysis to enhance the reproducibility of their work.

(2) Some analyses in the paper are exhaustive and compelling in showcasing the presence of longitudinal behavioural effects, functional activation changes, and lack of hippocampal volume changes. The breadth of analysis on hippocampal volume (including hippocampal subfields) is convincing in supporting the claim regarding a lack of volumetric effect in the hippocampus.

Weaknesses:

(1) The rationale for the study and its relationship with previous literature is not fully clear from the paper. In particular, there is a very large literature that has already explored the longitudinal effects of different types of training on functional and structural neuroimaging. However, this literature is barely acknowledged in the Introduction, which focuses on cross-sectional studies. Studies like the one by Draganski et al. 2004 are cited but not discussed, and are clumped together with cross-sectional studies, which is confusing. As a reader, it is difficult to understand whether the study was meant to be confirmatory based on previous literature, or whether it fills a specific gap in the literature on longitudinal neuroimaging effects of training interventions.

(2) The main claim regarding the lack of changes in brain structure seems only partially supported by the analyses provided. The limited whole-brain evidence from structural neuroimaging makes it difficult to confirm whether there is indeed no effect of training. Beyond hippocampal analyses, many whole-brain analyses of both volumetric and diffusion-weighted imaging metrics are only based on coarse ROIs (for example, 34 cortical parcellations for grey matter analyses). Although vertex-wise analyses in FreeSurfer are reported, it is unclear what metrics were examined (cortical thickness? area? volume?). Diffusion-weighted imaging seems to focus on whole-tract atlas ROIs, which can be less accurate/sensitive than tractography-defined ROIs or voxel-wise approaches.

(3) Quality control of images is only mentioned for FA images in subject space. Given that most analyses are based on atlas ROIs, visual checks following registration are fundamental and should be described in further detail.

eLife Assessment

This important study fills a gap in our knowledge of the evolution of GPCRs in holozoans, as well as the phylogeny of associated signaling pathway components such as G proteins, GRKs, and RIC8 proteins. The evidence supporting the conclusions is compelling, with the analysis of extensive new genomic data from choanoflagellates and other non-animal holozoans. Overall, the study is thorough and well-executed. It will be a resource for researchers interested in both the comparative genomics of multicellularity and GPCR biology more broadly, especially given the importance of GPCRs as highly druggable targets.

Reviewer #1 (Public review):

Summary:<br /> The authors strived for an inventory of GPCRs and GPCR pathway component genes within the genomes of 23 choanoflagellates and other close relatives of metazoans.

Strengths:<br /> The authors generated a solid phylogenetic overview of the GPCR superfamily in these species. Intriguingly, they discover novel GPCR families, novel assortments of domain combinations, novel insights into the evolution of those groups within the Opisthokonta clade. A particular focus is laid on adhesion GPCRs, for which the authors discover many hitherto unknown subfamilies based on Hidden Markov Models of the 7TM domain sequences, which were also reflected by combinations of extracellular domains of the homologs. In addition, the authors provide bioinformatic evidence that aGPCRs of choanoflagellates also contained a GAIN domain, which are self-cleavable thereby reflecting the most remarkable biochemical feat of aGPCRs.

Weaknesses:<br /> The chosen classification scheme for aGPCRs may require reassessment and amendment by the authors in order to prevent confusion with previously issued classification attempts of this family.

Reviewer #2 (Public review):

Summary:<br /> The authors set out to characterise the GPCR family in choanoflagellates (and other unicellular holozoans). GPCRs are the most abundant gene family in many animal genomes, playing crucial roles in a wide range of physiological processes. Although they are known to evolve rapidly, GPCRs are an ancient feature of eukaryotic biology. Identifying conserved elements across the animal-protist boundary is therefore a valuable goal, and the increasing availability of genomes from non-animal holozoans provides new opportunities to explore evolutionary patterns that were previously obscured by limited taxon sampling. This study presents a comprehensive re-examination of GPCRs in choanoflagellates, uncovering examples of differential gene retention and revealing the dynamic nature of the GPCR repertoire in this group. As GPCRs are typically involved in environmental sensing, understanding how these systems evolved may shed light on how our unicellular ancestors adapted their signalling networks in the transition to complex multicellularity.

Strengths:<br /> The paper combines a broad taxonomic scope with the use of both established and recently developed tools (e.g. Foldseek, AlphaFold), enabling a deep and systematic exploration of GPCR diversity. Each family is carefully described, and the manuscript also functions as an up-to-date review of GPCR classification and evolution. Although similar attempts of understanding GPCR evolution were done over the last decade, the authors build on this foundation by identifying new families and applying improved computational methods to better predict structure and function. Notably, the presence of Rhodopsin-like GPCRs in some choanoflagellates and ichthyosporeans is intriguing, even though they do not fall within known animal subfamilies. The computational framework presented here is broadly applicable, offering a blueprint for surveying GPCR diversity in other non-model eukaryotes (and even in animal lineages), potentially revealing novel families relevant to drug discovery or helping revise our understanding of GPCR evolution beyond model systems.

Weaknesses:<br /> While the study contributes several interesting observations, it does not radically revise the evolutionary history of the GPCR family. However, in an era increasingly concerned with the reproducibility of scientific findings, this is arguably a strength rather than a weakness. It is encouraging to see that previously established patterns largely hold, and that with expanded sampling and improved methods, new insights can be gained-especially at the level of specific GPCR subfamilies. Then, no functional follow ups are provided in the model system Salpingoeca rosetta, but I am sure functional work on GPCRs in choanoflagellates is set to reveal very interesting molecular adaptations in the future.

Comments on the latest version:

The authors have done a good job answering my questions and suggestions.

eLife Assessment

This valuable study tested the impact of DNA methylation on CTCF binding in two cancer cell lines. Increased CTCF binding sites are enriched in gene bodies, and associate with nuclear speckles, indicating a role in increased transcription. In the revised work, the inferred association with nuclear speckles has been supported with more solid data. These results will be of interest to the epigenetics field.

Reviewer #2 (Public review):

Summary:

CTCF is one of the most well-characterized regulators of chromatin architecture in mammals. Given that CTCF is an essential protein, understanding how its binding is regulated is a very active area of research. It has been known for decades that CTCF is sensitive to 5-cystosine DNA methylation (5meC) in certain contexts. Moreover, at genomic imprints and in certain oncogenes, 5meC-mediated CTCF antagonism has very important gene regulatory implications. A number of labs (eg, Schubeler and Stamatoyannopoulos) have assessed the impact of DNA methylation on CTCF binding, but it is important to also interrogate the effect on chromatin organization (ie, looping). Here, Roseman and colleagues used a DNMT1 inhibitor in two established human cancer lines (HCT116 [colon] and K562 [leukemia]), and performed CTCF ChIPseq and HiChIP. They showed that "reactivated" CTCF sites-that is, bound in the absence of 5meC-are enriched in gene bodies, participate in many looping events, and intriguingly, appear associated with nuclear speckles. This last aspect suggests that these reactivated loops might play an important role in increased gene transcription. They showed a number of genes that are upregulated in the DNA hypomethylated state actually require CTCF binding, which is an important result.

Strengths:

Overall, I found the paper to be succinctly written and the data presented clearly. The relationship between CTCF binding in gene bodies and association with nuclear speckles is an interesting result. Another strong point of the paper was combining DNMT1 inhibition with CTCF degradation.

Weaknesses:

The most problematic aspect of the original version was the insufficient evidence for the association of "reactivated" CTCF binding sites with nuclear speckles. This has been more diligently assessed in the revised version.

Comments on revisions:

The authors have adequately addressed my points in this revised version.

eLife Assessment

This important study investigates changes in oscillatory activity across cortical and subcortical areas during stroke recovery in a nonhuman primate model. The authors distinguish between global and local oscillatory bursts, providing solid evidence that these two types of bursts correlate with distinct aspects of movement; additionally, they show that the likelihood of these bursts occurring follows opposing trends during recovery. The study could be further improved by accounting for inter-individual differences and by some technical improvements, such as employing more robust burst detection methods and more stringent analyses.

Reviewer #1 (Public review):

Summary:

This manuscript investigates beta burst dynamics in the primate motor cortex during movement and recovery from stroke. The authors differentiate between "global" beta bursts, which are synchronous across cortical and often subcortical regions, and more spatially confined "local" bursts. Global bursts are associated with reduced spiking variability, slower movements, and are more frequent after stroke, while local bursts increase during recovery and grasp execution. The study provides compelling evidence that beta bursts with different spatial and temporal characteristics may play distinct roles in motor control and recovery.

Strengths:

The major strength of this paper lies in its conceptual advance: the identification and characterization of distinct global and local beta bursts in the primate motor cortex. This distinction builds upon and considerably extends previous work on the heterogeneity of beta bursts. The paper is methodologically rigorous, using simultaneous cortical and subcortical recordings, detailed behavioral tracking, and thorough analyses of spike-LFP interactions. The use of stroke models and neurotypical animals provides converging evidence for the functional dissociation between burst types. The observation that local bursts increase with motor recovery and occur during grasping is particularly novel and may prove valuable for developing biomarkers of motor function.

Weaknesses:

There are several conceptual and methodological limitations that should be addressed. First, the burst detection method relies on an amplitude threshold (median + 1 SD), which is susceptible to false positives and variability (Langford & Wilson, 2025). The classification into global or local bursts then depends on the number of co-bursting channels, compounding the arbitrariness. Second, the imposition of a minimum of three co-bursting cortical channels may bias against the detection of truly local bursts. Third, the classification is entirely cortical; subcortical activity is considered post hoc rather than integrated into the classification, despite the key role of subcortical-cortical synchrony in motor control. Fourth, the apparent dissociation between global and local bursts raises important questions about their spatial distribution across areas like M1 and PMv, which are not thoroughly analyzed. Finally, while the authors interpret local bursts during grasping as novel, similar findings have been reported (e.g., Szul et al., 2023; Rayson et al., 2023), and a deeper discussion of these precedents would strengthen the argument.

Impact:

This work is likely to have a substantial impact on the field of motor systems neuroscience. The distinction between global and local beta bursts offers a promising framework for understanding the dual roles of beta in motor inhibition and sensorimotor computation. The findings are relevant not only for basic research but also for translational efforts in stroke rehabilitation and neuromodulation, particularly given the emerging interest in beta burst-based biomarkers and stimulation targets. The dataset and analytical framework will be useful to researchers investigating beta dynamics, spike-field relationships, and recovery from neural injury.

Langford, Z.D., Wilson, C.R.E., 2025. Simulations reveal that beta burst detection may inappropriately characterize the beta band. https://doi.org/10.1101/2023.12.15.571838.

Rayson, H., Szul, M.J., El-Khoueiry, P., Debnath, R., Gautier-Martins, M., Ferrari, P.F., Fox, N., Bonaiuto, J.J., 2023. Bursting with potential: How sensorimotor beta bursts develop from infancy to adulthood. J. Neurosci. https://doi.org/10.1523/JNEUROSCI.0886-23.2023.

Szul, M.J., Papadopoulos, S., Alavizadeh, S., Daligaut, S., Schwartz, D., Mattout, J., Bonaiuto, J.J., 2023. Diverse beta burst waveform motifs characterize movement-related cortical dynamics. Prog. Neurobiol. 228, 102490.

Reviewer #2 (Public review):

Summary:

The paper by Khanna et al. describes global vs local beta synchrony between a cortical premotor area (PMv) and subcortical structures during motor tasks in the non-human primate, specifically investigating the progression following M1 injury. They found that increases in global beta synchrony between PMv and subcortical structures during the sub-acute phase of injury, and that global synchrony was associated with relatively slower motor movements. As recovery progressed, they report a shift from global synchrony to local synchrony and a subsequent reduction in the movement time. The authors suggest that global changes in subcortical and cortical beta synchrony may generally underpin a variety of movement disorders, including Parkinson's disease, and that shifting from global to local (or reducing global synchrony) might improve functional outcomes.

Strengths:

Ischemic insults and other acquired brain injuries have a significant public health impact. While there is a large body of clinical and basic science studies describing the behavioral, neurophysiological, and mechanistic outcomes of such injury, there is a significant lack studies looking at longitudinal, behaviorally-related neurophysiological measures following cortical injury, so any information has outsized contribution to understanding how brain injury disrupts underlying neural activity and how this may contribute to injury presentation and recovery.

A significant percentage of pre-clinical stroke studies tend to focus on peri-infarct or other cortical structures and their role in recovery. The addition of subcortical recordings allows for the investigation of the role of thalamo-basal gangliar-cortical loops that may be contributing to the degree of impairment or to the recovery process is important for the field. Here, there are longitudinal (up to 3 months post-injury) recordings in the ventral premotor area (PMv) and either the internal capsule or sensorimotor thalamus that can be synchronized with phases of behavioral recovery.

The methods are well described and can act as a framework for assessing synchrony across other data sets with similar recording locations. Limitations in methodology, recordings, and behavior were noted.

Weaknesses:

A major limitation of this paper is that it is a set of case studies rather than a well-designed, well-controlled study of beta synchrony following motor cortex injury. While non-human primate neurophysiological studies are almost always limited by extremely low animal numbers, they are made up for by the fact that they can acquire significant numbers of units or channels, and in the case of normal behavior, can obtain many behavioral trials over months of individual sessions. Here, there were two NHPs used, but they had different subcortical implant locations (thalamus vs internal capsule). They had different injury outcomes, with one showing a typical recovery curve following injury while one had complications and worsening behavior before ultimately recovering. Further, there were significant differences in the ability to record at different times, with one NHP having poor recordings early in the recovery process while one had poor recordings late in the process. Due to the injury, the authors report sessions in which they were not able to record many trials (~10). Assuming that recovery after a cortical injury is an evolving process, breaking analysis into "Early" and "Late" phases reduces the interpretation of where these shifts occur relative to recovery on the task, especially given different thresholds for recovery were used between animals. Because of this, despite a careful analysis of the data and an extensive discussion, the conclusions derived are not particularly compelling. To overcome this, the authors present data from neurotypical NHPs, but with electrodes in M1 rather than PMv, doing a completely different task with no grasping component, again making accurate conclusions about the results difficult. Even with low numbers, the study would have been much stronger if there were within-animal longitudinal data prior to and after the injury on the same task, so the impact of M1 injury could be better assessed.

It is unclear to what extent the subpial aspiration used is a stroke model. While it is much more difficult to perform a pure ischemic motor injury using electrocoagulatory methods in animal models that do not have a lissencephalic cortex, the suction ablation method that the authors use leads to different outcomes than an ischemic injury alone. For instance, in rat models, ischemic vs suction ablation leads to very different electrophysiological profiles and differences in underlying anatomical reorganization (see Carmichael and Chesselet, 2002), even if the behavioral outcomes were similar. There is a concern that the effects shown may be an artifact of the lesion model rather than informing underlying mechanisms of recovery.

The injury model leads to seemingly mild impairments in grasp (but not reach), with rapid and complete recovery occurring within 2-3 weeks from the time of injury. Because of the rapid recovery, relating the physiological processes of recovery to beta synchronization becomes challenging to interpret - Are the global bursts the result of the loss of M1 input to subcortical structures? Are they due to the lack of M1 targets, so there is a more distributed response? Is this due to other post-injury sub-acute mechanisms? How specific is this response - is it limited to peri-infarct areas (and to what extent is the PMv electrode truly in peri-infarct cortex), or would this synchrony be seen anywhere in the sensorimotor networks? Are the local bursts present because global synchrony wanes over time as a function of post-injury homeostatic mechanisms, or is local beta synchrony increasing as new motor plans are refined and reinforced during task re-acquisition? How coupled are they related to recovery - if it is motor plan refinement, the shift from global to local seemingly should lag the recovery? While the study has significant limitations in design that reduce the impact of the results, it should act as a useful baseline/pilot data set in which to build a more complete picture of the role of subcortical-cortical beta synchrony following cortical injury.

Reviewer #3 (Public review):

Summary:

Khanna et al. use a well-conceived and well-executed set of experiments and analyses primarily to document the interaction between neural oscillations in the beta range (here, 13-30 Hz) and recovery of function in an animal model of stroke. Specifically, they show that cortical "beta bursts", or short-term increases in beta power, correlate strikingly with the timeline of behavioral recovery as quantified with a reach-to-grasp task. A key distinction is made between global beta bursts (here, those that synchronize between cortical and subcortical areas) and local bursts (which appear on only a few electrodes). This distinction of global vs. local is shown to be relevant to task performance and movement speed, among other quantities of interest.

A secondary results section explores the relationship between beta bursts and neuronal firing during the grasp portion of the behavioral task. These results are valuable to include, though mostly unsurprising, with global beta in particular associated with lower mean and variance in spike rates.

Last, a partial recapitulation of the primary results is offered with a neurologically intact (uninjured) animal. No major contradictions are found with the primary results.

Highlights of the Discussion section include a thoughtful review of atypical movements executed by individuals with Parkinson's disease or stroke survivors, placing the current results in an appropriate clinical context. Potential physiological mechanisms that could account for the observed results are also discussed effectively.

Strengths:

Overall, this is a very interesting paper. The ultimate impact will be enhanced by the authors' choice to analyze beta bursts, which remain a relatively under-explored aspect of neural coding.

The reach-and-grasp task was also a well-considered choice; the combination of a relatively simple movement (reaching towards a target in the same location each time) and a more complex movement (a skilled object-manipulation grasp) provides an internal control of sorts for data analysis. In addition, the task's two sub-movements provide a differential in terms of their likelihood to be affected by the stroke-like injury: proximal muscles (controlling reach) are likely to be less affected by stroke, while distal muscles (controlling grasp) are highly likely to be affected. Lastly, the requirement of the task to execute an object lift maximizes its difficulty and also the potential translational impact of the results on human injury.

The above comments about the task exemplify a strength that is more generally evident: a welcome awareness of clinical relevance, which is in evidence several times throughout the Results and Discussion.

Weaknesses:

The study's weaknesses are mostly minor and, for the most part, correctable.

One concern that may not be correctable in this study: the results about the spatial extent of beta activity seem constrained by relatively poor-quality data. It seems half or more of the electrodes are marked as too noisy to provide useful data in Figure 3. If this reflects the wider reality for all analyses, as mentioned, it may not be correctable for the present study. In that case, perhaps some of the experiments or analyses can be revisited or expanded for a future study, when better electrode yields are available.

Other concerns:

In some places, there is a lack of clarity in the presentation of the results. This is not serious but should be addressed to aid readers' comprehension.

Lastly, given the central role of beta oscillations within the study, it would be better for completeness to include even a brief exploration of sustained beta power (rather than bursts), and the modulation of sustained beta (or lack thereof) in the study's areas of concern: behavioral recovery, task performance, etc.

Author response:

Reviewer #1 (Public review):

Summary:

This manuscript investigates beta burst dynamics in the primate motor cortex during movement and recovery from stroke. The authors differentiate between "global" beta bursts, which are synchronous across cortical and often subcortical regions, and more spatially confined "local" bursts. Global bursts are associated with reduced spiking variability, slower movements, and are more frequent after stroke, while local bursts increase during recovery and grasp execution. The study provides compelling evidence that beta bursts with different spatial and temporal characteristics may play distinct roles in motor control and recovery.

We thank the reviewer for their assessment that the manuscript proves compelling evidence for distinct roles of local and global beta bursts on motor control and recovery.  

Strengths:

The major strength of this paper lies in its conceptual advance: the identification and characterization of distinct global and local beta bursts in the primate motor cortex. This distinction builds upon and considerably extends previous work on the heterogeneity of beta bursts. The paper is methodologically rigorous, using simultaneous cortical and subcortical recordings, detailed behavioral tracking, and thorough analyses of spikeLFP interactions. The use of stroke models and neurotypical animals provides converging evidence for the functional dissociation between burst types. The observation that local bursts increase with motor recovery and occur during grasping is particularly novel and may prove valuable for developing biomarkers of motor function.

We thank the reviewer for recognizing the strengths of this manuscript. 

Weaknesses:

There are several conceptual and methodological limitations that should be addressed. First, the burst detection method relies on an amplitude threshold (median + 1 SD), which is susceptible to false positives and variability (Langford & Wilson, 2025). The classification into global or local bursts then depends on the number of co-bursting channels, compounding the arbitrariness. Second, the imposition of a minimum of three co-bursting cortical channels may bias against the detection of truly local bursts. 

We thank the reviewer for bringing up these methodological details. We plan to conduct a follow-up analysis using alternative burst detection methods to verify that the paper’s main results hold when using different burst detection methodologies. We anticipate this will improve confidence in our results. 

Third, the classification is entirely cortical; subcortical activity is considered post hoc rather than integrated into the classification, despite the key role of subcortical-cortical synchrony in motor control. 

We thank the reviewer for this comment. First, because the different animals had subcortical recording sites in different locations, we hesitate to use subcortical activity in the classification of bursts since we were not sure we would be identifying the same burst-phenomenon (e.g. thalamo-cortical bursts vs. capsule-cortical bursts may differ). Second, we believe that having a cortical-only criteria allows the designation of local vs. global bursts to be more widely applied in preparations that only have access to cortical data (e.g. surface ECoG recordings, EEG, Utah array recordings). Thus, in this study we chose to analyze the subcortical data post-hoc (after burst detection and classification) to support our “global” vs. “local” designation of burst types 

Fourth, the apparent dissociation between global and local bursts raises important questions about their spatial distribution across areas like M1 and PMv, which are not thoroughly analyzed. 

We thank the reviewer for this comment. In our study’s stroke animals, we chose to study PMv due to its role in compensating for damage to M1, thus we hesitate to make any comparisons between PMv (which was recorded in stroke animals) and M1 (recorded in healthy unimpaired animals). Furthermore, animals are doing different tasks (e.g. reaching vs. reaching and grasping) which may also influence the spatial distribution. We agree that future work should certainly investigate the spatial distribution of global vs. local beta bursts across areas of sensorimotor cortex and subcortex, and that this comparison would be best done in healthy animals with both reaching and grasping behaviors.  

Finally, while the authors interpret local bursts during grasping as novel, similar findings have been reported (e.g., Szul et al., 2023; Rayson et al., 2023), and a deeper discussion of these precedents would strengthen the argument.

Thank you for these references! We will review them and incorporate them into our discussion of our results. 

Impact:

This work is likely to have a substantial impact on the field of motor systems neuroscience. The distinction between global and local beta bursts offers a promising framework for understanding the dual roles of beta in motor inhibition and sensorimotor computation. The findings are relevant not only for basic research but also for translational efforts in stroke rehabilitation and neuromodulation, particularly given the emerging interest in beta burst-based biomarkers and stimulation targets. The dataset and analytical framework will be useful to researchers investigating beta dynamics, spike-field relationships, and recovery from neural injury.

We thank the reviewers for their assessment that our work will likely have a substantial impact on the field of motor systems neuroscience. 

Reviewer #2 (Public review):

Summary:

The paper by Khanna et al. describes global vs local beta synchrony between a cortical premotor area (PMv) and subcortical structures during motor tasks in the non-human primate, specifically investigating the progression following M1 injury. They found that increases in global beta synchrony between PMv and subcortical structures during the sub-acute phase of injury, and that global synchrony was associated with relatively slower motor movements. As recovery progressed, they report a shift from global synchrony to local synchrony and a subsequent reduction in the movement time. The authors suggest that global changes in subcortical and cortical beta synchrony may generally underpin a variety of movement disorders, including Parkinson's disease, and that shifting from global to local (or reducing global synchrony) might improve functional outcomes.

Strengths:

Ischemic insults and other acquired brain injuries have a significant public health impact. While there is a large body of clinical and basic science studies describing the behavioral, neurophysiological, and mechanistic outcomes of such injury, there is a significant lack studies looking at longitudinal, behaviorally-related neurophysiological measures following cortical injury, so any information has outsized contribution to understanding how brain injury disrupts underlying neural activity and how this may contribute to injury presentation and recovery.

A significant percentage of pre-clinical stroke studies tend to focus on peri-infarct or other cortical structures and their role in recovery. The addition of subcortical recordings allows for the investigation of the role of thalamo-basal gangliar-cortical loops that may be contributing to the degree of impairment or to the recovery process is important for the field. Here, there are longitudinal (up to 3 months post-injury) recordings in the ventral premotor area (PMv) and either the internal capsule or sensorimotor thalamus that can be synchronized with phases of behavioral recovery.

The methods are well described and can act as a framework for assessing synchrony across other data sets with similar recording locations. Limitations in methodology, recordings, and behavior were noted.

We thank the reviewer for their comments on the strengths of this paper.  

Weaknesses:

A major limitation of this paper is that it is a set of case studies rather than a welldesigned, well-controlled study of beta synchrony following motor cortex injury. While non-human primate neurophysiological studies are almost always limited by extremely low animal numbers, they are made up for by the fact that they can acquire significant numbers of units or channels, and in the case of normal behavior, can obtain many behavioral trials over months of individual sessions. Here, there were two NHPs used, but they had different subcortical implant locations (thalamus vs internal capsule). They had different injury outcomes, with one showing a typical recovery curve following injury while one had complications and worsening behavior before ultimately recovering. Further, there were significant differences in the ability to record at different times, with one NHP having poor recordings early in the recovery process while one had poor recordings late in the process. Due to the injury, the authors report sessions in which they were not able to record many trials (~10). Assuming that recovery after a cortical injury is an evolving process, breaking analysis into "Early" and "Late" phases reduces the interpretation of where these shifts occur relative to recovery on the task, especially given different thresholds for recovery were used between animals. Because of this, despite a careful analysis of the data and an extensive discussion, the conclusions derived are not particularly compelling. To overcome this, the authors present data from neurotypical NHPs, but with electrodes in M1 rather than PMv, doing a completely different task with no grasping component, again making accurate conclusions about the results difficult. Even with low numbers, the study would have been much stronger if there were within-animal longitudinal data prior to and after the injury on the same task, so the impact of M1 injury could be better assessed.

We thank the reviewer for these comments. Below we address some of these in more detail: 

Different subcortical implant locations: We would like to clarify that the subcortical recordings were only used to confirm that global beta bursts (as characterized by cortical recordings alone) did indeed occur on subcortical sites coincidentally with cortical site more frequently than local beta bursts. Neither the beta burst categories nor the beta bursts themselves were influenced by the subcortical recordings.  

Different injury outcomes: There is difficulty in creating strokes that result in identical deficits across animal as we and others have noted in previous work[1.3]. As a field, we are still understanding what factors give rise to variability in recovery curves. For example, one recent study noted that biological sex is a factor in predicting differences in recovery rates[4], and another noted that baseline white matter hyperintensities is also predictive of post-stroke recovery [5]. Overall, our methodology that creates structurally-consistent lesions can still result in very different functional outcomes depending on a variety of factors. Given this state of the field, we have done our best to match the recovery curves between our two animals, especially the initial recovery curves before Monkey H’s secondary decline. 

Differences in ability to record at different times: We note this as a strength. One concern with these studies that induce stroke at the same time as implanting electrode arrays is that it is well appreciated that single-unit neuron yield right after array implantation is low and then improves in the following weeks [6]. There is always that concern that having more units later in recovery may drive results, but in this case, since one animal showed the opposite trend we are more confident that results are not driven by increases in unit-yield. We also note that we broadly see similar unit quality metrics in the early and late stages in both animals (Fig. S7).  

Breaking continuous recovery curve into early and late: We note that this division was only made for one main analysis in the paper (Fig. 5CD): assessment of mean firing and variance of single-unit firing rates.  Without this split our analyses would be underpowered and inconclusive, thus we would not be able to provide any comment on how firing rates change, even coarsely, with recovery. 

Presentation of data from M1 of healthy animals doing a different task: We agree that the strongest data would be longitudinally recorded from the same animals/brain areas pre-stroke and then post-stroke. However, we also view our inclusion of separate healthy animals doing a different task as evidence that our global vs. local segregation of beta bursts generalizes beyond the reach-to-grasp task to reaching-only tasks.  

Overall, we appreciate the reviewer pointing out these notes about our data. In some cases we do not think these notes are concerning, in others, we acknowledge that have done the best we can given the state of the neurophysiology stroke recovery field. 

It is unclear to what extent the subpial aspiration used is a stroke model. While it is much more difficult to perform a pure ischemic motor injury using electrocoagulatory methods in animal models that do not have a lissencephalic cortex, the suction ablation method that the authors use leads to different outcomes than an ischemic injury alone. For instance, in rat models, ischemic vs suction ablation leads to very different electrophysiological profiles and differences in underlying anatomical reorganization (see Carmichael and Chesselet, 2002), even if the behavioral outcomes were similar. There is a concern that the effects shown may be an artifact of the lesion model rather than informing underlying mechanisms of recovery.

We thank the reviewer for bringing this up. 

Clarification of our stroke model methodology: We wish to highlight that when we create stroke, we first do surface vessel occlusion as the first step. This is designed to match true ischemic injury. After a waiting period, the injured tissue is then aspiration to reduce the effects of edema and secondary mass effect in the model. 

Carmichael and Chesselet 2002: The rodent work cited did show differential effects of a suction ablation method (without any surface vessel occlusion first) versus an ischemic method. The effects observed in this work were in the first 5 days following stroke. In our case, we started recording on day 7 and examined recovery over extended periods (weeks to months). 

Effects of acute insult on rehabilitation: From a rehabilitation perspective, it remains unclear how the acute insult affects outcomes weeks and months later. One line of evidence to suggest that the manner that the acute insult occurs may not matter for rehabilitation is the observation that one therapeutic approach (vagus nerve stimulation) has been found to successfully improve rehabilitation outcomes in a range of injury models (intracranial hemorrhage, stroke, spinal cord injury). We agree that additional work is required in this area.

Human stroke data shows similar results reported: Lastly, we note that neurophysiology performed in humans with clinical strokes supports the results we seek here (e.g.[7], see discussion section for full elaboration) suggesting that our stroke model methodology is similar enough to clinical stroke to result in similar results. 

The injury model leads to seemingly mild impairments in grasp (but not reach), with rapid and complete recovery occurring within 2-3 weeks from the time of injury. Because of the rapid recovery, relating the physiological processes of recovery to beta synchronization becomes challenging to interpret - Are the global bursts the result of the loss of M1 input to subcortical structures? Are they due to the lack of M1 targets, so there is a more distributed response? Is this due to other post-injury sub-acute mechanisms? How specific is this response - is it limited to peri-infarct areas (and to what extent is the PMv electrode truly in peri-infarct cortex), or would this synchrony be seen anywhere in the sensorimotor networks? Are the local bursts present because global synchrony wanes over time as a function of post-injury homeostatic mechanisms, or is local beta synchrony increasing as new motor plans are refined and reinforced during task re-acquisition? How coupled are they related to recovery - if it is motor plan refinement, the shift from global to local seemingly should lag the recovery?  

We think these are all wonderful questions that could be addressed in follow-up studies! 

While the study has significant limitations in design that reduce the impact of the results, it should act as a useful baseline/pilot data set in which to build a more complete picture of the role of subcortical-cortical beta synchrony following cortical injury.

We agree that this is a study that should be treated as a starting point for further investigation. 

Reviewer #3 (Public review):

Summary:

Khanna et al. use a well-conceived and well-executed set of experiments and analyses primarily to document the interaction between neural oscillations in the beta range (here, 13-30 Hz) and recovery of function in an animal model of stroke. Specifically, they show that cortical "beta bursts", or short-term increases in beta power, correlate strikingly with the timeline of behavioral recovery as quantified with a reach-to-grasp task. A key distinction is made between global beta bursts (here, those that synchronize between cortical and subcortical areas) and local bursts (which appear on only a few electrodes). This distinction of global vs. local is shown to be relevant to task performance and movement speed, among other quantities of interest.

A secondary results section explores the relationship between beta bursts and neuronal firing during the grasp portion of the behavioral task. These results are valuable to include, though mostly unsurprising, with global beta in particular associated with lower mean and variance in spike rates.

Last, a partial recapitulation of the primary results is offered with a neurologically intact (uninjured) animal. No major contradictions are found with the primary results.

Highlights of the Discussion section include a thoughtful review of atypical movements executed by individuals with Parkinson's disease or stroke survivors, placing the current results in an appropriate clinical context. Potential physiological mechanisms that could account for the observed results are also discussed effectively.

Strengths:

Overall, this is a very interesting paper. The ultimate impact will be enhanced by the authors' choice to analyze beta bursts, which remain a relatively under-explored aspect of neural coding.

The reach-and-grasp task was also a well-considered choice; the combination of a relatively simple movement (reaching towards a target in the same location each time) and a more complex movement (a skilled object-manipulation grasp) provides an internal control of sorts for data analysis. In addition, the task's two sub-movements provide a differential in terms of their likelihood to be affected by the stroke-like injury: proximal muscles (controlling reach) are likely to be less affected by stroke, while distal muscles (controlling grasp) are highly likely to be affected. Lastly, the requirement of the task to execute an object lift maximizes its difficulty and also the potential translational impact of the results on human injury.

The above comments about the task exemplify a strength that is more generally evident: a welcome awareness of clinical relevance, which is in evidence several times throughout the Results and Discussion.

Weaknesses:

The study's weaknesses are mostly minor and, for the most part, correctable.

One concern that may not be correctable in this study: the results about the spatial extent of beta activity seem constrained by relatively poor-quality data. It seems half or more of the electrodes are marked as too noisy to provide useful data in Figure 3. If this reflects the wider reality for all analyses, as mentioned, it may not be correctable for the present study. In that case, perhaps some of the experiments or analyses can be revisited or expanded for a future study, when better electrode yields are available.

We thank the reviewer for their comments. We note that we have chosen to be particularly conservative with which channels we considered noise-free and acceptable for analysis as our animals were not head-posted (see methods: “On each day, trials were manually inspected alongside camera data for any movement or chewing artifacts (note that animals were not head-posted) and were discarded from neural data analysis if there were any artifacts”). After re-visiting our analysis, we note that the data shown in Fig. 3 (spatial distribution of local bursts) is not representative from a data quality perspective – this data was from a session that had a particularly large number of channels discarded due to artifacts. We plan to correct this to show a more representative figure. 

Other concerns:

In some places, there is a lack of clarity in the presentation of the results. This is not serious but should be addressed to aid readers' comprehension.

We thank the reviewer for this comment and for their numerous suggestions in the notes to the authors. We plan to address as many of these as we can to improve clarity and comprehension.  

Lastly, given the central role of beta oscillations within the study, it would be better for completeness to include even a brief exploration of sustained beta power (rather than bursts), and the modulation of sustained beta (or lack thereof) in the study's areas of concern: behavioral recovery, task performance, etc.

We thank the reviewer for this suggestion – we plan to include this in our revisions.  

References cited in response to public reviewer comments: 

(1) Ganguly, K., Khanna, P., Morecraft, R. J. & Lin, D. J. Modulation of neural co-firing to enhance network transmission and improve motor function after stroke. Neuron 110, 2363–2385 (2022).

(2) Khanna, P. et al. Low-frequency stimulation enhances ensemble co-firing and dexterity after stroke. Cell 184, 912-930.e20 (2021).

(3) Darling, W. G. et al. Sensorimotor Cortex Injury Effects on Recovery of Contralesional Dexterous Movements in Macaca mulatta. Exp Neurol 281, 37–52 (2016).

(4) Bottenfield, K. R. et al. Sex differences in recovery of motor function in a rhesus monkey model of cortical injury. Biology of Sex Differences 12, 54 (2021).

(5) Schwarz, A. et al. Association that Neuroimaging and Clinical Measures Have with Change in Arm Impairment in a Phase 3 Stroke Recovery Trial. Ann Neurol 97, 709– 719 (2025).

(6) Gulati, T. et al. Robust Neuroprosthetic Control from the Stroke Perilesional Cortex. J. Neurosci. 35, 8653–8661 (2015).

(7) Silberstein, P. et al. Cortico-cortical coupling in Parkinson’s disease and its modulation by therapy. Brain 128, 1277–1291 (2005).

eLife Assessment

This manuscript describes solid and very interesting findings that substantially advance our understanding of a major research question on the role of Cx32 hemichannels in the Schwann cell paranode. It provides an interdisciplinary integration of imaging, in silico approaches, and functional data. This important study proposes a new mechanism with profound physiological relevance and provides new insights into glial modulation of electrical conduction in sensory/motor myelinated nerves.

Reviewer #1 (Public review):

The manuscript by Butler et al. explores a novel physiological role for connexin 32 (Cx32) hemichannels in Schwann cells at peripheral nerves. Building on the authors' prior work on CO₂-sensitive gating of connexins, this study proposes that mitochondrial CO₂ production dependent on neuronal activity promotes the opening of Cx32 hemichannels in the paranode, which in turn modulates neuronal activity by reducing conduction velocity. This hypothesis is addressed using a multifaceted approach that includes immunofluorescence microscopy, dye uptake assays, calcium imaging, computational modeling, and extracellular recordings in isolated sciatic nerves.

Among the strengths of the study are the interdisciplinary integration of imaging, in silico approaches, and functional data. Also, this study proposes a new mechanism with profound physiological relevance. Specifically, Butler et al. provide new insights into glial modulation of electrical conduction in sensory/motor myelinated nerves.

In the current state, the study has some limitations. The evidence linking Cx32 to the observed dye uptake and conduction velocity changes relies primarily on pharmacological inhibition with carbenoxolone, which lacks specificity. The imaging data show overlapping marker signals that preclude the anatomical distinction between nodes and paranodes. FITC uptake, while convincing to test Cx32 hemichannel gating, lacks spatial-temporal information and validation of distribution and localization to viable intracellular compartments. Moreover, while the findings are intriguing, functional proof that Cx32 regulates conduction velocity through ATP release or other downstream effects remains incomplete. Further work using targeted genetic tools, live-tissue imaging, and additional controls would strengthen the mechanistic conclusions.

Overall, the manuscript offers compelling preliminary evidence that supports a new role for Cx32 in peripheral nerve physiology and raises important questions for future investigation.

Reviewer #2 (Public review):

Summary:

This article aims to demonstrate that local production of CO₂ at the axonal node opens Cx32 hemichannels in the Schwann cell paranode, and that CO₂ diffuses through the AQP1 channel to reach Cx32 and trigger its opening. The authors also present evidence supporting a physiological role for this regulatory mechanism. They propose that CO₂-dependent Cx32 activation mediates activity-dependent Ca²⁺ influx into the paranode, and by increasing the leak current across the myelin sheath, it contributes to a slowing of action potential conduction velocity.

The study presents a very interesting and novel mechanism for the physiological regulation of Cx32 hemichannels. The findings are relevant to the field, and the methods and results are of good quality, with some improvements in interpretation and explanation required, and some minor experimental suggestions.

Strengths:

The article is solid in terms of the novelty of the findings and relevance for the physiology of myelinated axons. In addition, it is of major interest for the Connexin field because it explores a physiological way to open Cx32 hemichannels. The experiments are well elaborated, and most of them are sufficient for the main points described by the authors. The finding that nervous activity will trigger the mechanism of hemichannel opening by CO2 is probably the most relevant biological mechanism derived from this article.

Weaknesses:

Throughout the manuscript, the authors interpret their findings as if the described mechanism specifically occurs in the node and paranode regions. However, there is no direct evidence identifying the precise site of CO₂ production or the activation site of Cx32 hemichannels. Therefore, statements such as the one in the title ("activity-dependent CO₂ production in the axonal node opens Cx32 in the Schwann cell paranode") should be reconsidered or removed, as they may be misleading and are not essential to the interpretation of the data. In addition, the participation of aquaporin AQP1 as the main conduit for CO2 diffusion through the plasma membrane could have another interpretation.

Author response:

Reviewer #1 (Public review): 

The manuscript by Butler et al. explores a novel physiological role for connexin 32 (Cx32) hemichannels in Schwann cells at peripheral nerves. Building on the authors' prior work on CO₂-sensitive gating of connexins, this study proposes that mitochondrial CO₂ production dependent on neuronal activity promotes the opening of Cx32 hemichannels in the paranode, which in turn modulates neuronal activity by reducing conduction velocity. This hypothesis is addressed using a multifaceted approach that includes immunofluorescence microscopy, dye uptake assays, calcium imaging, computational modeling, and extracellular recordings in isolated sciatic nerves. 

Among the strengths of the study are the interdisciplinary integration of imaging, in silico approaches, and functional data. Also, this study proposes a new mechanism with profound physiological relevance. Specifically, Butler et al. provide new insights into glial modulation of electrical conduction in sensory/motor myelinated nerves. 

In the current state, the study has some limitations. The evidence linking Cx32 to the observed dye uptake and conduction velocity changes relies primarily on pharmacological inhibition with carbenoxolone, which lacks specificity. The imaging data show overlapping marker signals that preclude the anatomical distinction between nodes and paranodes. FITC uptake, while convincing to test Cx32 hemichannel gating, lacks spatial-temporal information and validation of distribution and localization to viable intracellular compartments. Moreover, while the findings are intriguing, functional proof that Cx32 regulates conduction velocity through ATP release or other downstream effects remains incomplete. Further work using targeted genetic tools, live-tissue imaging, and additional controls would strengthen the mechanistic conclusions. 

Overall, the manuscript offers compelling preliminary evidence that supports a new role for Cx32 in peripheral nerve physiology and raises important questions for future investigation. 

We thank the reviewer for their comments and agree that the evidence for involvement of Cx32 is indirect. We are planning to perform genetic manipulations to strengthen this link. We shall review our presentation of the morphology in terms of the node/paranode/juxtaparanode distribution and adjust accordingly. We have in the interim generated new data using GCaMP transduced into Schwann cells that provides the live-tissue imaging that the reviewer requests. This strengthens our conclusions, and we will add these data into the paper.

Reviewer #2 (Public review): 

Summary: 

This article aims to demonstrate that local production of CO₂ at the axonal node opens Cx32 hemichannels in the Schwann cell paranode, and that CO₂ diffuses through the AQP1 channel to reach Cx32 and trigger its opening. The authors also present evidence supporting a physiological role for this regulatory mechanism. They propose that CO₂-dependent Cx32 activation mediates activity-dependent Ca²⁺ influx into the paranode, and by increasing the leak current across the myelin sheath, it contributes to a slowing of action potential conduction velocity. 

The study presents a very interesting and novel mechanism for the physiological regulation of Cx32 hemichannels. The findings are relevant to the field, and the methods and results are of good quality, with some improvements in interpretation and explanation required, and some minor experimental suggestions. 

Strengths: 

The article is solid in terms of the novelty of the findings and relevance for the physiology of myelinated axons. In addition, it is of major interest for the Connexin field because it explores a physiological way to open Cx32 hemichannels. The experiments are well elaborated, and most of them are sufficient for the main points described by the authors. The finding that nervous activity will trigger the mechanism of hemichannel opening by CO2 is probably the most relevant biological mechanism derived from this article. 

Weaknesses: 

Throughout the manuscript, the authors interpret their findings as if the described mechanism specifically occurs in the node and paranode regions. However, there is no direct evidence identifying the precise site of CO₂ production or the activation site of Cx32 hemichannels. Therefore, statements such as the one in the title ("activity-dependent CO₂ production in the axonal node opens Cx32 in the Schwann cell paranode") should be reconsidered or removed, as they may be misleading and are not essential to the interpretation of the data. In addition, the participation of aquaporin AQP1 as the main conduit for CO2 diffusion through the plasma membrane could have another interpretation. 

We thank the reviewer for their comments and agree that we do not have direct evidence for the site of CO2 production or the site of activation of Cx32 hemichannels. This direct evidence is extremely difficult to obtain, and we therefore depend on indirect arguments. Mitochondria represent the major source of CO2, and their distribution will therefore indicate where CO2 is likely to be produced. We agree that this is not essential to the interpretation of the data and will adjust the text as recommended. We will add a section to the Discussion to consider this point in more detail.

eLife Assessment

The article presents important findings of a dissociation between phasic and tonic pain functions in adaptive behavior, combining immersive VR, computational modeling, skin conductance, and EEG data. The methodology used is solid. Its ecological design and sophisticated computational modeling are major strengths. The article would benefit from adding details on hypotheses, VR implementation, sample size determination, modeling, analysis, and pain specificity.

Reviewer #1 (Public review):

Summary:

This article presents a study consisting of two experiments, which aim to dissociate and quantify the distinct motivational functions of phasic and tonic pain within a naturalistic and immersive VR setting. Specifically, the authors test two hypotheses: (i) that phasic pain acts as a punishment signal that drives avoidance learning; (ii) that tonic pain reduces motivational vigor, promoting energy conservation and recuperation. In both experiments, participants performed a free-operant foraging task, where they collected virtual pineapples to earn points.

In Experiment 1, phasic pain was delivered as a brief electric shock to the grasping hand when picking up green pineapples. As phasic pain intensity increased, participants were less likely to choose painful fruits. A reinforcement learning model that incorporated reward, pain cost, and effort cost was able to successfully capture behavior.

Experiment 2 combined the effects of phasic and tonic pain. Tonic pain was induced by a pressure cuff on the non-dominant arm, simulating sustained discomfort. Interestingly, tonic pain did not affect the perceived intensity or avoidance of phasic pain. However, it significantly reduced movement velocity and pineapple collection rate, interpreted as a reduction of motivational vigor. A temporal decision model incorporating vigor cost successfully captured these effects.

Concomitant EEG recordings showed that tonic pain was associated with reduced alpha and beta power in parietal and temporal areas. Phasic pain ratings and decision values distinctively correlated with skin conductance responses.

Overall, these findings indicate that phasic and tonic pain have distinct and dissociable motivational effects.

Strengths:

This is an ambitious study that provides a quantitative dissociation of the roles of phasic and tonic pain in adaptive behavior, by integrating ecological neuroscience, motivational theory, and computational modeling. The use of immersive VR combined with a free-operant foraging task offers a more ecologically valid context to study pain-related behavior compared to traditional paradigms. Furthermore, the study employs a multimodal approach by combining behavioral data, computational frameworks, physiological signals, and EEG. In particular, one of the main strengths of the study is the use of sophisticated computational modeling to capture phasic and tonic pain effects. The experiment codes are available on GitHub, increasing reproducibility.

Weaknesses:

The main limitations of this article are that it provides insufficient detail on VR implementation. The design of the VR environment is, at this stage, under-described. Crucial information is missing, such as the number of pineapples per block, timing precision, details on how motion is mapped to the virtual movement, etc. This aspect strongly limits the reproducibility of the experiments. A second limitation lies in the lack of clarity regarding the study hypotheses. Although two overarching hypotheses can be inferred, they are not explicitly formulated. To this end, it is unclear which analyses were merely exploratory, especially for physiological and EEG outcomes.

In Experiment 2, the reduction in vigor during tonic pain could plausibly reflect attentional load rather than pain per se. As recognized by the authors, there is no control condition involving an innocuous salient stimulus to rule out non-specific effects of distraction. Perhaps a tonic non-painful but salient somatosensory stimulus (e.g., a strong vibrotactile stimulus applied on the same arm) could have been used as a control stimulus.

Reviewer #2 (Public review):

Summary:

The study investigated the distinct roles of phasic and tonic pain in adaptive behavior. Phasic pain was proposed to function as a teaching signal, promoting avoidance of further injury, while tonic pain was hypothesized to support recuperative behavior by reducing motivational vigor. This hypothesis was tested using an immersive virtual reality (VR) EEG foraging task, in which participants harvested fruit in a forest environment. Some fruits triggered brief phasic pain to the grasping hand, which in turn reduced the likelihood of choosing those fruits. Concurrently, tonic pressure pain applied to the contralateral upper arm was associated with reduced action velocities. The authors employed a free-operant computational framework to quantify how phasic and tonic pain modulate motivational vigor and decision value. Importantly, model parameters were found to correlate with EEG responses, providing neurophysiological support for the hypothesized functional distinctions.

Strengths:

Overall, this study aims to address an important topic and is generally well written.

Weaknesses:

Two critical issues require clarification or justification.

First, phasic pain was induced using electrical stimulation, which typically elicits somatosensory evoked potentials (SEPs). These responses may not reflect pain-specific processes and thus complicate interpretation. This issue bears directly on the study's conclusions, especially when discussing interactions between phasic and tonic pain. For example, tonic pain is known to reduce perceived intensity or cortical responses to phasic pain stimuli delivered elsewhere on the body - an effect not expected for SEPs elicited by electrical stimuli.

Second, additional control experiments are necessary to rule out alternative explanations. For instance, the authors are suggested to deliver phasic pain to the contralateral arm (e.g., at 1-2 Hz), which might also reduce action velocity. Similarly, tonic pain applied to the grasping hand should be tested to disentangle hand-specific effects.

Reviewer #3 (Public review):

Summary:

This study investigates how phasic and tonic pain modulate behaviour in a free-operant foraging paradigm. The authors apply a computational modeling approach to the behavioural data to quantify the decision value of phasic pain, as well as the degree to which tonic pain reduces motivational vigour. EEG assessments showed, e.g., reduced signal power at alpha and beta frequencies in tonic pain conditions compared to no-tonic-pain conditions, but no association between these neural measures and motivational vigour. The authors conclude that tonic and phasic pain serve different motivational functions, with phasic pain acting as a punishment signal promoting avoidance and tonic pain reducing motivational vigour.

Strengths:

The experimental paradigm is highly innovative. Assessing human behaviour in a naturalistic yet highly controlled setting represents a promising approach to pain research. Notably, assessing pain magnitude implicitly, via its motivational value, offers insights about the overall pain experience that are not usually accessible via common pain ratings.

Weaknesses:

Despite these strengths, the manuscript would benefit significantly from more precise definitions of key concepts and an overall clearer, more coherent presentation of its main arguments. The writing, in its current form, often presents claims that are too vague or insufficiently connected with the experimental findings. Moreover, certain aspects of the computational modeling and statistical analysis appear flawed or inadequately justified.

Author response:

Reviewer #1 (Public review):

The main limitations of this article are that it provides insufficient detail on VR implementation. The design of the VR environment is, at this stage, under-described. Crucial information is missing, such as the number of pineapples per block, timing precision, details on how motion is mapped to the virtual movement, etc. This aspect strongly limits the reproducibility of the experiments. A second limitation lies in the lack of clarity regarding the study hypotheses. Although two overarching hypotheses can be inferred, they are not explicitly formulated. To this end, it is unclear which analyses were merely exploratory, especially for physiological and EEG outcomes.

In Experiment 2, the reduction in vigor during tonic pain could plausibly reflect attentional load rather than pain per se. As recognized by the authors, there is no control condition involving an innocuous salient stimulus to rule out non-specific effects of distraction. Perhaps a tonic non-painful but salient somatosensory stimulus (e.g., a strong vibrotactile stimulus applied on the same arm) could have been used as a control stimulus.

We appreciate the reviewer's comments regarding the insufficient implementation details. We hope the newly uploaded software for reproducing the experiment can improve the reader's understanding of the task. In addition to making the software available, we will expand the Methods section in the revised manuscript to include greater detail on the task description.

The hypothesised functions of phasic and tonic pain, and their collaborative interaction, are both broad and deep topics. In the revised manuscript, we will more explicitly formulate our hypotheses and clarify the distinction between a priori predictions and exploratory analyses, particularly concerning the extent to which our evidence supports these hypotheses.

We agree that examining the potential role of attentional load on the interaction between tonic and phasic pain is an important area of future investigation. Addition of additional control conditions matched for attentional salience with additional experiments is possible but introduces other confounds related to their different qualities (e.g. a salient vibrotactile stimulus might invigorate behaviour): however more fundamentally, attentional processes are a core part of pain function, and should not necessarily be viewed as a confound (i.e. the way that pain mediates some of its core functional effects may directly be through its salient attentional nature) . This view is formalised in Wall and Melzack’s classical tripartite model of pain, and distinguishes pain from purely sensory systems such as somatosensation, vision and so on..

Reviewer #2 (Public review):

Two critical issues require clarification or justification. First, phasic pain was induced using electrical stimulation, which typically elicits somatosensory evoked potentials (SEPs). These responses may not reflect pain-specific processes and thus complicate interpretation. This issue bears directly on the study's conclusions, especially when discussing interactions between phasic and tonic pain. For example, tonic pain is known to reduce perceived intensity or cortical responses to phasic pain stimuli delivered elsewhere on the body - an effect not expected for SEPs elicited by electrical stimuli.

We acknowledge the reviewer’s concern regarding the specificity of evoked potentials elicited by electrical stimulation. We agree that traditional SEPs—particularly those evoked by large surface electrodes—primarily reflect activation of non-nociceptive A-beta fibres and thus may not reliably index pain-specific processes or be modulated by tonic pain via descending nociceptive control. However, we would like to clarify that phasic pain was administered in the present study using small-diameter concentric ‘Wasp’ electrodes. These are comparable to intraepidermal electrodes shown to preferentially activate nociceptive A-delta fibres, thereby eliciting ERPs more closely associated with nociceptive processing rather than mixed somatosensory input [1, 2]. Accordingly, our ERP results demonstrated a reliable increase in N1-P2 amplitude with higher phasic pain intensity, suggesting that the evoked responses captured stimulus-evoked nociceptive processing.

We acknowledge that these ERPs may still reflect mixed sensory processing and thus may not be fully modulated by tonic pain. Previous studies have shown that ERPs elicited by nociceptive electrical stimulation can be attenuated during tonic pain using cold-water immersion in CPM paradigms [3, 4]. However, these studies typically employ passive tasks, whereas our paradigm involved continuous voluntary behaviour during sustained tonic pressure pain. This difference in task context may engage distinct modulatory systems, possibly prioritising behavioural adaptation over sensory gating.

We will revise the manuscript to acknowledge these factors and to encourage a more nuanced interpretation of the ERP findings in light of this literature.

Second, additional control experiments are necessary to rule out alternative explanations. For instance, the authors are suggested to deliver phasic pain to the contralateral arm (e.g., at 1-2 Hz), which might also reduce action velocity. Similarly, tonic pain applied to the grasping hand should be tested to disentangle hand-specific effects.

We are grateful to the reviewer for this suggestion. In the current study, phasic pain was delivered to the grasping hand to generate a coherent, spatially congruent representation of virtual stimuli (painful fruit) and behavioural consequences (pain upon grasp). Delivering phasic pain stimuli to the contralateral hand would be incongruent with the task design and may alter the interpretation of the learning signal, which was central to our computational modelling framework. Similarly, tonic pain was not applied to the grasping hand to avoid interfering with motor control. Applying tonic pain to the grasping hand would make it extremely difficult for participants to effectively grasp the hand controller, thereby complicating the interpretation of behavioural and neural measures. We will discuss these issues in the revision. Therefore, while we agree that such manipulations could be informative for future studies, they were not the focus of the current investigation.

Reviewer #3 (Public review):

Despite these strengths, the manuscript would benefit significantly from more precise definitions of key concepts and an overall clearer, more coherent presentation of its main arguments. The writing, in its current form, often presents claims that are too vague or insufficiently connected with the experimental findings. Moreover, certain aspects of the computational modeling and statistical analysis appear flawed or inadequately justified.

We thank the reviewer for highlighting the need for clearer definitions and a more coherent presentation. In the revised manuscript, we will refine our definitions of key concepts and improve the presentation of hypothesised functions of phasic and tonic pain. As stated previously, we will clarify the extent to which our evidence supports these hypotheses. We also appreciate the feedback on our statistical analysis and computational modelling. We will address these points and provide the necessary clarifications and justifications in the revised manuscript.

eLife Assessment

This valuable study presents a mouse gastruloid system to generate successive waves of hematopoietic progenitors that in vivo would emerge during embryonic development. Although this newly revised manuscript has addressed some of the concerns raised during the first round of review, the study is still considered incomplete, as the claims are only partially supported. In particular, the claim of definitive wave hematopoietic progenitors being produced in the gastruloids, and their engraftment after transplantation, would benefit from further validation.

Reviewer #1 (Public review):

Summary

This manuscript describes a haemogenic gastruloid system that the authors claim recapitulates early mouse embryonic development to produce sequential waves of yolk sac and AGM-like haematopoiesis, with spatial and temporal accuracy. The model claims to reproduce mouse development to 'beyond' the E9.0 stage and apply its use to the aetiology of infant leukaemia.

Strengths

Gastruloids models are useful systems for studying early embryonic development, recapitulating aspects of gastrulation, anteroposterior regionalisation and somitogenesis. Gastruloid models that specifically mimic particular regions of the embryo could provide insights into how these regions form during development.

Weaknesses

There are a couple of major issues with this manuscript that I feel need to be addressed.

Firstly, the authors acknowledge that the proportion of blood cells that are produced by their haemogenic gastruloid system is very low - there are fewer than 2% of either blood or endothelium produced. The authors argue however, that this is because they have developed a hematopoietic organoid that captures much more of the essence of the developing embryo and therefore has a broader tissue representation and a more relevant spatial representation.

In order to prosecute this argument, this reviewer needs to understand how the differentiation protocol achieves this end, ie what is notable about the combination of factors and other media components. Also, they need to know what the evidence is to support this claim, in other words, what are the tissues that make up the organoid and is it truly representative of what would be expected in a developing embryo over this time. Does it pass from epiblast to primitive streak and then to cells of the germ layers? And how do haemGXs at different times map onto the developing mouse embryo?

Secondly, the point is repeatedly made by the authors that the distinction between non-engrafting yolk sac hematopoiesis and AGM-like hematopoiesis from which repopulating HSCs first derive is not really possible without spatial cues. This is really not true. It has been shown by a number of investigators, and summarised in a recent review (Abuhantash et al 2021), that the expression of HOXA cluster genes - most prominently HOXA9 - clearly distinguishes AGM-derived, from yolk sac derived cells. In this manner, it is evident from the UMAP provided that the is no HOXA9 expressed in either endothelium or blood cells. This argues very strongly against the proposition that AGM-type hematopoiesis is generated. Indeed, given the duration of the organoid culture of only 9 days (216hrs), it would be highly unlikely that development would even reach the stage of AGM hematopoiesis (E11.5 in the mouse), even with a 1:1 concordance between embryonic time and in vitro differentiation. Finally, if there is recapitulation of the normal pattern of embryogenesis, it would be expected that there would be a prominent phase of yolk sac hematopoiesis antedating AGM-associated hematopoiesis, which should be observed in the haemGx.

I feel that these are major conceptual points that need to be addressed in this manuscript.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors describe the development of a new hemogenic gastruloid (hGX) system, which they claim recapitulates the sequential generation of various hematopoietic cell types. A key proposed advantage of this system is its ability to more faithfully model the spatiotemporal emergence of hematopoietic progenitors within a physiologically relevant niche, as compared to existing in vitro platforms. While the authors provide some initial characterisation and demonstrate the utility of the system in studying infant leukemia, the presented data are not fully conclusive and fall short of robustly supporting several of their key assertions.

Strengths:

The development of a novel in vitro system to model hematopoietic development is innovative and could potentially address important limitations of existing platforms.

Weaknesses:

The characterization of the hematopoietic progenitors generated by the hGX system is not fully convincing. The evidence supporting the emergence of late yolk sac (YS) progenitors, including lymphoid cells, and AGM-like pre-hematopoietic stem cells (pre-HSCs), is incomplete and relies heavily on transcriptomic profiling and a limited set of markers.

The identification of lymphoid or pre-HSC-like populations is primarily inferred from scRNA-seq data. The lack of robust functional validation (e.g., lymphoid differentiation assays or long-term repopulation experiments) significantly weakens the manuscript's main claims.

In the revised manuscript, the authors incorporate single-cell RNA-seq analyses indicating that their cells resemble AGM-derived endothelial-to-hematopoietic transition (EHT) populations. However, they do not test whether these cells might more closely resemble YS-derived EHT, which remains an unresolved and critical question. Additionally, the claim in line 263 that Cluster 8 (CD45⁺ cells at 192-216 h) expresses lymphoid markers is not clearly supported by the provided supplemental data (Supplemental File S1-S2).

While the authors respond that they did not claim to generate bona fide HSCs, they do state at the end of the Introduction (lines 116-121) that their system captures AGM hematopoiesis. The current data do not support this conclusion and instead suggest that the system recapitulates the generation of multipotent lymphoid progenitors (MLPs) akin to those found in the YS.

The engraftment data presented are not particularly convincing. It is unclear why the analysis was terminated at 8 weeks post-transplant, especially given that a minimum of 12 weeks is generally required to meaningfully assess the presence of pre-HSCs or bona fide HSCs with long-term repopulating potential.

Given the uncertainties discussed above, the interpretability of the MNX1 overexpression study is limited.

The authors could have more directly tested their claim of capturing multiple hematopoietic waves by performing kinetic analyses of colony-forming potential, with the expectation that more multipotent colonies would emerge at later time points. Additionally, isolating and characterizing the potential of hemogenic endothelium at different time points corresponding to the putative waves would have strengthened their conclusions. In the absence of such data, it remains unclear whether the system recapitulates sequential waves of hematopoiesis or merely reflects the progressive maturation of cells originating from a single wave.

Reviewer #3 (Public review):

The authors present a revised version of their manuscript (Ragusa et al.) describing a hemogenic gastruloid (haemGx) model, used to investigate stages of blood production in vitro and for modeling a rare type of infant leukemia. The revisions address several major concerns raised during the initial round of review, and new data have been provided that overall improve the clarity and rigour of the study. In particular, the additional flow cytometry, single-cell RNA-seq analyses, and benchmarking against in vivo datasets help, to some extent, to substantiate the claims of developmental relevance of haemGx to yolk sac (YS)- and AGM-like hematopoietic waves. Nonetheless, some issues remain, particularly regarding the claims of short-term engraftment, novelty of the model, and the extent to which AGM-like HSPC are truly captured.

Major Points:

(1) The authors have clarified the novelty of their haemGx protocol relative to existing gastruloid models, including the importance of the Activin A pulse and protocol extension to 216h. Flow cytometry and scRNA-seq analyses support the emergence of endothelial and hematopoietic populations with dynamic marker expression. However, direct side-by-side comparisons with previously published protocols (e.g., Rossi et al., 2022) remain limited. The claim of "spatio-temporal accuracy" should be more cautiously phrased.

(2) The characterization of the identity of the hematopoietic waves generated in the haemGx system has been improved in the revised manuscript. Flow cytometry analysis now includes CD31/CD34 co-expression in CD41+ and CD45+ subsets, and scRNA-seq re-clustering supports two hematopoietic waves with distinct marker sets (e.g., Gata2/Myb vs. Hoxa9/Ikzf1). Projection onto multiple embryonic reference datasets (Hou et al., Zhu et al., Thambyrajah et al.) is a valuable addition. The case for YS-like EMP and AGM-like HSPC precursors is reasonably made, though further functional distinctions (e.g., lineage output differences) would strengthen the claims.

(3) The authors have now provided additional evidence for low-level engraftment following adrenal implantation of whole haemGx. Although technically demanding, this in vivo result remains marginal and should be interpreted with caution. Crucially, this still does not demonstrate HSC-level repopulation capacity. The revised manuscript has softened the claims accordingly, now referring to "progenitor" activity rather than "pre-HSC." We agree that this adjusted claim is more suitable, though the reproducibility of this experiment is still unclear.

(4) The MNX1 overexpression experiments are generally convincing in showing early expansion of a putative HE-to-EMP-like population and transcriptional resemblance to MNX1-r AML. However, the evidence for transformation is still solely based on in vitro data and lacks any evidence of in vivo leukaemia engraftment. The ability to perturb the system would add translational value to the haemGx platform, although future studies are needed to better define transformation dynamics and leukemogenic progression.

eLife Assessment

This valuable study presents findings linking prophage carriage to lifestyle regulation in the marine bacterium Shewanella fidelis, with potential implications for niche occupation within a host (Ciona robusta) and mediation of host immune responses. The study leverages a unique animal model system that offers distinct advantages in identifying select phenotypes to present overall solid evidence that supports findings relating to the impact of a prophage on host-microbe interaction. Understanding the role of integrated lysogenic phages in bacterial fitness, both within a host and in the environment, is a significant concept in bacterial eco-physiology, potentially contributing to the success of certain strains.

Reviewer #1 (Public review):

Summary:

The manuscript aims to elucidate the impact of a prophage within the genome of Shewanella fidelis on its interaction with the marine tunicate Ciona robusta. The authors made a deletion mutant of S. fidelis that lacks one of its two prophages. This mutant exhibited an enhanced biofilm phenotype, as assessed through crystal violet staining, and showed reduced motility. The authors examined the effect of prophage deletion on several genes that could modulate cyclic-diGMP levels. While no significant changes were observed under in vitro conditions, the gene for one protein potentially involved in cyclic-diGMP hydrolysis was overexpressed during microbe-host interactions. The mutant was retained more effectively within a one-hour timeframe, whereas the wild-type (WT) strain became more abundant after 24 hours. Fluorescence microscopy was used to visualize the localization patterns of the two strains, which appeared to differ. Additionally, a significant difference in the expression of one immune protein was noted after one hour, but this difference was not evident after 23 hours. An effect of VCBC-C addition on the expression of one prophage gene was also observed.

Strengths:

I appreciate how the authors integrate diverse expertise and methods to address questions regarding the impact of prophages on gut microbiome-host interactions. The chosen model system is appropriate, as it allows for high-throughput experimentation and the application of simple imaging techniques.

Weaknesses:

My primary concern is that the manuscript primarily describes observations without providing insight into the molecular mechanisms underlying the observed differences. It is particularly unclear how the presence of the prophage leads to the phenotypic changes related to bacterial physiology and host-microbe interactions. Which specific prophage genes are critical, or is the insertion at a specific site in the bacterial genome the key factor? While significant effects on bacterial physiology are reported under in vitro conditions, there is no clear attribution to particular enzymes or proteins. In contrast, when the system is expanded to include the tunicate, differences in the expression of a cyclic-diGMP hydrolase become apparent. Why do we not observe such differences under in vitro conditions, despite noting variations in biofilm formation and motility? Furthermore, given that the bacterial strain possesses two prophages, I am curious as to why the authors chose to target only one and not both.

Regarding the microbe-host interaction, it is not clear why the increased retention ability of the prophage deletion strain did not lead to greater cell retention after 24 hours, especially since no differences in the immune response were observed at that time point.

Concerning the methodological approach, I am puzzled as to why the authors opted for qPCR instead of transcriptomics or proteomics. The latter approaches could have provided a broader understanding of the prophage's impact on both the microbe and the host.

Comments on revisions:

While the authors were able to solve some of my issues, I see that other questions were not tackled.

Reviewer #2 (Public review):

Summary:

In the manuscript, "Prophage regulation of Shewanella fidelis 3313 motility and biofilm formation: implications for gut colonization dynamics in Ciona robusta", the authors are experimentally investigating the idea that integrated viruses (prophages) within a bacterial colonizer of the host Ciona robusta affect both the colonizer and the host. They found a prophage within the Ciona robusta colonizing bacterium Shewanella fidelis 3313, which affected both the bacteria and host. This prophage does so by regulating the phosphodiesterase gene pdeB in the bacterium when the bacterium has colonized the host. The prophage also regulates the activity of the host immune gene VCBP-C during early bacterial colonization. Prophage effects on both these genes affect the precise localization of the colonizing bacterium, motility of the bacterium, and bacterial biofilm formation on the host. Interestingly, VCBP-C expression also suppressed a prophage structural protein, creating a tripartite feedback loop in this symbiosis. This is exciting research that adds to the emerging body of evidence that prophages can have beneficial effects not only on their host bacteria but also on how that bacteria interacts in its environment. This study establishes the evolutionary conservation of this concept with intriguing implications of prophage effects on tripartite interactions.

Strengths:

This research effectively shows that a prophage within a bacterium colonizing a model ascidian affects both the bacterium and the host in vivo. These data establish the prophage effects on bacterial activity and expand these effects to the natural interactions within the host animal. The effects of the prophage through deletion on a suite of host genes are a strength, as shown by striking microscopy.

Weaknesses:

Unfortunately, global transcriptomics of the bacteria and the host during colonization by the prophage-containing and prophage-deleted bacteria (1 hour and 24 hours) would be suggested to better understand the tripartite interactions.

Impact:

The authors are correct to speculate that this research can have a significant impact on many animal microbiome studies, since bacterial lysogens are prevalent in most microbiomes. Screening for prophages, determining whether they are active, and "curing" the host bacteria of active prophages are effective tools for understanding the effects these mobile elements have on microbiomes. There are many potential effects of these elements in vivo, both positive and negative, this research is a good example of why this research should be explored.

Context:

The research area of prophage effects on host bacteria in vitro has been studied for decades, while these interactions in combination with animal hosts in vivo have been recent. The significance of this research shows that there could be divergent effects based on whether the study is conducted in vitro or in vivo. The in vivo results were striking. This is particularly so with the microscopy images. The benefit of using Ciona is that it has a translucent body which allows for following microbial localization. This is in contrast to mammalian studies where following microbial localization would either be difficult or near impossible.

Comments on revisions:

I am satisfied with the great amount of work that went into the comments provided by the reviewers. The figure presentations are more compelling for the story, and this latest revision is a very interesting read that should be considered for future microbiome studies.

Reviewer #3 (Public review):

In this manuscript, Natarajan and colleagues report on the role of a prophage, termed SfPat, in the regulation of motility and biofilm formation by the marine bacterium Shewanella fidelis. The authors investigate the in vivo relevance of prophage carriage by studying the gut occupation patterns of Shewanella fidelis wild-type and an isogenic SfPat- mutant derivative in a model organism, juveniles of the marine tunicate Ciona robusta. The role of bacterial prophages in regulating bacterial lifestyle adaptation and niche occupation is a relatively underexplored field, and efforts in this direction are appreciated.

Comments on revisions:

The authors have addressed my main concerns. While some responses remain somewhat ambiguous or defer key clarifications to future studies, I appreciate that not everything can be resolved within a single manuscript.

eLife Assessment

This work provides valuable insights by introducing a post-translational extrusion mechanism that could reshape how we understand the coupling between DnaA activity and DNA-replication initiation. While solid evidence is presented for some of the key results, other claims rest on indirect proxies and could be improved.

Reviewer #1 (Public review):

Summary:

The study by Li and coworkers addresses the important and fundamental question of replication initiation in Escherichia coli, which remains open, despite many classic and recent works. It leverages single-cell mRNA-FISH experiments in strains with titratable DnaA and novel DnaA activity reporters to monitor DNA activity peaks versus size. The authors find oscillations in DnaA activity and show that their peaks correlate well with the estimated population-average replication initiation volume across conditions and imposed dnaA transcription levels. The study also proposes a novel extrusion model where DNA-binding proteins regulate free DnaA availability in response to biomass-DNA imbalance. Experimental perturbations of H-NS support the model validity, addressing key gaps in current replication control frameworks.

Strengths:

I find the study interesting and well conducted, and I think its main strong points are:

(1) the novel reporters obtained with systematic synthetic biology methods, and combined with a titratable dnaA strain.

(2) the interesting perturbations (titration, production arrest, and H-NS).

(3) the use of single-cell mRNA FISH to monitor transcripts directly.

The proposed extrusion model is also interesting, though not fully validated, and I think it will contribute positively to the future debate.

Weaknesses and Limitations:

(1) A relevant limitation in novelty is that DnaA activity and concentration oscillations have been reported by the cited Iuliani and coworkers previously by dynamic microscopy, and to a smaller extent by the other cited study by Pountain and coworkers using mRNA FISH.

(2) An important limitation is that the study is not dynamic. While monitoring mRNA is interesting and relevant, the current study is based on concentrations and not time variations (or nascent mRNA). Conversely, the study by Iuliani and coworkers, while having the drawback of monitoring proteins, can directly assess production rates. It would be interesting for future studies or revisions to monitor the strains and reporters dynamically, as well as using (as a control) the technique of this study on the chromosomal reporters used by Iuliani et al.

(3) Regarding the mathematical models, a lot of details are missing regarding the definitions and the use of such models, which are only presented briefly in the Methods section. The reader is not given any tools to understand the predictions of different models, and no analytical estimates are used. The falsification procedures are not clear. More transparency and depth in the analysis are needed, unless the models are just used as a heuristic tool for qualitative arguments (but this would weaken the claims). The Berger model, for example, has many parameters and many regimes and behaviors. When models are compared to data (e.g., in Figure 2G), it is not clear which parameters were used, how they were fixed, and whether and how the model prediction depends on parameters.

(4) Importantly, the main statement about tight correlations of peak volumes and average estimated initiation volume does not establish coincidence, and some of the claims by the authors are unclear in these respects (e.g., when they say "we resolve a 1:1 coupling between DnaA activity thresholds and replication initiation", the statement could be correct but is ambiguous). Crucially, the data rely on average initiation volumes (on which there seems to be an eternally open debate, also involving the authors), and the estimate procedure relies on assumptions that could lead to biases and uncertainties added to the population variability (in any case, error bars are not provided).

(5) The delays observed by the authors (in both directions) between the peaks of DnaA-activity conditional averages with respect to volume and the average estimated initiation volumes are not incompatible with those observed dynamically by Iuliani and coworkers. The direct experiment to prove the authors' point would be to use a direct proxy of replication initiation, such as SeqA or DnaN, and monitor initiations and quantify DnaA activity peaks jointly, with dynamic measurements.

(6) While not being an expert, I had some doubt that the fact that the reporters are on plasmid (despite a normalization control that seems very sensible) might affect the measurements. Also, I did not understand how the authors validated the assumptions that the reporters are sensitive to DnaA-ATP specifically. It seems this assumption is validated by previous studies only.

Overall Appraisal:

In summary, this appears as a very interesting study, providing valuable data and a novel hypothesis, the extrusion model, open to future explorations. However, given several limitations, some of the claims appear overstated. Finally, the text contains some self-evaluations, such as "our findings redefine the paradigm for replication control", etc., that appear exaggerated.

Reviewer #2 (Public review):

Summary:

The authors show that in E. coli, the initiator protein DnaA oscillates post-translationally: its activity rises and peaks exactly when DNA replication begins, even if dnaA transcription is held constant. To explain this, they propose an "extrusion" mechanism in which nucleoid-associated proteins such as H-NS, whose amount grows with cell volume, dislodge DnaA from chromosomal binding sites; modelling and H-NS perturbations reproduce the observed drop in initiation mass and extra initiations seen after dnaA shut-down. Together, the data and model link biomass growth to replication timing through chromosome-driven, post-translational control of DnaA, filling gaps left by classic titration and ATP/ADP-switch models.

Strengths:

(1) Introduces an "extrusion" model that adds a new post-translational layer to replication control and explains data unexplained by classic titration or ATP/ADP-switch frameworks.

(2) A major asset of the study is that it bridges the longstanding gap between DnaA oscillations and DNA-replication initiation, providing direct single-cell evidence that pulses of DnaA activity peak exactly at the moment of initiation across multiple growth conditions and genetic perturbations.

(3) A tunable dnaA strain and targeted H-NS manipulations shift initiation mass exactly as the model predicts, giving model-driven validation across growth conditions.

(4) A purpose-built Psyn66 reporter combined with mRNA-FISH captures DnaA-activity pulses with cell-cycle resolution, providing direct, compelling data.

Weaknesses:

(1) What happens to the (C+D) period and initiation time as the dnaA mRNA level changes? This is not discussed in the text or figure and should be addressed.

(2) It is unclear what is meant by "relative dnaA mRNA level." Relative to what? Wild-type expression? Maximum expression? This should be explicitly defined.

(3) It would be helpful to provide some intuition for why an increase in dnaA mRNA level leads to a decrease in initiation mass per ori and an increase in oriC copy number.

(4) The titration and switch models do not explicitly include dnaA mRNA in the dynamics of DnaA protein. Yet, in Figure 2G, initiation mass is shown to decrease linearly with dnaA mRNA level in these models. How was dnaA mRNA level represented or approximated in these simulations?

(5) Is Schaechter's law (i.e., exponential scaling of average cell size with growth rate) still valid under the different dnaA mRNA expression conditions tested?

(6) The manuscript should explain more explicitly how the extrusion model implements post-translational control of DnaA and, in particular, how this yields the nonlinear drop in relative initiation mass versus dnaA mRNA seen in Figure 6E. Please provide the governing equation that links total DnaA, the volume-dependent "extruder" pool, and the threshold of free DnaA at initiation, and show - briefly but quantitatively - how this equation produces the observed concave curve.

(7) Does this Extrusion model give well well-known adder per origin, i.e., initiation to initiation is an adder.

(8) DnaA protein or activity is never measured; mRNA is treated as a linear proxy. Yet the authors' own narrative stresses post-translational (not transcriptional) control of DnaA. Without parallel immunoblots or activity readouts, it is impossible to know whether a six-fold mRNA increase truly yields a proportional rise in active DnaA.

(9) Figure 2 infers both initiation mass and oriC copy number from bulk measurements (OD₆₀₀ per cell and rifampicin-cephalexin run-out) instead of measuring them directly in single cells. Any DnaA-dependent changes in cell size, shape, or antibiotic permeability could skew these bulk proxies, so the plotted relationships may not accurately reflect true initiation events.

eLife Assessment

This paper reports the development of proteins and small molecules that drive bridge LMO2, an oncogenic transcription factor in T-ALL, to E3 ligases (Cereblon and VHL), and demonstrates their effectiveness in degrading FMO2, causing growth arrest and inducing apoptosis in T cell lines in vitro. The findings are valuable because they provide evidence that intrinsically disordered proteins can be targeted for degradation by PROTAC-type chemicals. The paper also provides a route for rational PROTAC design based on intracellular antibody paratopes. Overall, the paper is supported by solid evidence and will be of interest to chemical biologists and cancer pharmacologists.

Reviewer #1 (Public review):

Summary:

The authors describe the degradation of an intrinsically disordered transcription factor (LMO2) via PROTACs (VHL and CRBN) in T-ALL cells. Given the challenges of drugging transcription factors, I find the work solid and a significant scientific contribution to the field.

Strengths:

(1) Validation of LMO2 degradation by starting with biodegraders, then progressing to chemical degrades.

(2) interrogation of the biology and downstream pathways upon LMO2 degradation (collateral degradation and apoptotic markers).

(3) Cell line models that are dependent/overexpression of LMO2 vs LMO2 null cell lines.

(4) CRBN and VHL-derived PROTACs were synthesized and evaluated.

Weaknesses:

(1) The conventional method used to characterize PROTACs in the literature is to calculate the DC50 and Dmax of the degraders, I did not find this information in the manuscript.

(2) The proteomics data is not very convincing, and it is not clear why LMO2 does not show in the volcano plot (were higher concentrations of the PROTAC tested? and why only VHL was tested and not CRBN-based PROTAC?).

(3) The correlation between degradation potency and cell growth is not well-established (compare Figure 4C: P12-Ichikawa blots show great degradation at 24 and 48 hrs, but it is unclear if the cell growth in this cell line is any better than in PF-382 or MOLT-16) - Can the authors comment on the correlation between degradation and cell growth?

(4) The PROTACs are not very potent (double-digit micromolar range?) - can the authors elaborate on any challenges in the optimization of the degradation potency?

(5) The authors mentioned trying six iDAb-E3 ligase proteins; I would recommend listing the E3 ligases tried and commenting on the results in the main text.

Reviewer #2 (Public review):

Summary:

Sereesongsaeng et al. aimed to develop degraders for LMO2, an intrinsically disordered transcription factor activated by chromosomal translocation in T-ALL. The authors first focused on developing biodegraders, which are fusions of an anti-LMO2 intracellular domain antibody (iDAb) with cereblon. Following demonstrations of degradation and collateral degradation of associated proteins with biodegraders, the authors proceeded to develop PROTACs using antibody paratopes (Abd) that recruit VHL (Abd-VHL) or cereblon (Abd-CRBN). The authors show dose-dependent degradation of LMO2 in LMO2+ T-ALL cell lines, as well as concomitant dose-dependent degradation of associated bHLH proteins in the DNA-binding complex. LMO2 degradation via Abd-VHL was also determined to inhibit proliferation and induce apoptosis in LMO2+ T-ALL cell lines.

Strengths:

The topic of degrader development for intrinsically disordered proteins is of high interest, and the authors aimed to tackle a difficult drug target. The authors evaluated methods, including the development of biodegraders, as well as PROTACs that recruit two different E3 ligases. The study includes important chemical control experiments, as well as proteomic profiling to evaluate selectivity.

Weaknesses:

The overall degradation is relatively weak, and the mechanism of potential collateral degradation is not thoroughly evaluated. In addition, experiments comparing the authors' prior work with their anti-LMO2 iDAb or Abl-L are lacking, which would improve our understanding of the potential advantages of a degrader strategy for LMO2.

eLife Assessment

This well-designed, valuable study uses isotope tracing to analyse how iron limitation alters TCA cycle metabolism in Mycobacterium tuberculosis, revealing potential antibiotic targets for non-replicating bacteria in the host. The findings provide insights into metabolic remodelling under iron-limited conditions. Whilst some of the evidence is solid, the data around the GABA shunt is incomplete, requiring genetic validation, as was done for the glyoxylate shunt. Questions remain about the underlying mechanisms and their specific role in M. tuberculosis pathogenesis.

Reviewer #1 (Public review):

M. tuberculosis exhibits metabolic flexibility, enabling it to adapt to various environmental stresses, including antibiotic treatment. In this manuscript, Serafini et al. investigate the metabolic remodeling of M. tuberculosis used to survive iron-limited conditions by employing LC-MS metabolomics and 13C isotope tracing experiments. The results demonstrate that metabolic activity in the oxidative branch of the TCA cycle slows down, while the reductive branch is reverted to facilitate the biosynthesis of malate, which is subsequently secreted.

Overall, this study is experimentally well-designed, particularly the use of 13C isotope tracing to monitor TCA cycle remodeling under iron-limited conditions. The findings are valuable as they offer potential new targets for antibiotics aimed at non-replicating M. tuberculosis occurring in the hosts. However, despite these strengths, the reviewer has concerns regarding the mechanistic basis underlying the observed metabolic remodeling and its role in M. tuberculosis pathogenesis.

Major Comments:

The authors argue that iron starvation is a physiologically relevant stressor encountered by M. tuberculosis post-infection. Using Erdman and H37Rv strains under DFO conditions, Erdman loses viability, whereas H37Rv maintains it. Nonetheless, both strains exhibit similar metabolic remodeling in the TCA cycle based upon metabolomics and isotope tracing data. The authors should clarify the specific metabolic adaptations in H37Rv that enable it to sustain viability under DFO conditions.

The authors report no significant changes in NAD/NADH and ATP levels in H37Rv and Erdman exposed to DFO conditions. They observe TCA cycle remodeling, particularly the reversal of the reaction between OAA and MAL, catalyzed by malate dehydrogenase, an enzyme that uses NAD+ and NADH as cofactors. The directionality of this reaction likely depends on the relative levels of NAD+ and NADH. Additionally, other dehydrogenases, such as pyruvate DH and aKG DH, also require NAD+/NADH cofactors. In Figure 1I, NAD+ and NADH levels are monitored only at day 3 post-exposure to DFO conditions. Since Erdman loses viability after 2-3 weeks, the authors should include measurements of NAD+, NADH, and ATP levels at weekly intervals up to 3 weeks. Furthermore, glycine levels - which are linked to NAD+ recycling via the conversion of glyoxylate - should be measured under both HI and DFO conditions as an indirect indicator of the NAD+/NADH ratio.

In Figure 2A, it is unclear why a 100-fold accumulation of aKG does not correspond proportionally to the accumulation of (iso)citrate.

The authors state that fumarate, aKG, (iso)citrate, malate, and pyruvate are secreted under DFO conditions. While the secretion of aKG and pyruvate makes sense, given their marked intracellular accumulation, it is puzzling why (iso)citrate, malate, and fumarate are secreted even though there are no changes in their intracellular abundance. To rule out the possibility that these metabolites are released due to bacterial lysis rather than active secretion, the authors should analyze the 13C-labeled fractions of these metabolites in the culture filtrate using the M. tuberculosis culture in media containing 13C glycerol.

To validate the role of the PCK-mediated reductive TCA cycle in malate biosynthesis and secretion under DFO conditions, the authors should generate a malate dehydrogenase (MDH) knockdown strain, considering that MDH is essential, and examine the 13C labeling patterns and NAD/NADH under DFO conditions.

The authors also observe decreased GABA abundance and overall 13C labeling in DFO conditions, suggesting that the GABA shunt is the primary route for Succinate biosynthesis under DFO conditions. Thus, it is strongly recommended that the authors perform a 13C glutamate tracing experiment to directly track labeling in aKG and GABA shunt metabolites, providing more definitive evidence for the involvement of the GABA shunt.

Reviewer #2 (Public review):

Summary:

The authors investigated the effect of prolonged iron limitation (which does stop growth but does not lead to cell death), altering central metabolism in M. tuberculosis. The major tool they used is metabolomics combined with stable isotope tracing. They show that the Krebs cycle is still active, despite the fact that it is dependent on some iron-dependent enzymes. They show that carbon flux through the oxidative branch of the Krebs cycle is stalled, resulting in the accumulation of metabolites, such as malate and alpha-ketoglutarate, that are partially secreted. Apparently, the carbon flux from glycolysis is partially diverted to the reductive branch of the Krebs cycle. This is not achieved by using the glyoxylate shunt but probably through the GABA shunt. This unprecedented split of the Krebs cycle and malate secretion allows a continuous flow of carbon through the core of carbon metabolism, overcoming the metabolic stalling triggered by iron starvation.

Strengths:

Novel insight into the central metabolism of a major pathogen and its adaptation to iron starvation. Carefully conducted experimentation. The paper ends with a clear and helpful model.

Weaknesses:

The authors show some surprising and important findings, but they would need a little more effort to really substantiate these. Especially the role of the GABA shunt should be genetically tested, as they did for ICL and the glyoxylate shunt.

Also, dataset 1 is not very convincing, it is only based on transcriptomics and shown with up or down; this is not a strong base for major conclusions. As a minimum, one would want actual differences, preferably on the protein level, where it really counts.

eLife Assessment

This important paper reports the discovery of calcarins, a protein family that seems to be involved in calcification in the calcareous sponge Sycon ciliatum, significantly enhancing our understanding of the molecular and cellular mechanisms underlying spicule formation in sponges and the evolution of carbonate biomineralization. The conclusions are supported by compelling evidence based on an integrated analysis that combines transcriptomics, genomics, proteomics, and precise in situ hybridization. These findings will be of broad interest to cell biologists, biochemists, and evolutionary biologists.

Reviewer #1 (Public review):

To elucidate the mechanisms and evolution of animal biomineralization, Voigt et al. focused on the sponge phylum-the earliest branching extant metazoan lineages exhibiting biomineralized structures-with a particular emphasis on deciphering the molecular underpinnings of spicule formation. This study centered on calcareous sponges, specifically Sycon ciliatum, as characterized in previous work by Voigt et al. In S. ciliatum, two morphologically distinct spicule types are produced by set of two different types of cells that secrete extracellular matrix proteins, onto which calcium carbonate is subsequently deposited. Comparative transcriptomic analysis between a region with active spicule formation and other body regions identified 829 candidate genes involved in this process. Among these, the authors focused on the calcarine gene family, which is analogous to the Galaxins, the matrix proteins known to participate in coral calcification. The authors performed three-dimensional structure prediction using AlphaFold, examined mRNA expression of Calcarin genes in spicule-forming cell types via in situ hybridization, conducted proteomic analysis of matrix proteins isolated from purified spicules, and carried out chromosome arrangement analysis of the Calcarin genes. Based on these analyses, it was revealed that the combination of Calcarin genes expressed during spicule formation differs between the founder cells-responsible for producing diactines and triactines-and the thickener cells that differentiate from them, underscoring the necessity for precise regulation of Calcarin gene expression in proper biomineralization. Furthermore, the observation that 4 Calcarin genes are arranged in tandem arrays on the chromosome suggests that two rounds of gene duplication followed by neofunctionalization have contributed to the intricate formation of S. ciliatum spicules. Additionally, similar subtle spatiotemporal expression patterns and tandem chromosomal arrangements of Galaxins during coral calcification indicate parallel evolution of biomineralization genes between S. ciliatum and aragonitic corals.

Strength:

The study presents detailed and convincing insights that point to parallel evolution of biomineralization in calcitic sponges and corals. This is supported by a comprehensive analysis employing a wide range of experimental approaches including protein tertiary structure predictions, gene expression profiling during calcification (RNA seq and Whole-mount in situ hybridization), and chromosomal sequence analysis.

An integrative research approach, encompassing transcriptomic, genomic, and proteomic analyses as well as detailed FISH.

High-quality FISH images of Calcarin genes, along with a concise summary clearly illustrating their expression patterns, is appreciated.

It was suggested that thickener cells originate from founder cells. To the best of my knowledge, this is the first study to demonstrate trans-differentiation of sponge cells based on the cell-type specific gene expression, as determined by in situ hybridization.

Overall, this is a high-quality piece of work that proposes a compelling scenario for biomineralization.

Weaknesses:

I found no significant weakness in this manuscript.

Comments on revisions:

The authors have addressed all of the questions and recommendations from the prior review.

Reviewer #2 (Public review):

Summary:

This paper reports on the discovery of calcarins, a protein family that seems involved in calcification in the sponge Sycon ciliatum, based on specific expression in sclerocytes and detection by mass spectrometry within spicules. Two aspects stand out: (1) the unexpected similarity between Sycon calcarins and the galaxins of stony corals, which are also involved in mineralization, suggesting a surprising, parallel co-option of similar genes for mineralization in these two groups; (2) the impressively cell-type-specific expression of specific calcarins, many of which are restricted to either founder or thickener cells, and to either diactines, triactines, or tetractines. The finding that calcarins likely diversified at least partly by tandem duplications (giving rise to gene clusters) is a nice bonus.

Strengths:

I enjoyed the thoroughness of the paper, with multiple lines of evidence supporting the hypothesized role of calcarins: spatially and temporally resolved RNAseq, mass spectrometry, and whole-mount in situ hybridization using CISH and HCR-FISH (the images are really beautiful and very convincing). The structural predictions and the similarity to galaxins are very surprising and extremely interesting, as they suggest parallel evolution of biomineralization in sponges and cnidarians during the Cambrian explosion by co-option of the same "molecular bricks".

Weaknesses:

I did not detect any major weakness, beyond those inherent to working with sponges (lack of direct functional inhibition of these genes) or with fast-evolving gene families with complex evolutionary histories (lack of a phylogenetic tree that would clarify the history of galaxins/calcarins and related proteins).

Comments on revisions:

I am fully satisfied with the revision, and notably with the new Figure 3 which is now extremely informative and readable. Congratulations on a job well done.

Reviewer #3 (Public review):

Summary:

Voigt et al. present a comprehensive study exploring the molecular mechanisms and evolution of biomineralization in the calcareous sponge Sycon ciliatum. Using a multi-omics approach, including comparative transcriptomics, proteomics, genomic analyses, and high-resolution in situ hybridization, the authors identify 829 candidate biomineralization genes, with a special focus on the calcarin gene family. These calarains, structurally analogous to galaxin in stony corals, show cell-type- and spicule-type-specific expression patterns, revealed through meticulous FISH imaging. Chromosomal analysis further uncovers that several calcarin genes are arranged in tandem arrays, suggesting diversification via gene duplication and neofunctionalization. Notably, the study finds striking parallels between the calcarins of S. ciliatum and galaxins of aragonitic corals in terms of gene arrangement, tertiary structure predictions, and expression dynamics, pointing to a remarkable case of parallel evolution during the emergence of biomineralized skeletons in early metazoans.

Strengths:

The study is methodologically robust, integrating transcriptomic, proteomic, and genomic data with detailed cell biological analysis.

High-quality, carefully annotated FISH images convincingly demonstrate the spatial expression patterns of calcarins.

Novel evidence of sponge cell trans-differentiation is presented through cell-type-specific gene expression.

The comparative perspective with coral galaxins is well-executed and biologically insightful, supported by structural predictions and chromosomal data.

Figures and supplementary materials are thoughtfully revised for clarity and accessibility, addressing reviewer feedback.

Weaknesses:

Direct functional validation of calcarin roles in biomineralization is lacking, a limitation acknowledged by the authors and inherent to sponge models.

The evolutionary history of calcarins and galaxins remains only partially resolved due to challenges in reconstructing phylogenies of fast-evolving gene families.

Some initial figure annotations and definitions (e.g., "radial tube") required clarification, although these were addressed in revision.

Overall, the work significantly advances our understanding of biomineralization´s molecular basis and its parallel evolution in early diverging metazoans.

Comments on revisions:

I would like to thank the authors for addressing all my comments/suggestions. I am OK with the revised version of the manuscript

Author response:

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

Reviewer #1 (Public review): 

To elucidate the mechanisms and evolution of animal biomineralization, Voigt et al. focused on the sponge phylum - the earliest branching extant metazoan lineages exhibiting biomineralized structures - with a particular emphasis on deciphering the molecular underpinnings of spicule formation. This study centered on calcareous sponges, specifically Sycon ciliatum, as characterized in previous work by Voigt et al. In S. ciliatum, two morphologically distinct spicule types are produced by a set of two different types of cells that secrete extracellular matrix proteins, onto which calcium carbonate is subsequently deposited. Comparative transcriptomic analysis between a region with active spicule formation and other body regions identified 829 candidate genes involved in this process. Among these, the authors focused on the calcarine gene family, which is analogous to the Galaxins, the matrix proteins known to participate in coral calcification. The authors performed three-dimensional structure prediction using AlphaFold, examined mRNA expression of Calcarin genes in spiculeforming cell types via in situ hybridization, conducted proteomic analysis of matrix proteins isolated from purified spicules, and carried out chromosome arrangement analysis of the Calcarin genes.

Based on these analyses, it was revealed that the combination of Calcarin genes expressed during spicule formation differs between the founder cells-responsible for producing diactines and triactinesand the thickener cells that differentiate from them, underscoring the necessity for precise regulation of Calcarin gene expression in proper biomineralization. Furthermore, the observation that 4 Calcarin genes are arranged in tandem arrays on the chromosome suggests that two rounds of gene duplication followed by neofunctionalization have contributed to the intricate formation of S. ciliatum spicules. Additionally, similar subtle spatiotemporal expression patterns and tandem chromosomal arrangements of Galaxins during coral calcification indicate parallel evolution of biomineralization genes between S. ciliatum and aragonitic corals. 

Strengths: 

(1) An integrative research approach, encompassing transcriptomic, genomic, and proteomic analyses as well as detailed FISH. 

(2) High-quality FISH images of Calcarin genes, along with a concise summary clearly illustrating their expression patterns, is appreciated. 

(3) It was suggested that thickener cells originate from founder cells. To the best of my knowledge, this is the first study to demonstrate trans-differentiation of sponge cells based on the cell-typespecific gene expression, as determined by in situ hybridization. 

(4) The comparison between Calcarins of Calcite sponge and Galaxins of aragonitic corals from various perspective-including protein tertiary structure predictions, gene expression profiling during calcification, and chromosomal sequence analysis to reveal significant similarities between them. 

We thank the reviewer for this assessment. 

(1) The conclusions of this paper are generally well supported by the data; however, some FISH images require clearer indication or explanation.

We have modified Fig. 3 by including some insets indicating the depicted part of the sponge body and to change the color-scheme as suggested by reviewer3 for the FISH images. In accordance to the following comment, we decided to remove single-channel views in Fig. 3 A. 

(2) Figure S2 (B, C, D): The fluorescent signals in these images are difficult to discern. If the authors choose to present signals at such low magnification, enhancing the fluorescence signals would improve clarity. Additionally, incorporating Figure S2A as an inset within Figure S2E may be sufficient to convey the necessary information about signal localization. 

We changed the figure according to the suggestions.

(3) Figure S3A: The claim that Cal2-expressing spherical cells are closely associated with the choanoderm at the distal end of the radial tube is difficult to follow. Are these Cal2-expressing spherical cells interspersed among choanoderm cells, or are they positioned along the basal surface of the choanoderm? Clarifying their precise localization and indicating it in the image would strengthen the interpretation. 

In the figure, the view is on the choanoderm that lines the inner surface of the radial tube. Our interpretation is that the spherical cells are positioned at the basal surface of the choanoderm. We updated Fig. S3, which now includes another view to support our interpretation and also indicate some choanocytes.

(4) To further highlight the similarities between S.ciliatum and aragonitic corals in the molecular mechanisms of calcification, consider including a supplementary figure providing a concise depiction of the coral calcification process. This would offer valuable context for readers.

We considered this suggestion, and have included such a supplementary figure (Fig. S9).

Reviewer #2 (Public review): 

Summary: 

This paper reports on the discovery of calcarins, a protein family that seems involved in calcification in the sponge Sycon ciliatum, based on specific expression in sclerocytes and detection by mass spectrometry within spicules. Two aspects stand out: (1) the unexpected similarity between Sycon calcarins and the galaxins of stony corals, which are also involved in mineralization, suggesting a surprising, parallel co-option of similar genes for mineralization in these two groups; (2) the impressively cell-type-specific expression of specific calcarins, many of which are restricted to either founder or thickener cells, and to either diactines, triactines, or tetractines. The finding that calcarins likely diversified at least partly by tandem duplications (giving rise to gene clusters) is a nice bonus. 

Strengths: 

I enjoyed the thoroughness of the paper, with multiple lines of evidence supporting the hypothesized role of calcarins: spatially and temporally resolved RNAseq, mass spectrometry, and whole-mount in situ hybridization using CISH and HCR-FISH (the images are really beautiful and very convincing). The structural predictions and the similarity to galaxins are very surprising and extremely interesting, as they suggest parallel evolution of biomineralization in sponges and cnidarians during the Cambrian explosion by co-option of the same "molecular bricks". 

Weaknesses: 

I did not detect any major weakness, beyond those inherent to working with sponges (lack of direct functional inhibition of these genes) or with fast-evolving gene families with complex evolutionary histories (lack of a phylogenetic tree that would clarify the history of galaxins/calcarins and related proteins). 

We thank the reviewer for this assessment and the detailed comments be addressed below.

Reviewer #3 (Public review):

Summary: 

The study explores the extent to which the biomineralization process in the calcitic sponge Sycon ciliatum resembles aragonitic skeleton formation in stony corals. To investigate this, the authors performed transcriptomic, genomic, and proteomic analyses on S. ciliatum and examined the expression patterns of biomineralization-related genes using in situ hybridization. Among the 829 differentially expressed genes identified in sponge regions associated with spicule formation, the authors focused on calcarin genes, which encode matrix proteins analogous to coral galaxins. The expression patterns of calcarins were found to be diverse but specific to particular spicule types. Notably, these patterns resemble those of galaxins in stony corals. Moreover, the genomic organization of calcarine genes in S. ciliatum closely mirrors that of galaxin genes in corals, suggesting a case of parallel evolution in carbonate biomineralization between calcitic sponges and aragonitic corals. 

Strengths: 

The manuscript is well written, and the figures are of high quality. The study design and methodologies are clearly described and well-suited to addressing the central research question. Particularly noteworthy is the authors´ integration of various omics approaches with molecular and cell biology techniques. Their results support the intriguing conclusion that there is a case of parallel evolution in skeleton-building gene sets between calcitic sponges and aragonitic corals. The conclusions are well supported by the data and analyses presented. 

Weaknesses: 

The manuscript is strong, and I have not identified any significant weaknesses in its current form. 

We thank the reviewer for the insight and addressed the detailed comments below.

Reviewer #1 (Recommendations for the authors): 

The description of the region "radial tube" is unclear. Please define and explain it at its first mention in the manuscript, and, if possible, refer to the appropriate figure(s) (e.g., Figure 1A). 

We now explain radial tubes at the beginning of the results and added a label in figure 1A. “Sycon ciliatum is a tube-shaped sponge with a single apical osculum and a sponge wall of radial tubes around the central atrium (Fig. 1A). The radial tubes are internally lined with choanoderm, which forms elongated chambers in an angle of approximately 90° to the tube axis”. 

Reviewer #2 (Recommendations for the authors): 

Scientific suggestions: 

(1) Page 13: "Despite their presence in the same orthogroups, the octocoral and stony coral proteins were only distantly related to the calcareous sponge calcarins (e.g., 12-24% identity between octocoral and calcareous sequences in orthogroup Cal 2-4-6), resulting in poor alignment. Their homology to calcarins, therefore, remains to be determined." Could 3D structures of these coral proteins be predicted with AlphaFold to substantiate (or nuance) the comparison with calcarins? 

We run additional alphafold predictions for two octocoral and two scleractinian galaxins. A galaxin-like sequence from Pinnigorgia flava was only a short fragment and therefore we did not attempt any structure predictions. The result shows that the octocoral galaxin-like proteins show some structural similarity (12 beta-harpins), while the scleractinian galaxin-like proteins differ from the sponge counterparts of the same orthogroup. We added this information to the results and in the new Fig. S7.

Minor improvements to the text: 

(1)  Page 7 : "The expression of Cal1 to Cal8 was investigated using chromogenic in situ hybridization (CISH) and hairpin-chain reaction fluorescence in situ hybridization (HCR-FISH), confirming their presence in sclerocytes." - Figure 3 should be cited here. 

We refer to the figure now.

(2) Page 8-9: "Cal6 expression mirrors that of Cal2, occurring in rounded cells at the distal tip of radial tubes and in a ring of cells around the oscular ring." - Please cite a figure here. 

We refer now to Fig. 3K

(3) Page 11-12: Please define eigengene, this term is not necessarily common knowledge. 

We provide now a short definition in this sentence: “ The analysis provided eight meta-modules, of which four showed significant changes in expression module eigengenes —summary profiles that capture the overall expression pattern of each module— between samples with high spicule formation context (osculum region and regeneration stages older than four days) and samples with low spicule formation (sponge-wall and early regeneration stages until day 3-4) (Fig. S5).” 

(4) Page 13: "Species without skeletons, such as the cnidarians Hydra, Actinia, Exaiptasia, and Nematostella, also possess galaxin-like proteins." This is too concise - can you explain what evidence was used? PANTHER, AlphaFold, OrthoFinder, Blastp...? 

The evidence used is from PANTHER, and we enhanced clarification of this by modifying the last sentence of the section.

(5) Page 20: "We have identified calcarins, galaxin-like proteins, as crucial components of the biomineralization toolkit in calcareous sponges." I'm not sure you showed they are crucial (this would require functional evidence). Perhaps "novel" components or some other adjective would fit better. 

We changed the adjective to “novel”.

Suggestions for the figures: 

(1) Figure 1A: radial tubes should be labelled. 

A label was added.

(2) Figure 3 is beautiful but hard to parse. The name of all markers should be written on each panel (notably B, C, and D) and ideally placed in a consistent position (top right corner?) so that the reader's eye doesn't have to look for them anew in each panel. Consider depicting the same gene with the same color in all panels if possible (confocal imaging gives virtual colors anyway, there's no reason to be bound to the real-life color of the fluorophores used - if that was the original intent). Finally, the red/green color scheme is not colorblind-readable, so please consider switching to another scheme (white/cyan/magenta, for example).

We have updated the figure according to the suggestions. The names of all markers are now included on each panel. Placing them in the upper right corner was not feasible for all panels, so we adjusted their placement as needed. Reoccurring genes are shown in the same color where possible. To improve accessibility for individuals with red/green color vision deficiency, we adopted a cyan/magenta/yellow color scheme. Each HCR-FISH image was processed in ImageJ by splitting the image into channels, applying cyan, magenta, or yellow lookup tables, converting each channel to RGB, and then stacking and blending them using the Z-Project function with maximum intensity projection. Since the original channel information is not preserved after this processing, we provide the original red/green/blue version of the figure in the supplementary material in Fig S11. Additionally, we added small sketches of Figure 1A to indicate the sponge body regions depicted, where relevant.

(3) Figure S3: the blue staining is not explained. It is also unclear where choanocytes are - could individual choanocytes be indicated with arrows or lines? 

We added the information to the figure legend. The blue channel shows “Autofluorescence detected with the Leica TXR filter (approx. 590–650 nm), included to help distinguish true signal from background autofluorescence observed in the FITC channel (used for Spiculin detection).”

Reviewer #3 (Recommendations for the authors): 

I have no major concerns about the manuscript - only minor edits and comments, which are listed below: 

(1) On page 13, the authors refer to Figure S8; however, I believe this should be Figure S7. 

We now refer to the correct Figure. Because of introducing a new Fig. S7, now the correct reference is Fig. S8.

(2) On page 16, please correct "Spciulin" to "Spiculin". 

Now corrected.

(3) On page 17, there are two commas following "(Sycon)"; please remove one. 

Corrected.

(4) In the Data Accessibility section, none of the provided links appear to work. Please ensure all links are functional. 

We apologize for this oversight and now provide working links. 

(5) In Figure 3, the description of panel L is missing from the figure legend. 

We added the description of this panel.

(6) On page 39, change "Fig. 4" to "Figure 4" to maintain consistency throughout the manuscript. 

Changed.

(7) Figure S7 is not cited in the main text. Please, address this. 

Corrected (see above at point 1)

(8) In the legend for Table S2, the reference to Soubigou et al. (3) is incorrect, as it is not listed in the SI reference section. Please correct this. 

Soubigou et al. (2020) is now included in the SI reference list.

eLife Assessment

This revised study provides fundamental insights into the differences in migratory primordial germ cells based on their anterior or posterior location. Through convincing methodology and analysis of single-cell RNA sequencing of an exceptionally large number of migratory primordial germ cells and surrounding somatic cells, the novel findings and datasets generated from this study provide many hypotheses of interest to germ cell biologists.

Reviewer #1 (Public review):

Summary:

Migration of the primordial germ cells (PGCs) in mice is asynchronous, such that leading and lagging populations of migrating PGCs emerge. Prior studies found that interactions between the cells the PGCs encounter along their migration routes regulates their proliferation. In this study, the authors used single cell RNAseq to investigate PGC heterogeneity and to characterize their niches during their migration along the AP axis. Unlike prior scRNAseq studies of mammalian PGCs, the authors conducted a time course covering 3 distinct stages of PGC migration (pre, mid, and post migration) and isolated PGCs from defined somite positions along the AP axis. In doing so, this allowed the authors to uncover differences in gene expression between leading and lagging PGCs and their niches and to investigate how their transcript profiles change over time. Among the pathways with the biggest differences were regulators of actin polymerization and epigenetic programming factors and Nodal response genes. In addition, the authors report changes in somatic niches, specifically greater non-canonical WNT in posterior PGCs compared to anterior PGCs. This relationship between the hindgut epithelium and migrating PGCs was also detected in reanalysis of a previously published dataset of human PGCs. Using whole mount immunofluorescence, the authors confirmed elevated Nodal signaling based on detection of the LEFTY antagonists and targets of Nodal during late stage PGC migration. Taken together, the authors have assembled a temporal and spatial atlas of mouse PGCs and their niches. This resource and the data herein provide support for the model that interactions of migrating mouse PGCs with their niches influences their proliferation, cytoskeletal regulation, epigenetic state and pluripotent state.

Overall, the findings provide new insights into heterogeneity among leading and lagging PGC populations and their niches along the AP axis, as well as comparisons between mouse and human migrating PGCs. The data are clearly presented, and the text is clear and well-written. This atlas resource will be valuable to reproductive and developmental biologists as a tool for generating hypotheses and for comparisons of PGCs across species.

Strengths:

(1) High quality atlas of individual PGCs prior to, during and post migration and their niches at defined positions along the AP axis.

(2) Comparisons to available datasets, including human embryos, provide insight into potentially conserved relationships among PGCs and the identified pathways and gene expression changes.

(3) Detailed picture of PGC heterogeneity.

(4) Valuable resource for the field.

(5) Some validation of Nodal results and further support for models in the literature based on less comprehensive expression analysis.

Reviewer #2 (Public review):

Summary:

Germ cells go on to form sperm and eggs and are, therefore, critical for the survival of the species. This work addresses the question of how 'leading' and 'lagging' PGCs differ, molecularly, during their migration to the mouse genital ridges/gonads during fetal life (E9.5, E10.5, E11.5), and how this is regulated by different somatic environments encountered during the process of migration. E9.5 and E10.5 cells differed in expression of genes involved in canonical WNT signaling and focal adhesions. Differences in cell adhesion, actin cytoskeletal dynamics were identified between leading and lagging cells, at E9.5, before migration into the gonads. At E10.5, when some PGCs have reached the genital ridges, differences in Nodal signaling response genes and reprogramming factors were identified. This last point was verified by whole mount IF for proteins downstream of Nodal signaling, Lefty1/2. At E11.5, there was upregulation of genes associated with chromatin remodeling and oxidative phosphorylation. Some aspects of the findings were also found to be likely true in human development, established via analysis of a dataset previously published by others.

Strengths:

The work is strong in that a large number of PGCs were isolated and sequenced, along with associated somatic cells. The authors dealt with the problem of a very small number of migrating mouse PGCs by pooling cells from embryos (after ascertaining age matching using somite counting). 'Leading' and 'lagging' populations were separated by anterior and posterior embryo halves and the well-established Oct4-deltaPE-eGFP reporter mouse line was used.

The most likely possible use of this fundamental information will be the incorporation of some aspects (e.g. the potential importance of Nodal signaling) into protocols for generation of in vitro derived gametes.

Reviewer #3 (Public review):

Summary:

The migration of primordial germ cells (PGCs) to the developing gonad is a poorly understood yet essential step in reproductive development. Here, the authors examine whether there are differences in leading and lagging migratory PGCs using single-cell RNA sequencing of mouse embryos. Cleverly, the authors dissected embryonic trunks along the anterior-to-posterior axis prior to scRNAseq in order to distinguish leading and lagging migratory PGCs. After batch corrections, their analyses revealed several known and novel differences in gene expression within and around leading and lagging PGCs, intercellular signaling networks, as well as number of genes upregulated upon gonad colonization. The authors then compared their datasets with publicly available human datasets to identify common biological themes. Altogether, this rigorous study reveals several differences between leading and lagging migratory PGCs, hints at signatures for different fates among the population of migratory PGCs, and provides new potential markers for post-migratory PGCs in both humans and mice. While many of the interesting hypotheses that arise from this work are not extensively tested, these data provide a rich platform for future investigations.

Strengths:

The authors have successfully navigated significant technical challenges to obtain a substantial number of mouse migratory primordial germ cells for robust transcriptomic analysis. Here, the authors were able to collect quality data on ~13,000 PGCs and ~7,800 surrounding somatic cells, which is ten times more PGCs than previous studies.

The decision to physically separate leading and lagging primordial germ cells was clever and well-validated based on expected anterior-to-posterior transcriptional signatures.

Within the PGCs and surrounding tissues, the authors found many gene expression dynamics they would expect to see both along the PGC migratory path as well as across developmental time, increasing confidence in the new differentially expressed genes they found.

The comparison of their mouse-based migratory PGC datasets with existing human migratory PGC datasets is appreciated.

The quality control, ambient RNA contamination elimination, batch correction, cell identification and analysis of scRNAseq data were thorough and well-done such that the new hypotheses and markers found through this study are dependable.

The subsetting of cells in their trajectory analysis is appreciated, further strengthening their cell terminal state predictions.

Weaknesses:

There were a few validation experiments within this study. For one such experiment, whether there is a difference in pSMAD2/3 along the AP axis is unclear and not quantified, as was nicely done for Lefty1/2.

Author response:

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

Reviewer #1 (Public review):

Summary:

Migration of the primordial germ cells (PGCs) in mice is asynchronous, such that leading and lagging populations of migrating PGCs emerge. Prior studies found that interactions between the cells the PGCs encounter along their migration routes regulates their proliferation. In this study, the authors used single cell RNAseq to investigate PGC heterogeneity and to characterize their niches during their migration along the AP axis. Unlike prior scRNAseq studies of mammalian PGCs, the authors conducted a time course covering 3 distinct stages of PGC migration (pre, mid, and post migration) and isolated PGCs from defined somite positions along the AP axis. In doing so, this allowed the authors to uncover differences in gene expression between leading and lagging PGCs and their niches and to investigate how their transcript profiles change over time. Among the pathways with the biggest differences were regulators of actin polymerization and epigenetic programming factors and Nodal response genes. In addition, the authors report changes in somatic niches, specifically greater non-canonical WNT in posterior PGCs compared to anterior PGCs. This relationship between the hindgut epithelium and migrating PGCs was also detected in reanalysis of a previously published dataset of human PGCs. Using whole mount immunofluorescence, the authors confirmed elevated Nodal signaling based on detection of the LEFTY antagonists and targets of Nodal during late stage PGC migration. Taken together, the authors have assembled a temporal and spatial atlas of mouse PGCs and their niches. This resource and the data herein provide support for the model that interactions of migrating mouse PGCs with their niches influences their proliferation, cytoskeletal regulation, epigenetic state and pluripotent state.

Overall, the findings provide new insights into heterogeneity among leading and lagging PGC populations and their niches along the AP axis, as well as comparisons between mouse and human migrating PGCs. The data are clearly presented, and the text is clear and well-written. This atlas resource will be valuable to reproductive and developmental biologists as a tool for generating hypotheses and for comparisons of PGCs across species.

Strengths:

(1) High quality atlas of individual PGCs prior to, during and post migration and their niches at defined positions along the AP axis.

(2) Comparisons to available datasets, including human embryos, provide insight into potentially conserved relationships among PGCs and the identified pathways and gene expression changes.

(3) Detailed picture of PGC heterogeneity.

(4) Valuable resource for the field.

(5) Some validation of Nodal results and further support for models in the literature based on less comprehensive expression analysis.

Weaknesses:

(1) No indication of which sex(es) were used for the mouse data and whether or not sex-related differences exist or can excluded at the stages examined. This should be clarified.

We have added: “Embryos of both sexes were pooled without genotyping, as the timepoints analyzed were prior to sex specification” to both the Animals section of the Materials and Methods and the Figure 1 legend. In addition, bioinformatic evaluation of potential sex biases in Nodal-Lefty signaling using Y-chromosome gene expression is reported in supplementary figure 4 and discussed in Discussion paragraph 2.

Reviewer #2 (Public review):

Summary:

This work addresses the question of how 'leading' and 'lagging' PGCs differ, molecularly, during their migration to the mouse genital ridges/gonads during fetal life (E9.5, E10.5, E11.5), and how this is regulated by different somatic environments encountered during the process of migration. E9.5 and E10.5 cells differed in expression of genes involved in canonical WNT signaling and focal adhesions. Differences in cell adhesion, actin cytoskeletal dynamics were identified between leading and lagging cells, at E9.5, before migration into the gonads. At E10.5, when some PGCs have reached the genital ridges, differences in Nodal signaling response genes and reprogramming factors were identified. This last point was verified by whole mount IF for proteins downstream of Nodal signaling, Lefty1/2. At E11.5, there was upregulation of genes associated with chromatin remodeling and oxidative phosphorylation. Some aspects of the findings were also found to be likely true in human development, established via analysis of a dataset previously published by others.

Strengths:

The work is strong in that a large number of PGCs were isolated and sequenced, along with associated somatic cells. The authors dealt with problem of very small number of migrating mouse PGCs by pooling cells from embryos (after ascertaining age matching using somite counting). 'Leading' and 'lagging' populations were separated by anterior and posterior embryo halves and the well-established Oct4-deltaPE-eGFP reporter mouse line was used.

Weaknesses:

The work seems to have been carefully done, but I do not feel the manuscript is very accessible, and I do not consider it well written. The novel findings are not easy to find. The addition of at least one figure to show the locations of putative signaling etc. would be welcome.

Thank you for the excellent suggestion. Fig. 6 has been added to highlight the main novel findings of this work and integrate them among contributions of earlier studies to provide a more complete view of signaling pathways and cell behaviors governing PGC migration.

(1) The initial discussion of CellRank analysis (under 'Transcriptomic shifts over developmental time...' heading) is somewhat confusing - e.g. If CellRank's 'pseudotime analysis' produces a result that seems surprising (some E9.5 cells remain in a terminal state with other E9.5 cells) and 'realtime analysis' produces something that makes more sense, is there any point including the pseudotime analysis (since you have cells from known timepoints)? Perhaps the 'batch effects' possible explanation (in Discussion) should be introduced here. Do we learn anything novel from this CellRank analysis? The 'genetic drivers' identified seem to be genes already known to be key to cell transitions during this period of development.

Thank you for this important observation. We have clarified the text in this section and added “This discrepancy may reflect differences in differentiation potential of some E9.5 PGCs that end in a terminal state among anterior E9.5 PGCs, but could also result from technical batch effects generated during library preparation. These possible interpretations are further discussed in the Discussion section.” to the pertinent results section and added additional relevant thoughts on the implications of this finding in Discussion paragraphs 4 and 7. We feel that it is important to include both results to the reader, as it is challenging to differentiate between heterogeneous developmental and migratory potential among E9.5 anterior PGCs and differential influence of batch effects across sequencing libraries with the data available.

(2) In Discussion - with respect to Y-chromosome correlation, it is not clear why this analysis would be done at E10.5, when E11.5 data is available (because some testis-specific effect might be more apparent at the later stage).

Since we had identified autocrine Nodal signaling primarily in anterior late migratory PGCs at E10.5 and knew that Nodal signaling was involved in sex specification of testicular germ cells into prospermatogonia by E12.5, we wanted to determine whether the Nodal signaling in late migratory PGCs at E10.5 was likely to be a sex-specific effect or was common to PGCs in both sexes. This was assessed in supplementary figure 4 and determined unlikely to be related to sex specification of PGCs as Nodal signaling was not strongly correlated with Y-chromosome transcripts in migratory PGCs. Assessing the relationship between Nodal signaling and Y-chromsome transcription at E11.5, when migration is complete, would be unlikely to help us further understand the dynamics of Nodal signaling during late PGC migration.

(3) Figure 2A - it seems surprising that there are two clusters of E9.5 anterior cells

Thank you for the interesting observation! One possibility is that the two states represent differential developmental competence as is suggested by the presence of one E9.5 anterior cluster along the differentiation trajectory in Fig 2A and one not within this differentiation trajectory. Another is that technical aspects of generating these sequencing libraries affected some cells more than others, resulting in clustering of highly affected and less affected cells, which would also be consistent with some E9.5 anterior cells lying within the differentiation trajectory and some not. Since it is challenging to differentiate between these possibilities with the data available, we have intentionally avoided overstating interpretations of this result in the manuscript text. We have included discussion of the potential implications of the transcriptional divergence you identify in Discussion paragraphs 4 and 7.

(4) Figure 5F - there does seem to be more LEFTY1/2 staining in the anterior region, but also more germ cells as highlighted by GFP

This is true; based on our selected anatomic landmarks for “anterior” and “posterior” as indicated in Methods, the “anterior” compartment typically contains more PGCs. Thus, we have included violin plots with all data points shown of signal intensities of both LEFTY1/2 and pSMAD2/3 in Fig. 5G and 5I so that the reader can evaluate the entire distribution of PGC signal intensities for each embryo.

Reviewer #3 (Public review):

Summary:

The migration of primordial germ cells (PGCs) to the developing gonad is a poorly understood, yet essential step in reproductive development. Here, the authors examine whether there are differences in leading and lagging migratory PGCs using single-cell RNA sequencing of mouse embryos. Cleverly, the authors dissected embryonic trunks along the anterior-to-posterior axis prior to scRNAseq in order to distinguish leading and lagging migratory PGCs. After batch corrections, their analyses revealed several known and novel differences in gene expression within and around leading and lagging PGCs, intercellular signaling networks, as well as number of genes upregulated upon gonad colonization. The authors then compared their datasets with publicly available human datasets to identify common biological themes. Altogether, this rigorous study reveals several differences between leading and lagging migratory PGCs, hints at signatures for different fates among the population of migratory PGCs, and provides new potential markers for post-migratory PGCs in both humans and mice. While many of the interesting hypotheses that arise from this work are not extensively tested, these data provide a rich platform for future investigations.

Strengths:

The authors have successfully navigated significant technical challenges to obtain a substantial number of mouse migratory primordial germ cells for robust transcriptomic analysis. Here the authors were able to collect quality data on ~13,000 PGCs and ~7,800 surrounding somatic cells, which is ten times more PGCs than previous studies.

The decision to physically separate leading and lagging primordial germ cells was clever and well-validated based on expected anterior-to-posterior transcriptional signatures.

Within the PGCs and surrounding tissues, the authors found many gene expression dynamics they would expect to see both along the PGC migratory path as well as across developmental time, increasing confidence in the new differentially expressed genes they found.

The comparison of their mouse-based migratory PGC datasets with existing human migratory PGC datasets is appreciated.

The quality control, ambient RNA contamination elimination, batch correction, cell identification and analysis of scRNAseq data were thorough and well-done such that the new hypotheses and markers found through this study are dependable.

The subsetting of cells in their trajectory analysis is appreciated, further strengthening their cell terminal state predictions.

Weaknesses:

Although it is useful to compare their mouse-based dataset with human datasets, the authors used two different analysis pipelines for each dataset. While this may have been due to the small number of cells in the human dataset as mentioned, it does make it difficult to compare them.

Direct comparisons between findings in human and mouse focused on CellChat cell-cell communication prediction results, which were conducted in an identical fashion using the same analysis methods for both datasets.

There were few validation experiments within this study. For one such experiment, whether there is a difference in pSMAD2/3 along the AP axis is unclear and not quantified as was nicely done for Lefty1/2.

Additional validation of the pSMAD2/3 signal intensity along the AP axis was performed and is now included in Fig. 5.

eLife Assessment

This valuable study highlights how the diversity of the malaria parasite population diminishes following the initiation of effective control interventions but quickly rebounds as control wanes. It also demonstrates that the asymptomatic reservoir is unevenly distributed across host age groups. The data presented are convincing and the work shows how genetic studies could be used to monitor changes in disease transmission.

Reviewer #2 (Public review):

In this manuscript, Tiedje and colleagues longitudinally track changes in parasite number across four time points as a way of assessing the effect of malaria control interventions in Ghana. Some of the study results have been reported previously, and in this publication, the authors focus on age-stratification of the results. Malaria prevalence was lower in all age groups after IRS. Follow-up with SMC, however, maintained lower parasite prevalence in the targeted age group but not the population as a whole. Additionally, they observe that diversity measures rebound more slowly than prevalence measures. This adds to a growing literature that demonstrates the relevance of asymptomatic reservoirs.

Overall, I found these results clear, convincing, and well presented. There is growing interest in developing an expanded toolkit for genomic epidemiology in malaria, and detecting changes in transmission intensity is one major application. As the authors summarize, there is no one-size-fits-all approach, and the Bayesian MOIvar estimate developed here has the potential to complement currently used methods, particularly in regions with high diversity/transmission. I find its extension to a calculation of absolute parasite numbers appealing as this could serve as both a conceptually straightforward and biologically meaningful metric.

As the authors address, their use of the term "census population size" is distinct from how the term is used in the population genetics literature. I therefore anticipate that parasite count will be most useful in an epidemiological context where the total number of sampled parasites can be contrasted with other metrics to help us better understand how parasites are divided across hosts, space, and time.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #2 (Public review): 

In this manuscript, Tiedje and colleagues longitudinally track changes in parasite numbers across four time points as a way of assessing the effect of malaria control interventions in Ghana. Some of the study results have been reported previously, and in this publication, the authors focus on age-stratification of the results. Malaria prevalence was lower in all age groups after IRS. Follow-up with SMC, however, maintained lower parasite prevalence in the targeted age group but not the population as a whole. Additionally, they observe that diversity measures rebound more slowly than prevalence measures. This adds to a growing literature that demonstrates the relevance of asymptomatic reservoirs. 

Strengths:  

Overall, I found these results clear, convincing, and well-presented. There is growing interest in developing an expanded toolkit for genomic epidemiology in malaria, and detecting changes in transmission intensity is one major application. As the authors summarize, there is no one-size-fits-all approach, and the Bayesian MOIvar estimate developed here has the potential to complement currently used methods, particularly in regions with high diversity/transmission. I find its extension to a calculation of absolute parasite numbers appealing as this could serve as both a conceptually straightforward and biologically meaningful metric.

We thank the reviewer for this positive review of our results and approach.

Weaknesses:

While I understand the conceptual importance of distinguishing among parasite prevalence, mean MOI, and absolute parasite number, I am not fully convinced by this manuscript's implementation of "census population size".

This reviewer remains unconvinced of the use of the term “census population size”. This appears to be due to the dependence of the term on sample size rather than representing a count of a whole population. To give context to our use we are clear in the study presented that the term describes a count of the parasite “strains” in an age-specific sample of a human population in a specified location undergoing malaria interventions. 

They have suggested instead using “sample parasite count”.  We argue that this definition is too specific and less applicable when we extrapolate the same concept to a different denominator, such as the population in a given area. Importantly, our ecological use of a census allows us to count the appearance of the same strain more than once should this occur in different people. 

The authors reference the population genetic literature, but within the context of that field, "census population size" refers to the total population size (which, if not formally counted, can be extrapolated) as opposed to "effective population" size, which accounts for a multitude of demographic factors. There is often interesting biology to be gleaned from the magnitude of difference between N and Ne.

As stated in the introduction we have been explicit in saying that we are not using a population genetic framework. Exploration of N and Ne in population genetics has merit. How this is reconciled when using a “strain” definition and not neutral markers would need to be assessed.  

In this manuscript, however, "census population size" is used to describe the number of distinct parasites detected within a sample, not a population. As a result, the counts do not have an immediate population genetic interpretation and cannot be directly compared to Ne. This doesn't negate their usefulness but does complicate the use of a standard population genetic term.

We are clear we are defining a census of parasite strains in an age-specific sample of a population living in two catchment areas of Bongo District. We appreciate the concern of the reviewer and have now further edited the relevant paragraphs in both the Introduction (Lines 75-80) and the Discussion (Lines 501-506) to make very clear the dependence of the reported quantity on sample size, but also its feasible extrapolation consistent with the census of a population. 

In contrast, I think that sample parasite count will be most useful in an epidemiological context, where the total number of sampled parasites can be contrasted with other metrics to help us better understand how parasites are divided across hosts, space and time. However, for this use, I find it problematic that the metric does not appear to correct for variations in participant number. For instance, in this study, participant numbers especially varied across time for 1-5 year-olds (N=356, 216, 405, and 354 in 2012, 2014, 2015, and 2017 respectively).

The reviewer has made an important point that for the purpose of comparisons across the four surveys or study time points (i.e., 2012, 2014, 2015, and 2017), we should "normalize" the number of individuals considered for the calculation of the "census population size".  Given that this quantity is a sum of the estimated MOI_var,, we need to have constant numbers for its values to be compared across the surveys, within age group and the whole population. This is needed not only to get around the issue of the drop in 1-5 year olds surveyed in 2014 but to also stabilize the total number of individuals for the whole sample and for specific age groups. One way to do this is to use the smaller sample size for each age group across time, and to use that value to resample repeatedly for that number of individuals for surveys where we have a larger sample size. This has now been updated included in the manuscript as described in the Materials and Methods (Lines 329-341) and in the Results (Lines 415-430; see updated Figure 4 and Table supplement 7). This correction produces very similar results to those we had presented before (see updated Figure 4 and Table supplement 7).   

As stated in our previous response we have used participant number in an interrupted time series where the population was sampled by age to look at age-specific effects of sequential interventions IRS and SMC. As shown in Table supplement 1 of the 16 age-specific samples of the total population, we have sampled very similar proportions of the population by age group across the four surveys. The only exception was the 1-5 year-old age group during the survey in 2014. We are happy to provide additional details to further clarify the lower number (or percentage) of 1-5 year olds (based on the total number of participants per survey) in 2014 (~12%; N = 216) compared to the other surveys conducted 2012, 2015, and 2017 (~18-20%; N = 356, 405, and 354, respectively). Please see Table supplement 1 for the total number of participants surveyed in each of the four surveys (i.e., 2012, 2014, 2015, and 2017).   

This sample size variability is accounted for with other metrics like mean MOI. 

We agree that mean MOI by age presents a way forward with variable samples to scale up. Please see updated Figure supplement 8.  

In sum, while the manuscript opens up an interesting discussion, I'm left with an incomplete understanding of the robustness and interpretability of the new proposed metric.”

We thank you for your opinion. We have further edited the manuscript to make clear our choice of the term and the issue of sample size.  We believe the proposed terminology is meaningful as explained above.

Reviewer #3 (Public review): 

Summary

The manuscript coins a term "the census population size" which they define from the diversity of malaria parasites observed in the human community. They use it to explore changes in parasite diversity in more than 2000 people in Ghana following different control interventions. 

Strengths:

This is a good demonstration of how genetic information can be used to augment routinely recorded epidemiological and entomological data to understand the dynamics of malaria and how it is controlled. The genetic information does add to our understanding, though by how much is currently unclear (in this setting it says the same thing as age stratified parasite prevalence), and its relevance moving forward will depend on the practicalities and cost of the data collection and analysis. Nevertheless, this is a great dataset with good analysis and a good attempt to understand more about what is going on in the parasite population.

Thank you to the reviewer for their supportive assessment of our research.

Weaknesses

None

Reviewer #3 (Recommendations for the authors): 

New figure supplement 8 - x-axis says percentage but goes between 0-1, so is a proportion

We thank the reviewer for bringing this to our attention. We have amended the x-axis labels accordingly for Figure supplement 8.

eLife Assessment

This study presents fundamental new findings introducing a new approach for the reprogramming of brain glial cells to corticospinal neurons. The data is highly compelling, with multiple lines of evidence demonstrating the success of this new assay. These exciting findings set the stage for future studies of the potential of these reprogrammed cells to form functional connections in vivo and their utility in clinical conditions where corticospinal neurons are compromised.

Reviewer #1 (Public review):

Summary:

The manuscript by Ozcan et al., presents compelling evidence demonstrating the latent potential of glial precursors of the adult cerebral cortex for neuronal reprogramming. The findings substantially advance our understanding of the potential of endogenous cells in the adult brain to be reprogrammed. Moreover, they describe a molecular cocktail that directs reprogramming toward corticospinal neurons (CSN).

Strengths:

Experimentally, the work is compelling and beautifully designed. The work provides a characterization of endogenous progenitors, genetic strategies to isolate them, and proof of concept of exploiting these progenitors' potential to produce a specific desired neuronal type with "a la carte" combination of transcription factors.

Weaknesses:

This study demonstrates reprogramming in vitro. Future research will need to assess how these reprogrammed corticospinal neurons integrate and function under physiological conditions and in models of trauma or neurodegeneration.

Although still in its early stages, neural reprogramming holds significant promise. This study reinforces the hope that, in the future, it may be possible to restore lost or damaged neurons through targeted cellular reprogramming.

Reviewer #2 (Public review):

Summary:

Here the authors show a novel direct neuronal reprogramming model using a very pure culture system of oligodendrocyte progenitor cells and demonstrate hallmarks of corticospinal neurons to be induced when using Neurogenin2, a dominant-negative form of Olig2 in combination with the CSN master regulator Fezf2.

Strengths:

This is a major achievement as the specification of reprogrammed neurons towards adequate neuronal subtypes is crucial for repair and is still largely missing. The work is carefully done, and the comparison of the neurons induced only by Neurogenin 2 versus the NVOF cocktail is very interesting and convincingly demonstrates a further subtype specification by the cocktail.

Weaknesses:

As carefully as it is done in vitro, the identity of projection neurons can best be assessed in vivo. If this is not possible, it could be interesting to co-culture different brain regions and see if these neurons reprogrammed with the cocktail, indeed preferentially send out axons to innervate a co-cultured spinal cord versus other brain region tissue.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The manuscript by Ozcan et al., presents compelling evidence demonstrating the latent potential of glial precursors of the adult cerebral cortex for neuronal reprogramming. The findings substantially advance our understanding of the potential of endogenous cells in the adult brain to be reprogrammed. Moreover, they describe a molecular cocktail that directs reprogramming toward corticospinal neurons (CSN).

Strengths:

Experimentally, the work is compelling and beautifully designed, with no major caveats. The main conclusions are fully supported by the experiments. The work provides a characterization of endogenous progenitors, genetic strategies to isolate them, and proof of concept of exploiting these progenitors' potential to produce a specific desired neuronal type with "a la carte" combination of transcription factors.

Weaknesses:

Some issues need to be addressed or clarified before publication. The manuscript requires editing. It is dense and rich in details while in other parts there are a few mistakes.

We thank the reviewer for their excellent summary and for their extremely positive review of our paper. We are pleased that the experimental design and conclusions were judged to be wellsupported.

We have revised the paper to enhance clarity, include additional relevant citations, and refine terminology in some sections of the original version.

We appreciate the reviewer’s thoughtful review and agree that these revisions enhance the paper.

Reviewer #2 (Public Review):

Summary:

Here the authors show a novel direct neuronal reprogramming model using a very pure culture system of oligodendrocyte progenitor cells and demonstrate hallmarks of corticospinal neurons to be induced when using Neurogenin2, a dominant-negative form of Olig2 in combination with the CSN master regulator Fezf2.

Strengths:

This is a major achievement as the specification of reprogrammed neurons towards adequate neuronal subtypes is crucial for repair and still largely missing. The work is carefully done and the comparison of the neurons induced only by Neurogenin 2 versus the NVOF cocktail is very interesting and convincingly demonstrates a further subtype specification by the cocktail.

Weaknesses:

As carefully as it is done in vitro, the identity of projection neurons can best be assessed in vivo. If this is not possible, it could be interesting to co-culture different brain regions and see if these neurons reprogrammed with the cocktail, indeed preferentially send out axons to innervate a co-cultured spinal cord versus other brain region tissue.

We appreciate the reviewer’s positive evaluation of our work and their recognition of its significance in advancing neuronal subtype specification through directed differentiation of endogenous progenitors. 

We agree with the reviewer’s suggestion that a very interesting future stage of this work would be to investigate the projection neuron identity in vivo. We aim to pursue follow-up studies to investigate in vivo integration and connectivity of such neurons generated by directed differentiation from endogenous SOX6+/NG2+ cortical progenitors. As the reviewer insightfully suggests, co-culturing different brain regions with these neurons could offer an alternative strategy to partially assess potential preferential connectivity into cultured spinal cord vs. alternate tissue.

We agree with the reviewer that future investigation in vivo will further strengthen the implications of this work.

Reviewer #3 (Public Review):

Summary:

Ozkan, Padmanabhan, and colleagues aim to develop a lineage reprogramming strategy towards generating subcerebral projection neurons from endogenous glia with the specificity needed for disease modelling and brain repair. They set out by targeting specifically Sox6-positive NG2 glia. This choice is motivated by the authors' observation that the early postnatal forebrain of Sox6 knockout mice displays marked ectopic expression of the proneural transcription factor (TF) Neurog2, suggesting a latent neurogenic program may be derepressed in NG2 cells, which normally express Sox6. Cultured NG2 glia transfected with a construct ("NVOF") encoding Neurog2, the corticofugal neuron-specifying TF Fezf2, and a constitutive repressor form of Olig2 are efficiently reprogrammed to neurons. These acquire complex morphologies resembling those of mature endogenous neurons and are characterized by fewer abnormalities when compared to neurons induced by Neurog2 alone. NVOF-induced neurons, as a population, also express a narrower range of cortical neuron subtype-specific markers, suggesting narrowed subtype specification, a potential step forward for Neurog2-driven neuronal reprogramming. Comparison of NVOF- and Neurog2-induced neurons to endogenous subcerebral projection neurons (SCPN) also indicates Fezf2 may aid Neurog2 in directing the generation of SCPN-like neurons at the expense of other cortical neuronal subtypes.

Strengths:

The report describes a novel, highly homogeneous in vitro system amenable to efficient reprogramming. The authors provide evidence that Fezf2 shapes the outcome of Neurog2-driven reprogramming towards a subcerebral projection neuron identity, consistent with its known developmental roles. Also, the use of the modified RNA for transient expression of Neurog2 is very elegant.

Weaknesses:

The molecular characterization of NVOF-induced neurons is carried out at the bulk level, therefore not allowing to fully assess heterogeneity among NVOF-induced neurons. The suggestion of a latent neurogenic potential in postnatal cortical glia is only partially supported by the data from the Sox6 knockout. Finally, some of the many exciting implications of the study remain untested.

Discussion:

The study has many exciting implications that could be further tested. For example, an ultimate proof of the subcerebral projection neuron identity would be to graft NVOF cells into neonatal mice and study their projections. Another important implication is that Sox6-deficient NG2 glia may not only express Neurog2 but activate a more complete neurogenic programme, a possibility that remains untested here.

Also, is the subcerebral projection neuron dependent on the starting cell population? Could other NG2 glia, not expressing Sox6, also be co-axed by the NVOF cocktail into subcerebral projection neurons? And if not, do they express other (Sox) transcription factors that render them more amenable to reprogramming into other cortical neuron subtypes? The authors state that SOX6-positive NG2 glia are a quiescent progenitor population. Given that NG2 glia is believed to undergo proliferation as a whole, are Sox6-positive NG2 glia an exception from this rule? Finally, the authors seem to imply that subcerebral projection neurons and Sox6-positive NG2 glia are lineage-related. However, direct evidence for this conjecture seems missing.

We appreciate the reviewer’s thoughtful and detailed review of this work. We especially appreciate the positive evaluation of the work and the highlighting of multiple strengths of our approach, including the role of Fezf2 in refining neuronal subtype identity and the use of modified RNA to enable transient expression of Neurog2.

We acknowledge the reviewer’s comment that single-cell transcriptomic analysis would indeed provide a more granular view of likely heterogeneity. This current study focuses on investigating the feasibility of directed differentiation of corticospinal-like neurons from endogenous progenitors. Future work employing single-cell sequencing could indeed help delineate the heterogeneity of neurons generated by directed differentiation, and potentially contribute toward identification of potential molecular roadblocks in different subsets.

Regarding the suggestion that SOX6-deficient NG2+ progenitors might activate a broader neurogenic program, we agree that this is an intriguing possibility. We are currently conducting indepth investigation of the loss of SOX6 function in NG2+ progenitors, and we aim to submit this quite distinct work for separate publication.

The reviewer raises an important point about whether SOX6+/NG2+ progenitors and subcerebral projection neurons are indeed normally lineage-related. In the current work, we utilized postnatal cortical SOX6+/NG2+ progenitors that are thought to be largely derived from EMX1+ and GSH2+ ventricular zone neural progenitors. Our unpublished data from the separate study noted above indicate that SOX6 is expressed by both these lineages in vivo. Since subcerebral projection neurons are derived from EMX1+ ventricular zone progenitors (SOX6-expressing), at least some of the SOX6+/NG2+ progenitors are expected to share a lineage relationship with subcerebral projection neurons. While our data strongly suggest such a link, we agree that direct lineagetracing could be pursued in future work. 

Finally, we agree with the reviewer’s suggestion that in vivo transplantation to assess the identity and connectivity of neurons generated by directed differentiation would be very interesting, and is a natural next phase of this work. We aim to pursue such work in future investigations.

We again thank the reviewer for their insightful comments.

Reviewer #1 (Recommendations For The Authors): 

The most important clarification for me concerns the initial description of the progenitors. I think there is a mistake with the transgenic line NG2. The dsRed mouse used in Figure 1 C is not described until later in the results describing Figure 2. This was confusing. Moreover, perhaps this is a reason why I get confused and do not understand how the authors conclude that SOX6+ cells are a subset of NG2positive cells. Panel C shows the opposite. Please correct the description and show the quantification of data in panel 1C.

We thank the reviewer for their thoughtful review and for highlighting this important point. We appreciate the reviewer pointing out the benefit of further clarity regarding the NG2.DsRed transgenic mouse description in Figure 1C. We have revised the text to clarify the use of the transgenic line and ensure that the DsRed mouse is properly introduced. Additionally, we have further clarified the description explaining the basis for concluding that SOX6+ cells are a subset of NG2+ cells and further integrate this conclusion with the data presented.

During cell sorting from the cortices of NG2.DsRed mice, we observe two distinct populations of NG2-DsRed+ cells based on fluorescence intensity in FACS: NG2-DsRed “bright” and NG2-DsRed “dim” populations. The NG2-DsRed “dim” population consists of a heterogenous mix of NESTIN+ progenitors, GFAP+ astrocytes/progenitors, a subset of NG2+ cells, and other unidentified cells. In contrast, the DsRed “bright” population includes a broader group of progenitors that also give rise to oligodendrocytes (please see Zhu, Bergles, and Nishiyama 2008), along with pericytes. 

Previous studies have shown that, while dorsal/pallial VZ progenitors express SOX6 during embryonic development, SOX6 expression becomes restricted to interneurons postnatally (these do not express NG2 proteoglycan; Azim et al., 2009) and to the broader group of NG2+ progenitors that also give rise to oligodendrocytes. The ICC image in Fig. 1C shows bright NG2+ cells in the cortex, many of which express SOX6. Thus, we conclude that SOX6+ cells constitute a subset of NG2-DsRed+ cells. 

In a similar line, the work is beautiful, but the manuscript can gain a lot from shortening and some more editing. for example:

(1) In the abstract, the word inappropriate should be removed. It seems to me that is an unnecessary subjective qualification - it is hardly possible that in biology we found repression of something inappropriate.

We have removed the word “inappropriate”.

(2) FACS-purify these genetically accessible....establish a pure culture. Genetically accessible is nice, and I understand that it conveys that they can be traced in the mouse, but everything is genetically accessible with the right tool, and perhaps it is more informative to explain which gene or report is used for the isolation. These cells are not accessible in humans. Also, I consider it best to remove pure- the culture is pure (purified by FACS) cells.

We have revised the text to specify the gene/reporter used for isolation instead of using "genetically accessible", and we removed "pure", since FACS purification is already explicitly mentioned.

(3) In the initial paragraph in the results: "They are exposed to the same morphogen gradients throughout embryonic development, and thus, compared to distant cell types, have similar epigenomic and transcription landscapes." This is proven in the cited publication, but the way is stated here seems a bit of an unnecessary overstatement. The hypothesis stated after this paragraph is as good as it is with or without this argument.

We have revised the text and simplified the statement. We agree that the hypothesis remains clear and well-supported without this emphasis.

(4) In the result sections, "two distinct populations of DsREd-positive cells were identified based on fluorescence intensity"- I know it is correct, but when reading the percentages, I was confused because those percentages divided the population into three fractions. What the authors do not explain is that they discard the intermediate-expressing population.

We appreciate the reviewer highlighting this inadvertent point of confusion. We erred by discussing only the two populations of central interest to us (DsRed-bright and DsRed-dim), and did not explicitly mention the DsRed-negative population. We have now clarified the text to include all three cell populations and their percentages of the total cells in all three populations (in the original manuscript and still now, ~75-78% were DsRed-negative). We have also further clarified that only DsRed-Bright cells (identified as progenitors) were used for all subsequent experiments.

These examples illustrate the type of editing that would be appreciated but which is entirely up to the authors.

We thank the reviewer for their thoughtful suggestions toward improving clarity and precision. We have incorporated these recommendations, along with suggestions from the other two reviewers, in the revised paper.

Reviewer #2 (Recommendations For The Authors):

(1)  The authors start their results section by showing in situ Hybridization for Ngn2 in control and Sox6KO mice. These control sections do not look convincing, as there is not even some signal in the adult VZSVZ region and virtually no background. Please show sections where some positive signal can also be detected in the control sections.

We agree with the reviewer that making direct comparisons in ISH experiments is an important point. In our ISH experiments, to ensure consistency and appropriate comparisons, we process WT and KO sections together and stop the signal development simultaneously. We could have extended the development time to enhance WT signal to a detectable level, but that would have led to excessive background and over-saturated signal in the KO sections.

To address the reviewer’s point, we have added a new supplementary figure with an additional pair of WT and KO sections, along with reference data from the Allen Brain Atlas. The WT section shows faint Neurog2 expression in the dentate gyrus region of the hippocampus, while the KO section confirms very substantial upregulation of Neurog2 in the absence of SOX6 function. These additional data enhance the clarity and depth of our results.

Please see the following link for the Allen Brain Atlas ISH data demonstrating that Neurog2 expression in the postnatal (P4) SVZ/SGZ is inherently low. (https://developingmouse.brainmap.org/experiment/show/100093831). 

(2) As a hallmark of projection neurons is where they send their axons, it would be important to include a biological assay for this. Of course, in vivo experiments would be great, but if this is not possible, the authors could co-culture sections from the late embryonic cortex, striatum, and spinal cord to see if the reprogrammed neurons preferentially extend their axons towards one of these targets (as normally developing neurons would, see e.g. Bolz et al., 1990).

We agree with the reviewer’s suggestion that a very interesting future stage of this work would be to investigate the projection neuron identity including connectivity in vivo. We aim to pursue follow-up studies to investigate in vivo integration and connectivity of such neurons generated by directed differentiation from endogenous SOX6+/NG2+ cortical progenitors. As the reviewer insightfully suggests, co-culturing different brain regions with these neurons could offer an alternative strategy to partially assess potential preferential connectivity into cultured spinal cord vs. alternate tissue. This area of investigation is of substantial interest to our lab, and we aim to pursue it in the coming years– it is a very large undertaking by either approach.

(3) However, if the loss of Sox6 is sufficient for Ngn2 to be upregulated, why did the authors not pursue this approach in their reprogramming experiments? Are these endogenous levels sufficient for reprogramming? Please add some OPC cultures from WT and KO mice to explore their conversion to neurons and possibly combine them with Olig2VP16 and Fezf2.

We thank the reviewer for this insightful comment and for raising this broader area of inquiry regarding whether SOX6 might be down-regulated to enhance induction of neurogenesis. We are writing a separate manuscript regarding function of SOX6 in these progenitors during normal or molecularly manipulated development. We investigate function of SOX6 using both whole body null mice and a series of conditional null mice. We aim to post that work as a preprint and submit it for review and publication in the coming months. Beyond that work, the potential strategy of downregulating SOX6 function while simultaneously upregulating other molecular controls to refine directed neuronal differentiation is also of substantial interest to us, and we aim to pursue this in follow-up work. Though these are both interesting questions/topics, we respectfully submit that these broad areas of parallel, complex, and future investigation would substantially expand the scope of work in this paper, so we aim to address them in separate studies.

(4) Please indicate independent biological replicates as individual data points in all histograms, i.e. also in Figure 2K, Figure 4I, S2H.

We have updated the figure legends indicating the biological replicates, and explained the broad media optimization that was used successfully in all further experiments.

(5) GFP labelling in Figures S2K-N is not convincing - too high background. Please optimize.

We have redesigned this figure and now present it as a new supplementary figure, with GFP pseudocolored in gray and enlarged subpanels for improved visualization of cell morphology.

Reviewer #3 (Recommendations For The Authors):

This is an extremely well-written manuscript with very exciting implications. Obviously, not all can be tested here. Some of the suggestions are relatively easy and may be worth testing right away, others may require more extensive study in the future. In my view, completing some of the points below could make this paper a landmark study.

I start with the key questions:

(1) Do grafted NVOF cells give rise to subcerebral projection neurons in vivo?

We agree with the reviewer’s suggestion that a very interesting future stage of this work would be to investigate the projection neuron identity including connectivity in vivo. As noted above in response to Reviewer 2, we aim to pursue follow-up studies to investigate in vivo integration and connectivity of such neurons generated by directed differentiation from endogenous SOX6+/NG2+ cortical progenitors. This question is of substantial interest to us, and we aim to pursue it in the coming years– as the reviewer notes, this is a very large undertaking, and beyond the scope of this paper.

(2) What is the fate of the Sox6 deficient NG2 glia that express Neurog2? One could isolate these cells and subject them to scRNA sequencing to see how far neurogenesis proceeds without addition of exogenous factors.

We thank the reviewer for this insightful question. As noted in our response to Reviewer 2, we are writing a separate manuscript regarding function of SOX6 in these progenitors during normal or molecularly manipulated development. We investigate function of SOX6 using both whole body null mice and a series of conditional null mice. We aim to post that work as a preprint and submit it for review and publication in the coming months, likely in early summer. We respectfully submit that this broad area of parallel, complex investigation would substantially expand the scope of work in this paper and make this paper too complex and multi-directional, so we aim to publish them as separate papers for the benefit of clarity for readers.

(3) Obviously, what happens to Sox6-deficient (or non-deficient cells) when forced to express NVOF? In this context, it might be fair to cite Felske et al (PLoS Biol, 2023) who report Neurog2 and Fezf2-induced reprogramming in the postnatal brain. In their model, these authors did not distinguish between converted astrocytes and NG2 glia. Thus, some of the reprogrammed cells may comprise the SOX6positive cells described here.

We thank the reviewer for highlighting for us that we inadvertently omitted referencing the important paper by Felske et al., 2023. We have now included this citation. 

We thank the reviewer for raising this broader area of inquiry regarding whether SOX6 might be down-regulated to enhance induction of neurogenesis. Beyond the work noted above regarding function of SOX6 in these progenitors during normal or molecularly manipulated development, the potential strategy of downregulating SOX6 function while simultaneously upregulating other molecular controls to refine directed neuronal differentiation is of substantial interest to us, and we aim to pursue this in follow-up work. We again respectfully submit that this area of complex, future investigation should be addressed in future studies.

Very interesting unaddressed questions include:

(1) Are Sox6+ NG glia of dorsal origin? This is implied but not shown. One could use Emx1Cre lines to assess this. Are Sox6+ glia and subcerebral projection neurons clonally related? This may be more challenging. In this context, it might be again fair to refer to Herrero-Navarro et al (Science Advances 2021) who show that glia lineage related to nearby neurons gives rise to induced neurons with regional specificity.

The reviewer raises an important question regarding the competence of SOX6+/NG2+ progenitors from distinct origins to generate corticospinal-like neurons by directed differentiation. In ongoing unpublished work, we have identified SOX6 expression by NG2+ progenitors of the three lineages derived from ventricular zone progenitors that express either Emx1, Gsh2, or Nkx2.1 transcription factors. The EMX1+ lineage-derived SOX6+/NG2+ progenitors are directly lineage related to cortical projection neurons. As the reviewer suggests, future experiments could explore potential differences in competence between these three populations.

We again thank the reviewer for highlighting for us that we also inadvertently omitted referencing the exciting study by Herrero-Navarro that addresses the question of regional heterogeneity within astrocytes and the differential reprogramming potential related to their origins. We have now cited this paper in the manuscript.

(2) Do other NG2 glia not give rise to subcerebral projection neurons when challenged with NVOF? Thus, how important is Sox6 expression really?

The question of the specific competence of dorsal/cortical SOX6+/NG2+ progenitors to differentiate into corticospinal-like neurons, and the strategy of downregulating SOX6 function while simultaneously upregulating other molecular controls to direct neuronal differentiation, are both of great interest to us. In pilot experiments, we observed reduced competence of ventrallyderived SOX6+/NG2+ progenitors to generate similar neurons. We plan to pursue the SOX6 manipulation in follow up work.

(3) Do Sox6+ NG2 glia proliferate like other NG2 glia and thereby represent a replenishable pool of progenitors?

Yes; as noted in the text shortly after Figure 1, and as presented in Figure S3l-L, these progenitors proliferate robustly in response to the mitogens PDGF-A and FGF2.

(4) How heterogenous are the NVOF-induced neurons? The bulk highlights the overall specificity, but does not tell whether all cells make it equally well.

We agree with the reviewer that this is an interesting question. ICC analysis (Fig. 4G-4H) presents the variation in the levels of a few functionally important proteins in the population of NVOFinduced neurons. This could be due to any or all of at least three potential possibilities: 1) potential diversity in the population of purified SOX6+/NG2+ progenitors; 2) technical variability in the amount of NVOF plasmid delivered to individual progenitors during transfection; and/or 3) natural stochastic TF-level variations generating closely-related neuron types, that also occurs during normal development. Future experiments could explore these questions.

eLife Assessment

The authors use a range of techniques to examine the role of Aurora Kinase A (AurA) in trained immunity. The study is hypothesis driven, it uses solid experimental approaches, and the data are presented in a logical manner. The findings are valuable to the trained immunity field because they provide an in-depth look at a common inducer of trained immunity, beta-glucan.

Reviewer #1 (Public review):

In this updated and improved manuscript, the authors investigate the role of Aurora Kinase A (AurA) in trained immunity, following a broader drug screening aimed at finding inhibitors of training. They show AurA is important for trained immunity by looking at the different aspects and layers of training using broad omics screening, followed up by a more detailed investigation of specific mechanisms. The authors finalised the investigation with an in vivo MC-38 cancer model where AurA inhibition reduces beta-glucan's antitumour effects.

Strengths:

The experimental methods are generally well-described. I appreciate the authors' broad approach to studying different key aspects of trained immunity (from comprehensive transcriptome/chromatin accessibility measurements to detailed mechanistic experiments). Approaching the hypothesis from many different angles inspires confidence in the results. Furthermore, the large drug-screening panel is a valuable tool as these drugs are readily available for translational drug-repurposing research.

In response to the rebuttal, I would like to compliment and thank the authors for the large amount of work they have done to improve this manuscript. They have removed most of my previous concerns and confusions, and explained some of their approaches in a way that I now agree with them - a great learning opportunity for me as well.

Weaknesses:

(1) The authors have adequately responded to my comments and updated the manuscript accordingly.

(2) The authors have removed most of my concerns. Regarding the use of unpaired tests because that is what is often done in the literature: I still don't agree with this, nor do I think that 'common practice' is a solid argument to justify the approach. However, we can agree to disagree, as I know indeed that many people argue over when paired tests are appropriate in these types of experiments. I appreciate that n=2 for sequencing experiments is justifiable in the way these analyses are used as exploratory screening methods with later experimental validation. I also want to thank the authors for reporting biological replicates where relevant and (I should have mentioned this in my original review also) I appreciate they validate some findings in a separate cell line - many papers neglect this important step.

(3) The authors have adequately responded to my comments and updated the manuscript accordingly.

(4) The authors have adequately responded to my comments and updated the manuscript accordingly.

(5) The authors have adequately responded to my comments and updated the manuscript accordingly.

(6) The authors have adequately responded to my comments and updated the manuscript accordingly. They have actually gone above and beyond.

(7) I would like to thank the authors for highlighting this information and taking away my confusion. The authors have adequately responded to my comments and updated the manuscript accordingly.

(8) The authors have adequately responded to my comments and updated the manuscript accordingly.

(9) I still think adding the 'alisertib alone' control would be of great added value, but I can see how it is unreasonable to ask the authors to redo those experiments.

(10) The authors have adequately responded to my comments and updated the manuscript accordingly.

(11) The authors have adequately responded to my comments and updated the manuscript accordingly.

(12) I thank the authors for their work to repeat this experiment with my suggestions included. I am convinced by this nice data. I would recommend that the authors put the data from New Figure 4 also in the manuscript as it adds value to the manuscript (unless I just missed it, I don't see it in Figure 6 or the supplement). Not every reader may look at the reviewer comments/rebuttal documents.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the inhibition of Aurora A and its impact on β-glucan-induced trained immunity via the FOXO3/GNMT pathway. The study demonstrates that inhibition of Aurora A leads to overconsumption of SAM, which subsequently impairs the epigenetic reprogramming of H3K4me3 and H3K36me3, effectively abolishing the training effect.

Strengths:

The authors identify the role of Aurora A through small molecule screening and validation using a variety of molecular and biochemical approaches. Overall, the findings are interesting and shed light on the previously underexplored role of Aurora A in the induction of β-glucan-driven epigenetic change.

Weaknesses:

Given the established role of histone methylations, such as H3K4me3, in trained immunity, it is not surprising that depletion of the methyl donor SAM impairs the training response. Nonetheless, this study provides solid evidence supporting the role of Aurora A in β-glucan-induced trained immunity in murine macrophages. The part of in vivo trained immunity antitumor effect is insufficient to support the final claim as using Alisertib could inhibits Aurora A other cell types other than myeloid cells.

Revision:

The authors have satisfactorily addressed the majority of my concerns. In particular, the new bone marrow transplantation data convincingly demonstrate that Aurora A inhibition with Alisertib abolishes the β-glucan-trained antitumor effect-an essential finding supporting the manuscript's conclusions.

Author response:

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

Reviewer#1 (Public review):

This work regards the role of Aurora Kinase A (AurA) in trained immunity. The authors claim that AurA is essential to the induction of trained immunity. The paper starts with a series of experiments showing the effects of suppressing AurA on beta-glucan-trained immunity. This is followed by an account of how AurA inhibition changes the epigenetic and metabolic reprogramming that are characteristic of trained immunity. The authors then zoom in on specific metabolic and epigenetic processes (regulation of S-adenosylmethionine metabolism & histone methylation). Finally, an inhibitor of AurA is used to reduce beta-glucan's anti-tumour effects in a subcutaneous MC-38 model.

Strengths:<br /> With the exception of my confusion around the methods used for relative gene expression measurements, the experimental methods are generally well-described. I appreciate the authors' broad approach to studying different key aspects of trained immunity (from comprehensive transcriptome/chromatin accessibility measurements to detailed mechanistic experiments). Approaching the hypothesis from many different angles inspires confidence in the results (although not completely - see weaknesses section). Furthermore, the large drug-screening panel is a valuable tool as these drugs are readily available for translational drug-repurposing research.

We thank the reviewer for the positive and encouraging comments.

Weaknesses:

(1) The manuscript contains factual inaccuracies such as:

(a) Intro: the claim that trained cells display a shift from OXPHOS to glycolysis based on the paper by Cheng et al. in 2014; this was later shown to be dependent on the dose of stimulation and actually both glycolysis and OXPHOS are generally upregulated in trained cells (pmid 32320649).

We appreciate the reviewer for pointing out this inaccuracy, and we have revised our statement to ensure accurate and updated description in manuscript. We are aware that trained immunity involves different metabolic pathways, including both glycolysis and oxidative phosphorylation [1, 2]. We also detected Oxygen Consumption Rate (please see response to comment 8 of reviewer#1) but observed no obvious increase of oxygen consumption in trained BMDMs in our experiment setting. As the reviewer pointed out, it might be dependent on the dose of stimulation.

(b) Discussion: Trained immunity was first described as such in 2011, not decades ago.

We are sorry for the inaccurate description, and we have corrected the statement in our revised manuscript as “Although the concept of ‘trained immunity’ has been proposed since 2011, the detailed mechanisms that regulate trained immunity are still not completely understood.”

(2) The authors approach their hypothesis from different angles, which inspires a degree of confidence in the results. However, the statistical methods and reporting are underwhelming.

(a) Graphs depict mean +/- SEM, whereas mean +/- SD is almost always more informative. (b) The use of 1-tailed tests is dubious in this scenario. Furthermore, in many experiments/figures the case could be made that the comparisons should be considered paired (the responses of cells from the same animal are inherently not independent due to their shared genetic background and, up until cell isolation, the same host factors like serum composition/microbiome/systemic inflammation etc). (c) It could be explained a little more clearly how multiple testing correction was done and why specific tests were chosen in each instance.

We sincerely thank the reviewer for this thoughtful comment. (a) The data from animal experiments in which trained immunity was induced in vivo are presented as mean ± SD, while the statistical results from cell-based experiments are presented as mean ± SEM in the revised manuscript. (b) We have replaced one-tailed test with two-tailed test (see Figure 3J in revised manuscript, with updated P value label). We agree that cells derived from the same animal and subjected to different treatment conditions may be deemed paired data. We reanalyzed our data using paired statistical tests. While this led to a slight reduction in statistical significance for some comparisons, the overall trends remained consistent, and our biological interpretation remains unchanged. For in vitro experiments unpaired statistical tests are commonly used in literature [3, 4]. Thus, we still used unpaired test results here. (c) We have provided a detailed description of how multiple comparisons were performed in revised figure legends.

(d) Most experiments are done with n = 3, some experiments are done with n = 5. This is not a lot. While I don't think power analyses should be required for simple in vitro experiments, I would be wary of drawing conclusions based on n = 3. It is also not indicated if the data points were acquired in independent experiments. ATAC-seq/RNA-seq was, judging by the figures, done on only 2 mice per group. No power calculations were done for the in vivo tumor model.

We are sorry for the confusion in our description in figure legends. For the in vivo experiment, we determined the sample size (n=5, n refers to number of mice used as biological replicates) by referring to the animal numbers used for similar experiments in literatures. And according to a reported resource equation approach for calculating sample size in animal studies [5], n=5-7 is suitable for most of our mouse experiments. The in vitro cell assay was performed at least three independent experiments (BMs isolated from different mice), and each experiment was independently replicated at least three times and points represents biological replicates in our revised manuscript. In Figure 1A, 5 biological replicates of these experiments are presented to carefully determine a working concentration of alisertib that would not significantly affect the viability of trained macrophages, and that was subsequently used in all related cell-based experiments. As for seq data, we acknowledge the reviewer's concern regarding the small sample size (n=2) in our RNA-seq/ATAC-seq experiment. We consider the sequencing experiment mainly as an exploratory/screening approach, and performed rigorous quality control and normalization of the sequencing data to ensure the reliability of our findings. For RNA-seq data analysis, we referred to the DESeq2 manual, which specifies that its statistical framework is based on the Negative Binomial Distribution and is capable of robustly inferring differential gene expression with a minimum of two replicates per group. Therefore, the inclusion of two replicates per group was deemed sufficient for our analysis. Nevertheless, the genomic and transcriptome sequencing data were used primarily for preliminary screening, where the candidates have been extensively validated through additional experiments. For example, we conducted ChIP followed by qPCR for detecting active histone modification enrichment in Il6 and Tnf region to further verify the increased accessibility of trained immunity-induced inflammatory genes.

(e) Furthermore, the data spread in many experiments (particularly BMDM experiments) is extremely small. I wonder if these are true biological replicates, meaning each point represents BMDMs from a different animal? (disclaimer: I work with human materials where the spread is of course always much larger than in animal experiments, so I might be misjudging this.).

Thanks for your comments. In our initially submitted manuscript, some of the statistical results were presented as the representative data (technical replicates) from one of three independent biological replicates (including BMDMs experiments showing the suppression and rescue experiments of trained immunity under different inhibitors or activators, see original Figure 1B-C, Figure 5D, and Figure 5H, also related to Figure 1B-C, Figure 5D, and Figure 5H respectively in our revised manuscript) while other experimental data are biological replicates including CCK8 experiment, metabolic assay and ChIP-qPCR. In response to your valuable suggestion, we have revised the manuscript to present all statistical results as biological replicates from three independent experiments (presented as mean ± SEM), and we have provided all the original data for the statistical analysis results (please see Appendix 2 in resubmit system).

(3) Maybe the authors are reserving this for a separate paper, but it would be fantastic if the authors would report the outcomes of the entire drug screening instead of only a selected few. The field would benefit from this as it would save needless repeat experiments. The list of drugs contains several known inhibitors of training (e.g. mTOR inhibitors) so there must have been more 'hits' than the reported 8 Aurora inhibitors.

Thank you for your suggestion and we have briefly reported the outcomes of the entire drug screening in the revised manuscript. The targets of our epigenetic drug library are primarily categorized into several major classes, including Aurora kinase family, histone methyltransferase and demethylase (HMTs and KDMs), acetyltransferase and deacetylase (HDACs and SIRTs), JAK-STAT kinase family, AKT/mTOR/HIF, PARP family, and BRD family (see New Figure 1, related to Figure 1-figure supplement 1B in revised manuscript). Notably, previous studies have reported that inhibition of mTOR-HIF1α signaling axis suppressed trained immunity[6]. Our screening results also indicated that most inhibitors targeting mTOR-HIF1α signaling exhibit an inhibitory effect on trained immunity. Additionally, cyproheptadine, a specific inhibitor for SETD7, which was required for trained immunity as previously reported [7], was also identified in our screening.

JAK-STAT signaling is closely linked to the interferon signaling pathway, and certain JAK kinase inhibitors also target SYK and TYK kinases. A previous drug library screening study has reported that SYK inhibitors suppressed trained immunity [8]. Consistently, our screening results reveal that most JAK kinase inhibitors exhibit suppressive effects on trained immunity.

BRD (Bromodomain) and Aurora are well-established kinase families in the field of oncology. Compared to BRD, the clinical applications of the Aurora kinase inhibitor are still at early stage. In previous studies using inflammatory arthritis models where trained immunity was established, both adaptive and innate immune cells exhibited upregulated expression of AurA [9, 10]. Our study provides further evidence supporting an essential role of AurA in trained immunity, showing that AurA inhibition leads to the suppression of trained immunity.

(4) Relating to the drug screen and subsequent experiments: it is unclear to me in supplementary figure 1B which concentrations belong to secondary screens #1/#2 - the methods mention 5 µM for the primary screen and "0.2 and 1 µM" for secondary screens, is it in this order or in order of descending concentration?

Thank you for your comments and we are sorry for unclear labelled results in original manuscript (related to Figure 1-supplement 1C). We performed secondary drug screen at two concentrations, and drug concentrations corresponding to secondary screen#1 and #2 are 0.2 and 1 μM respectively. It was just in this order, but not in an order of descending concentration.

(a) It is unclear if the drug screen was performed with technical replicates or not - the supplementary figure 1B suggests no replicates and quite a large spread (in some cases lower concentration works better?)

Thank you for your question. The drug screen was performed without technical replicates for initial screening purpose, and we need to verify any hit in the following experiment individually. Yes, we observed that lower concentration works better in some cases. We speculate that it might be due to the fact that the drug's effect correlates positively with its concentration only within a specific range. But in our primary screening, we simply choose one concentration for all the drugs. This is a limitation for our screening, and we acknowledge this limitation in our discussion part.

(5) The methods for (presumably) qPCR for measuring gene expression in Figure 1C are missing. Which reference gene was used and is this a suitably stable gene?

We are sorry for this omission. The mRNA expression of Il6 and Tnf in trained BMDMs was analyzed by a quantitative real-time PCR via a DDCt method, and the result was normalized to untrained BMDMs with Actb (β-actin) as a reference gene, a well-documented gene with stable expression in macrophages. We have supplemented the description for measuring gene expression in Material and Methods in our revised manuscript.

(6) From the complete unedited blot image of Figure 1D it appears that the p-Aurora and total Aurora are not from the same gel (discordant number of lanes and positioning). This could be alright if there are no/only slight technical errors, but I find it misleading as it is presented as if the actin (loading control to account for aforementioned technical errors!) counts for the entire figure.

We are very sorry for this omission. In the original data, p-Aurora and total Aurora were from different gels. In this experiment the membrane stripping/reprobing after p-Aurora antibody did not work well, so we couldn’t get all results from one gel, and we had to run another gel using the same samples to blot with anti-aurora antibody and used β-tubulin as loading control for total AurA (please see New Figure 2A, also related to original Figure 1D). We have provided the source data for β-tubulin from the same membrane of total AurA (please see Figure 1-source data). To avoid any potential misleading, we have repeated this experiment and updated this Figure (please see New Figure 2B, also related to Figure 1D in revised manuscript) with phospho-AurA, total AurA and β-actin from the same gel. The bands for phospho AurA (T288) were obtained using a new antibody (Invitrogen, 44-1210G) and we have revised this information in Material and Methods. We have provided data of three biological replicates to confirm the experiment result also see New Figure 2B, related to Figure 1D in revised manuscript, and the raw data have been added in source data for Figure 1)

(7) Figure 2: This figure highlights results that are by far not the strongest ones - I think the 'top hits' deserve some more glory. A small explanation on why the highlighted results were selected would have been fitting.

We appreciate the valuable suggestion. Figure 2 (see also Figure 2 in revised manuscript) presented information on the chromatin landscape affected by AurA inhibition to confirm that AurA inhibition impaired key gene activation involved in pro-inflammatory macrophage activation by β-glucan. In Figure 2B we highlighted a few classical GO terms downregulated including “regulation of growth”, “myeloid leukocyte activation” and “MAPK cascade” (see also Figure 2B in revised manuscript), among which “regulation of growth” is known function of Aurora A, just to show that alisertib indeed inhibited Aurora A function in vivo as expected. “Myeloid leukocyte activation” and “MAPK cascade” were to show the impaired pro-inflammatory gene accessibility. We highlighted KEGG terms downregulated like “JAK-STAT signaling pathway”, “TNF signaling pathway” and “NF-kappa B signaling pathway” in Figure 2F (see also Figure 2F in revised manuscript), as these pathways are highly relevant to trained immunity. Meanwhile, KEGG terms “FOXO signaling pathway” (see also Figure 2G in revised manuscript) was highlighted to confirm the anti-inflammation effect of alisertib in trained BMDMs, which was further illustrated in Figure 5 (see also Figure 5 in revised manuscript, illustrating FOXO3 acts downstream of AurA). Some top hits in Figure 2B like “positive regulation of cell adhesion”, and “pathway of neurodegeneration” and "ubiquitin mediated proteolysis" in Figure 2F and 2G, is not directly related to trained immunity, thus we did not highlight them, but may provide some potential information for future investigation on other functions of Aurora A.

(8) Figure 3 incl supplement: the carbon tracing experiments show more glucose-carbon going into TCA cycle (suggesting upregulated oxidative metabolism), but no mito stress test was performed on the seahorse.

We appreciate this question raised by the reviewer. We previously performed seahorse XF analyze to measure oxygen consumption rate (OCR) in β-glucan-trained BMDMs. The results showed no obvious increase in oxidative phosphorylation (OXPHOS) indicated by OCR under β-glucan stimulation (related to Figure 3-figure supplement 1 A) although the carbon tracing experiments showed more glucose-carbon going into TCA cycle. We speculate that the observed discrepancy between increased glucose incorporation into TCA cycle and unchanged OXPHOS may reflect a characteristic metabolic reprogramming induced by trained immunity. The increased incorporation of glucose-derived carbon into the TCA cycle likely serves a biosynthetic purpose—supplying intermediates for anabolic processes—rather than augmenting mitochondrial respiration[6]. Moreover, the unchanged OXPHOS may be attributed to a reduced reliance on fatty acid oxidation- “catabolism”, with glucose-derived acetyl-CoA becoming the predominant substrate. Thus, while overall OXPHOS remains stable, the glucose contribution to the TCA cycle increases. This is in line with reports showing that trained immunity promotes fatty acid synthesis- “anabolism”[11]. Alternatively, the partial decoupling of the TCA cycle from OXPHOS could result from the diversion of intermediates such as fumarate out of the cycle. Oxygen consumption rate (OCR) after a mito stress test upon sequential addition of oligomycin (Oligo, 1 μM), FCCP (1 mM), and Rotenone/antimycin (R/A, 0.5 μM), in BMDMs with different treatment for 24 h. β-glucan, 50 μg/mL; alisertib, 1 μM.

(9) Inconsistent use of an 'alisertib-alone' control in addition to 'medium', 'b-glucan', 'b-glucan + alisertib'. This control would be of great added value in many cases, in my opinion.

Thank you for your comment. We appreciate that including “alisertib-alone” group throughout all the experiments may further solidify the results. We set the aim of the current study to investigate the role of Aurora kinase A in trained immunity. Therefore, in most settings, we did not include the group of alisertib only without β-glucan stimulation.

(10) Figure 4A: looking at the unedited blot images, the blot for H3K36me3 appears in its original orientation, whereas other images appear horizontally mirrored. Please note, I don't think there is any malicious intent but this is quite sloppy and the authors should explain why/how this happened (are they different gels and the loading sequence was reversed?)

Thank you for pointing out this error. After checking the original data, we found that we indeed misassembled the orientation of several blots in original data submitted. We went through the assembling process and figured out that the orientation of blots in original data was assembled according to the loading sequences, but not saved correctly, so that the orientations in Figure 4A were not consistent with the unedited blot image. We are sorry for this careless mistake, and we have double checked to make sure all the blots are correctly assembled in the revised manuscript. We also provided three replicates of for the Western blot results showing the level of H3K36me3 in trained BMDMs was inhibited by alisertib (as seen in New Figure 7 at recommendation 2 of reviewer#2).

(11) For many figures, for example prominently figure 5, the text describes 'beta-glucan training' whereas the figures actually depict acute stimulation with beta-glucan. While this is partially a semantic issue (technically, the stimulation is 'the training-phase' of the experiment), this could confuse the reader.

Thanks for the reviewer’s suggestion and we have reorganized our language to ensure clarity and avoid any inconsistencies that might lead to misunderstanding.

(12) Figure 6: Cytokines, especially IL-6 and IL-1β, can be excreted by tumour cells and have pro-tumoral functions. This is not likely in the context of the other results in this case, but since there is flow cytometry data from the tumour material it would have been nice to see also intracellular cytokine staining to pinpoint the source of these cytokines.

Thanks for the reviewer’s suggestion. In Figure 6, we performed assay in mouse tumor model and found that trained immunity upregulated cytokines level like IL-6 in tumor tissue, which was downregulated by alisertib administration. In order to rule out the possibility that the detected cytokines such as IL-6 was from tumor cells, we performed intracellular cytokine staining of single cells isolated from tumor tissues (please see New Figure 4). The result showed that only a small fraction of non-immune cells (CD45^- population) expressed IL-6 (0.37% ± 0.11%), whereas a significantly higher proportion of IL-6-positive cells was observed among CD45⁺ population (deemed as immune cells, 13.66% ± 1.82%), myeloid cells (CD45⁺CD11b⁺, 15.60% ± 2.19%), and in particular, macrophages (CD45⁺CD11b⁺F4/80⁺37.24% ± 3.04%). These findings strongly suggest that immune cells, especially macrophages, are the predominant source of IL-6 cytokine within the tumor microenvironment. Moreover, we also detected higher IL-6 positive population in myeloid cells and macrophages (please see Figure 6I in revised manuscript).

Reviewer#2 (Public review):

Summary:

This manuscript investigates the inhibition of Aurora A and its impact on β-glucan-induced trained immunity via the FOXO3/GNMT pathway. The study demonstrates that inhibition of Aurora A leads to overconsumption of SAM, which subsequently impairs the epigenetic reprogramming of H3K4me3 and H3K36me3, effectively abolishing the training effect.

Strengths:

The authors identify the role of Aurora A through small molecule screening and validation using a variety of molecular and biochemical approaches. Overall, the findings are interesting and shed light on the previously underexplored role of Aurora A in the induction of β-glucan-driven epigenetic change.

We thank the reviewer for the positive and encouraging comments.

Weaknesses:

Given the established role of histone methylations, such as H3K4me3, in trained immunity, it is not surprising that depletion of the methyl donor SAM impairs the training response. Nonetheless, this study provides solid evidence supporting the role of Aurora A in β-glucan-induced trained immunity in murine macrophages. The part of in vivo trained immunity antitumor effect is insufficient to support the final claim as using Alisertib could inhibits Aurora A other cell types other than myeloid cells.

We appreciate the question raised by the reviewer. Though SAM generally acts as a methyl donor, whether the epigenetic reprogram in trained immunity is directly linked to SAM metabolism was not formally tested previously. In our study, we provided evidence suggesting the necessity of SAM maintenance in supporting trained immunity. As for in vivo tumor model, we agree that alisertib may inhibits Aurora A in many cell types besides myeloid cells. To further address the reviewer’s concern, we have performed the suggested bone marrow transplantation experiment (trained mice as donor and naïve mice as recipient) to verify the contribution of myeloid cell-mediated trained immunity for antitumor effect (please see New Figure 8, also related to Figure 6C, 6D and Figure 6-figure supplement 1B and 1C in revised manuscript).

Reviewer #1 (Recommendations for the authors):

Some examples of spelling errors and other mistakes (by far not a complete list):

(a) Introduction, second sentence: reads as if Candida albicans (which should be italicised and capitalised properly) and BCG are microbial polysaccharide components.

(b) Methods: ECAR is ExtraCellular Acidification Rate, not 'Extracellular Acid Ratio'

(c) Figure 2C: β-glucan is misspelled in the graph title.

(d) TNFα has been renamed to 'TNF' for a long time now.

(e) Inconsistent use of Tnf and Tfnα (the correct gene symbol is Tnf) (NB: this field does not allow me to italicise gene symbols)

(f) Figure supplement 1B: 'secdonary'

(g) Caption of figure 4: "Turkey's multiple-comparison test"

(h) etc

I would ask the authors that they please go over the entire manuscript very carefully to correct such errors.

We apologize for these errors and careless mistakes. We greatly appreciate your suggestions, and have carefully proofread the revised manuscript to make sure no further mistakes.

Please also address the points I raised in the public review about statistical approaches. Even more important than the relatively low 'n' is my question about biological replicates. Please clarify what you mean by 'biological replicate'.If you are able to repeat at least the in vitro experiments (if this is too much work pick the most important ones) a few more times this would really strengthen the results.

Thank you for your comment. Our biological replicates refer to independently repeated experiments using bone marrow cells isolated from different mice, and n represents the number of mice used. We repeated each experiment at least three times using BMDMs isolated from different mice (n =3, biological replicates). Specifically, we repeated several in vitro experiments showing inhibition of AurA upregulated GNMT in trained BMDMs and showing transcription factor FOXO3 acted as a key protein in AurA-mediated GNMT expression to control trained immunity as well as showing mTOR agonist rescued trained immunity inhibited by alisertib (see New Figure 5, related to Figure 5B-C, Figure 5H in revised manuscript). Additionally, we have provided data with three biological replicates to show the β-glucan induced phosphorylation of AurA (see comment 6 of reviewer#1) and changes of histone modification marker under AurA inhibition and GNMT deficiency (see recommendation 2 of reviewer#2). We also repeated in vivo tumor model to analysis intratumor cytokines (see recommendation 12 of reviewer#1).

Finally: the authors report 'no funders' during submission, but the manuscript contains funding details. Please modify this in the eLife submission system if possible.

Thank you for your kind reminder and we have modified funding information in the submission system.

Reviewer #2 (Recommendations for the authors):

(1) I have the following methodological and interpretative comments for consideration:

Aurora A has been previously implicated in M1 macrophage differentiation and NF-κB signaling. What is the effect of Aurora A inhibition on basal LPS stimulation? Considering that β-glucan + Ali also skews macrophage priming towards an M2 phenotype, as shown in Fig. 2E, further clarification on this point would strengthen the study.

Thanks for your suggestion. Previous study showed AurA was upregulated in LPS-stimulated macrophages and the inhibition of AurA downregulated M1 markers of LPS-stimulated macrophages through NF-κB pathway but did not affect IL-4-induced M2 macrophage polarization [12]. Consistently, we also found that AurA inhibition downregulated inflammatory response upon basal LPS stimulation as shown by decreased IL-6 level (see New Figure 6). In original Figure 2E (also related to Figure 2E in revised manuscript), we showed an increased accessibility of Mrc1 and Chil3 under “β-glucan +Ali” before re-challenge, both of which are typical M2 macrophage markers. Motif analysis showed that AurA inhibition would upregulate genes controlled by PPARγ (STAT6 was not predicted). Different from STAT6, a classical transcriptional factor in controlling M2 polarization (M2a) dependent on IL-4 or IL-13, PPARγ mediates M2 polarization toward M2c and mainly controls cellular metabolism on anti-inflammation independent on IL-4 or IL-13. Thus, we speculate that inhibition of AurA might promote non-classical M2 polarization, and the details warrant future investigation.

(2) In Figure 4A, it looks like that H3K27me3 is also significantly upregulated by β-glucan and inhibited by Ali. How many biological replicates were performed for these experiments? It would be beneficial to include densitometric analyses to visualize differences across multiple Western blot experiments for better reproducibility and quantitative assessment. In addition, what is the effect of treatment of Ali alone on the epigenetic profiling of macrophages?

We are sorry for this confusion. Each experiment was performed with at least three independent biological replicates. In original Figure 4-figure supplement 1 (also related to Figure 4-figure supplementary 1 in the revised manuscript), we presented the densitometric analysis results from three independent Western blot experiments, which showed that β-glucan did not affect H3K27me3 levels under our experimental conditions. Three biological replicates data for histone modification were shown as follows (New Figure 7, as related to Figure 4-figure supplement 1 in revised manuscript). We appreciate that assay for “Ali alone” in macrophages may add more value to the findings. We set the aim of the current study to investigate the role of Aurora kinase A in trained immunity, and we know that alisertib itself would not induce or suppress trained immunity. Therefore, in most settings, we did not test the effect of Alisertib alone without β-glucan stimulation.

(3) The IL-6 and TNF concentrations exhibit considerable variability (Fig. 3K and Fig. 5H), ranging from below 10 pg/mL to 500-1000 pg/mL. Please specify the number of replicates for these experiments and provide more detail on how variability was managed. Including this information would enhance the robustness of the conclusions.

Thank you for your comment. These experiments were replicated as least three times using BMDMs isolated from different mice. The observed variations in cytokines concentration may be attributed to factors such as differences in cell density, variability among individual mice, and the passage number of the MC38 cells used for supernatant collection. We have prepared new batch of BMDMs and repeated the experiment and provided consistent results in the revised manuscript (please see Figure 5H in revised manuscript). Data for biological replicates have been provided (please see Appendix 2 in resubmit system).

(4) The impact of Aurora A inhibition on β-glucan-induced anti-tumor responses appears complex. Specifically, GNMT expression is significantly upregulated in F4/80- cells, with stronger effects compared to F4/80+ cells as seen in Fig. 6D. To discern whether this is due to the abolishment of trained immunity in myeloid cells or an effect of Ali on tumor cells which inhibit tumor growth, I suggest performing bone marrow transplantation. Transplant naïve or trained donor BM into naïve recipients, followed by MC38 tumor transplantation, to clarify the mechanistic contribution of trained immunity versus off-target effects.

Thanks for your valuable suggestion. Following your suggestion, we have performed bone marrow transplantation to clarify that alisertib acts on the BM cells to inhibit anti-tumor effect induced by trained immunity (see New Figure 8, related to Figure 6C-D in revised manuscript). As the results shown below, transplantation of trained BM cells conferred antitumor activity in recipient mice, while transplantation of trained BM cells with alisertib treatment lost such activity, further demonstrating that alisertib inhibited AurA in trained BM cells to impair their antitumor activity.

References

(1) Ferreira, A.V., et al., Metabolic Regulation in the Induction of Trained Immunity. Semin Immunopathol, 2024. 46(3-4): p. 7.

(2) Keating, S.T., et al., Rewiring of glucose metabolism defines trained immunity induced by oxidized low-density lipoprotein. J Mol Med (Berl), 2020. 98(6): p. 819-831.

(3) Cui, L., et al., N(6)-methyladenosine modification-tuned lipid metabolism controls skin immune homeostasis via regulating neutrophil chemotaxis. Sci Adv, 2024. 10(40): p. eadp5332.

(4) Yu, W., et al., One-Carbon Metabolism Supports S-Adenosylmethionine and Histone Methylation to Drive Inflammatory Macrophages. Mol Cell, 2019. 75(6): p. 1147-1160 e5.

(5) Arifin, W.N. and W.M. Zahiruddin, Sample Size Calculation in Animal Studies Using Resource Equation Approach. Malays J Med Sci, 2017. 24(5): p. 101-105.

(6) Cheng, S.C., et al., mTOR- and HIF-1α-mediated aerobic glycolysis as metabolic basis for trained immunity. Science, 2014. 345(6204): p. 1250684.

(7) Keating, S.T., et al., The Set7 Lysine Methyltransferase Regulates Plasticity in Oxidative Phosphorylation Necessary for Trained Immunity Induced by β-Glucan. Cell Rep, 2020. 31(3): p. 107548.

(8) John, S.P., et al., Small-molecule screening identifies Syk kinase inhibition and rutaecarpine as modulators of macrophage training and SARS-CoV-2 infection. Cell Rep, 2022. 41(1): p. 111441.

(9) Glant, T.T., et al., Differentially expressed epigenome modifiers, including aurora kinases A and B, in immune cells in rheumatoid arthritis in humans and mouse models. Arthritis Rheum, 2013. 65(7): p. 1725-35.

(10) Jeljeli, M.M. and I.E. Adamopoulos, Innate immune memory in inflammatory arthritis. Nat Rev Rheumatol, 2023. 19(10): p. 627-639

(11) Ferreira, A.V., et al., Fatty acid desaturation and lipoxygenase pathways support trained immunity. Nat Commun, 2023. 14(1): p. 7385.

(12) Ding, L., et al., Aurora kinase a regulates m1 macrophage polarization and plays a role in experimental autoimmune encephalomyelitis. Inflammation, 2015. 38(2): p. 800-11.

eLife Assessment

This manuscript reports a large series of experiments to investigate specific aspects of plant adaptation, leveraging genetic and genomic resources of Arabidopsis thaliana. The study provides convincing evidence for local adaptation in this highly selfing plant. This is an important dataset contributing to the developing understanding of non-linear selection in plants and beyond.

Reviewer #1 (Public review):

Summary:

As a general phenomenon, adaptation of populations to their respective local conditions is well-documented, though not universally. In particular, local adaptation has been amply demonstrated in Arabidopsis thaliana, the focal species of this research, which is naturally highly selfing. Here, the authors report assays designed to evaluate the spatial scale of fitness variation among source populations and sites, as well as temporal variability in fitness expression. Further, they endeavor to identify traits and genomic regions that contribute to the demonstrated variation in fitness.

Strengths:

With many (200) inbred accessions drawn from throughout Sweden, the study offers an unusually fine sampling of genetic variation within this much-studied species, and through assays in multiple sites and years, it amply demonstrates the context-dependence of fitness expression. It supports the general phenomenon of local adaptation, with multiple nuances. Other examples exist, but it is of value to have further cases illustrating not only the context-dependence of fitness expression but also the sometimes idiosyncratic nature of fitness variation. I commend the authors on their cautionary language in relation to inferences about the roles of particular genomic regions (e.g.l.140-144; l.227)

Weaknesses:

To my mind, the manuscript is written primarily for the Arabidopsis community. This community is certainly large, but there are many evolutionary biologists who could appreciate this work but are not invited to do so. The authors could address the broader evolution community by acknowledging more of the relevant work of others (I've noted a few references in my comments to the authors). At least as important, the authors could make clearer the fact that A. thaliana is (almost) strictly selfing and how this feature of its biology both enables such a study and also limits inferences from it. Further, it seems to me that though I could be wrong, readers would appreciate a more direct, less discursive style of writing, and one that makes the broader import of the focal questions clearer.

As a reader, I would value seeing estimates of the overall fitness of the accessions in the different conditions, i.e., by combining the survival and fecundity results of the common garden experiments.

Reviewer #2 (Public review):

Summary:

The goal of this study was to find evidence for local adaptation in survival and fecundity of the model plant Arabidopsis thaliana. The authors grew a large set of Swedish Arabidopsis accessions at four common garden sites in northern and southern Sweden. Accessions were grown from seed in trays, which were laid on the ground at each site in late summer, screened for survival in fall and the following spring, and fecundity was determined from rosette size and seed production in spring. Experiments were complemented by 'selection experiments', in which seeds of the same accessions were sown in plots, and after two years of growth, plants were sampled to determine fitness from genotype frequencies, providing a more comprehensive evaluation of lifetime fitness than can be gleaned from fecundity alone.

As the main result, southern accessions had higher mortality in northern sites in one of two years, but also suffered more slug damage in southern sites in one year, indicating a potential link between frost tolerance and herbivore resistance. Fecundity of accession was highest when growing close to the 'home' environment, but while accessions from one sand dune population in southern Sweden had among the lowest fecundities overall, they consistently had the highest fitness in the selection experiment. Accessions from this population had large seed size and rapid root growth, which might be related to establishment success when arriving in a new, partially occupied habitat. However, neither trait could fully explain the very high fitness of this population, suggesting the presence of other, unmeasured traits.

Overall, the authors could provide clear evidence of local adaptation in different traits for some of their experiments, but they also highlight high temporal and spatial variability that makes prediction of microevolutionary change so challenging.

Strengths:

A major strength of this study is the highly comprehensive evaluation of different fitness-related traits of Arabidopsis under natural conditions. The evaluation of survival and fecundity in common garden experiments across four sites and two years provides an estimate of variability and consistency of results. The addition of the 'selection experiment' provides an extended view on plant fitness that is both original and interesting, in particular highlighting potential limitations of 'fitness-proxies' such as seed production that don't take into account seedling establishment and competitive exclusion.

Throughout the study, the authors have gone to impressive depths in exploring their data, and particularly the discovery of 'native volunteers' in selection experiment plots and their statistical treatment is very elegant and has resulted in compelling conclusions. Also, while the authors are careful in the interpretation of their GWAS results, they nonetheless highlight a few interesting gene candidates that may be underlying the observed plant adaptations, and which likely will stimulate further research.

Overall, the authors provide a rich new resource that is relevant and interesting both in the context of general evolutionary theory as well as more specifically for molecular biology.

Weaknesses:

While the repetition of the common garden experiments over two years is certainly better than no repetition (hence its mention also under 'strengths'), the very high variability found between the two years highlights the need for more extensive temporal replication. In this context, two temporal replicates are the bare minimum, and more repeats in time would be necessary to draw any kind of conclusion about the role of 'high mortality' and 'low mortality' years for the microevolution of Arabidopsis. It also seems that the authors missed an opportunity to explore potentially causal variation among years, as they did not attempt to relate winter mortality to actual climatic variables, even though they discuss winter harshness as a potential predictor.

The low temporal variation also makes the accidental slug herbivory appear somewhat random. Potted plants are notoriously susceptible to slug herbivory, and while it is certainly nice that slug damage predominantly affected one group of accessions, it nonetheless raises the question whether this reflects a 'real' selection pressure that plants commonly face in their respective local environments.

The addition of the 'selection experiment' is certainly original and provides valuable additional insights, but again, it seems a bit questionable which natural process really has affected this outcome. While the genetic and statistical analysis of this experiment seems to be state-of-the-art, the experimental design is rather rudimentary compared to more standard selection experiments. Specifically, the authors added seeds from greenhouse-grown mothers to experimental plots and only sampled plants two years later. This means that, potentially,y the first very big bottleneck was germination under natural conditions, which may have already excluded many of the accessions before they had a chance to grow. While this certainly is one type of selection, it is not exactly the type of selection that a 2-year selection experiment is set up to measure. Either initially establishing the selection experiment from plants instead of seeds, or genotyping the population over several generations, would have substantially strengthened the conclusions that could be drawn from this experiment. Also, the complete lack of information on population density is a bit problematic. It is not clear if there were other (non-Arabidopsis) plants present in the plots, how many Arabidopsis plants were established, if numbers changed over the year, etc. Given all of these limitations, calling this a 'selection experiment' is in fact somewhat misleading.

Despite these weaknesses, the authors could achieve their main goals, and despite the somewhat minimal temporal replication, they were lucky to sample two fairly distinct years that provided them with interesting variation, which they could partially explain using the variation among their accessions. Overall, this study will likely make an important contribution to the field of evolutionary biology, and it is another very strong example of how the extensive molecular tools in Arabidopsis can be leveraged to address fundamental questions in evolution and ecology, to an extent that is not (yet) possible in other plant systems.

Reviewer #3 (Public review):

Summary:

The manuscript presents a large common garden experiment across Sweden using solely local germplasm. Additionally, there is a collection of selection experiments that begin investigating the factors shaping fecundity in these populations. This provides an impressive amount of data and analysis investigating the underlying factors involved. Together, this helps support the data showing that fluctuations and interactions are key components determining Arabidopsis fitness and are more broadly applicable across plant and non-plant species.

Strengths:

The field trials are well conducted with extensive effort and sampling. Similarly while the genetic analysis is complex it is well conducted and reflects the complexity of dealing with population structure that may be intricately linked to adaptive structure. This has no real solution and the option of presenting results with and without correction is likely the only appropriate option.

Weaknesses:

A significant finding from this study was that fecundity is shaped more by yearly fluctuations and their interaction with genotype than it is by the main effect of location or genotype. Another significant finding is that the strength of selection can be quite strong, with nearly 5x ranges across accessions. It should be noted that there are a number of other studies using Arabidopsis in the wild with multiple years and locations that found similar observations beyond the Oakley citation. In general, the context of how these findings relate to existing knowledge in Arabidopsis is a bit underdeveloped.

The effects of the populations across the locations seem to rely on individual tests and PC analysis. It would seem to be possible to incorporate these tests more directly in the linear modeling analysis, and it isn't quite clear why this wasn't conducted.

I'm a bit puzzled by the discussion on how to find causative loci. This seems to focus solely on GWAS as the solution, with a goal to sequence vast individuals. But the loci that the manuscript discussed were found by a combination of structured mapping populations followed by molecular validation that then informed the GWAS. As such, I'm unsure if the proposed future approach of more sequencing is the best when a more balanced approach integrating diverse methods and population types will be more useful.

Author response:

Reviewer #1 (Public review):

Summary: 

As a general phenomenon, adaptation of populations to their respective local conditions is well-documented, though not universally. In particular, local adaptation has been amply demonstrated in Arabidopsis thaliana, the focal species of this research, which is naturally highly selfing. Here, the authors report assays designed to evaluate the spatial scale of fitness variation among source populations and sites, as well as temporal variability in fitness expression. Further, they endeavor to identify traits and genomic regions that contribute to the demonstrated variation in fitness.  

Strengths: 

With many (200) inbred accessions drawn from throughout Sweden, the study offers an unusually fine sampling of genetic variation within this much-studied species, and through assays in multiple sites and years, it amply demonstrates the context-dependence of fitness expression. It supports the general phenomenon of local adaptation, with multiple nuances. Other examples exist, but it is of value to have further cases illustrating not only the context-dependence of fitness expression but also the sometimes idiosyncratic nature of fitness variation. I commend the authors on their cautionary language in relation to inferences about the roles of particular genomic regions (e.g.l.140-144; l.227)  

Weaknesses: 

To my mind, the manuscript is written primarily for the Arabidopsis community. This community is certainly large, but there are many evolutionary biologists who could appreciate this work but are not invited to do so. The authors could address the broader evolution community by acknowledging more of the relevant work of others (I've noted a few references in my comments to the authors). At least as important, the authors could make clearer the fact that A. thaliana is (almost) strictly selfing and how this feature of its biology both enables such a study and also limits inferences from it. Further, it seems to me that though I could be wrong, readers would appreciate a more direct, less discursive style of writing, and one that makes the broader import of the focal questions clearer. 

we agree that connecting the paper better to the broader field is desirable, and will try to do this in the revision. As for how selfing matters, there certainly are some things we can discuss, but a general discussion is probably a suitable topic for a review/opinion article!

As a reader, I would value seeing estimates of the overall fitness of the accessions in the different conditions, i.e., by combining the survival and fecundity results of the common garden experiments.

Combining estimates would be possible in the common garden experiments, and would bring us somewhat closer to total fitness estimates, although as noted by another reviewer (and also emphasized by us), the time scale of our experiment is not sufficient to evaluate the trade-off between survival and fecundity. Furthermore, we would still be missing the establishment component of fitness, which we found to be extremely important. Therefore little would be gained by combining the estimates, while at the same time losing resolution to disentangle the fitness components. We thus decided to focus on the individual fitness components and leave consideration of their joint effect for the Discussion.

Reviewer #2 (Public review):

Summary: 

The goal of this study was to find evidence for local adaptation in survival and fecundity of the model plant Arabidopsis thaliana. The authors grew a large set of Swedish Arabidopsis accessions at four common garden sites in northern and southern Sweden. Accessions were grown from seed in trays, which were laid on the ground at each site in late summer, screened for survival in fall and the following spring, and fecundity was determined from rosette size and seed production in spring. Experiments were complemented by 'selection experiments', in which seeds of the same accessions were sown in plots, and after two years of growth, plants were sampled to determine fitness from genotype frequencies, providing a more comprehensive evaluation of lifetime fitness than can be gleaned from fecundity alone. 

To clarify, fecundity was determined from total plant area using photos of the mature stems, not the rosettes or direct counting of seeds. That said, it is true that our fecundity estimate was well correlated with rosette area. Furthermore, we validate our fecundity estimates by showing they were highly correlated with seed production estimated by measuring and counting siliques on a separate set of plants grown under common garden conditions in one of our sites (Brachi et al.2022). 

As the main result, southern accessions had higher mortality in northern sites in one of two years, but also suffered more slug damage in southern sites in one year, indicating a potential link between frost tolerance and herbivore resistance. Fecundity of accession was highest when growing close to the 'home' environment, but while accessions from one sand dune population in southern Sweden had among the lowest fecundities overall, they consistently had the highest fitness in the selection experiment. Accessions from this population had large seed size and rapid root growth, which might be related to establishment success when arriving in a new, partially occupied habitat. However, neither trait could fully explain the very high fitness of this population, suggesting the presence of other, unmeasured traits. 

Overall, the authors could provide clear evidence of local adaptation in different traits for some of their experiments, but they also highlight high temporal and spatial variability that makes prediction of microevolutionary change so challenging. 

Strengths: 

A major strength of this study is the highly comprehensive evaluation of different fitness-related traits of Arabidopsis under natural conditions. The evaluation of survival and fecundity in common garden experiments across four sites and two years provides an estimate of variability and consistency of results. The addition of the 'selection experiment' provides an extended view on plant fitness that is both original and interesting, in particular highlighting potential limitations of 'fitness-proxies' such as seed production that don't take into account seedling establishment and competitive exclusion. 

Throughout the study, the authors have gone to impressive depths in exploring their data, and particularly the discovery of 'native volunteers' in selection experiment plots and their statistical treatment is very elegant and has resulted in compelling conclusions. Also, while the authors are careful in the interpretation of their GWAS results, they nonetheless highlight a few interesting gene candidates that may be underlying the observed plant adaptations, and which likely will stimulate further research. 

Overall, the authors provide a rich new resource that is relevant and interesting both in the context of general evolutionary theory as well as more specifically for molecular biology. 

Weaknesses:

While the repetition of the common garden experiments over two years is certainly better than no repetition (hence its mention also under 'strengths'), the very high variability found between the two years highlights the need for more extensive temporal replication. In this context, two temporal replicates are the bare minimum, and more repeats in time would be necessary to draw any kind of conclusion about the role of 'high mortality' and 'low mortality' years for the microevolution of Arabidopsis. It also seems that the authors missed an opportunity to explore potentially causal variation among years, as they did not attempt to relate winter mortality to actual climatic variables, even though they discuss winter harshness as a potential predictor.

We agree that two years is insufficient to understand how variation in selective pressures compound over time to generate micro-evolutionary change. The eight-year data in Oakley et al. (2023), which we discuss in the paper, support this. Our results are nonetheless sufficient to demonstrate the idiosyncratic nature of selection. In the revision, we will further emphasize that far longer time series would be needed for definitive conclusions.

Our short time series is also why we do not try to correlate with climate data, as this would amount to doing statistics with four data points (mostly two groups of accession N vs S, with mostly homogenous climates within groups, and two years).

The low temporal variation also makes the accidental slug herbivory appear somewhat random. Potted plants are notoriously susceptible to slug herbivory, and while it is certainly nice that slug damage predominantly affected one group of accessions, it nonetheless raises the question whether this reflects a 'real' selection pressure that plants commonly face in their respective local environments. 

We agree with this point as well. The evidence for selection on glucosinolates by generalist herbivores such as slugs is fairly strong, but the precise agent is not known, and probably varies over time and space. Our results merely demonstrate one possibility (and we will clarify this in the revision).

The addition of the 'selection experiment' is certainly original and provides valuable additional insights, but again, it seems a bit questionable which natural process really has affected this outcome. While the genetic and statistical analysis of this experiment seems to be state-of-the-art, the experimental design is rather rudimentary compared to more standard selection experiments. Specifically, the authors added seeds from greenhouse-grown mothers to experimental plots and only sampled plants two years later. This means that, potentially,y the first very big bottleneck was germination under natural conditions, which may have already excluded many of the accessions before they had a chance to grow. While this certainly is one type of selection, it is not exactly the type of selection that a 2-year selection experiment is set up to measure. Either initially establishing the selection experiment from plants instead of seeds, or genotyping the population over several generations, would have substantially strengthened the conclusions that could be drawn from this experiment.

We agree that more data would have been beneficial, and we do not make strong claims about the nature of selection. Among other phenotypes, we mention dormancy, and note that existing dormancy estimates do not predict fitness in our selection experiments. In addition the same seed batches germinated uniformly in the common-garden experiments with minimal stratification (we will note this in the revision).

Also, the complete lack of information on population density is a bit problematic. It is not clear if there were other (non-Arabidopsis) plants present in the plots, how many Arabidopsis plants were established, if numbers changed over the year, etc. Given all of these limitations, calling this a 'selection experiment' is in fact somewhat misleading. 

Seeds were introduced into sites that appeared appropriate for A. thaliana, leaving the background community intact. We provided information on sowing density; the density of plants (A. thaliana and other species) that we obtained during the course of the experiments varied considerably between sites, much like in natural populations, although we lack systematic measurements. We will provide more information (including photos) in the revision.  

Despite these weaknesses, the authors could achieve their main goals, and despite the somewhat minimal temporal replication, they were lucky to sample two fairly distinct years that provided them with interesting variation, which they could partially explain using the variation among their accessions. Overall, this study will likely make an important contribution to the field of evolutionary biology, and it is another very strong example of how the extensive molecular tools in Arabidopsis can be leveraged to address fundamental questions in evolution and ecology, to an extent that is not (yet) possible in other plant systems. 

Reviewer #3 (Public review)

Summary: 

The manuscript presents a large common garden experiment across Sweden using solely local germplasm. Additionally, there is a collection of selection experiments that begin investigating the factors shaping fecundity in these populations. This provides an impressive amount of data and analysis investigating the underlying factors involved. Together, this helps support the data showing that fluctuations and interactions are key components determining Arabidopsis fitness and are more broadly applicable across plant and non-plant species. 

Strengths: 

The field trials are well conducted with extensive effort and sampling. Similarly while the genetic analysis is complex it is well conducted and reflects the complexity of dealing with population structure that may be intricately linked to adaptive structure. This has no real solution and the option of presenting results with and without correction is likely the only appropriate option. 

Weaknesses: 

A significant finding from this study was that fecundity is shaped more by yearly fluctuations and their interaction with genotype than it is by the main effect of location or genotype. Another significant finding is that the strength of selection can be quite strong, with nearly 5x ranges across accessions. It should be noted that there are a number of other studies using Arabidopsis in the wild with multiple years and locations that found similar observations beyond the Oakley citation. In general, the context of how these findings relate to existing knowledge in Arabidopsis is a bit underdeveloped. 

We shall remedy this in the revision (see also comments by Reviewer #1).

The effects of the populations across the locations seem to rely on individual tests and PC analysis. It would seem to be possible to incorporate these tests more directly in the linear modeling analysis, and it isn't quite clear why this wasn't conducted. 

The fecundity estimates were modelled for all experiments simultaneously and the results are presented in Figure 6 to explore the relative importance of genotype effects and interaction terms including genotypes. For survival and fecundity, the BLUPS are generated from linear mixed models fitted for all experiments simultaneously including a random intercept effect for the genotypes within experiments. A principal component analysis is used to explore the pattern of accession effects (BLUPS) on fecundity (Figure 7); this will be explained in the Methods.  

I'm a bit puzzled by the discussion on how to find causative loci. This seems to focus solely on GWAS as the solution, with a goal to sequence vast individuals. But the loci that the manuscript discussed were found by a combination of structured mapping populations followed by molecular validation that then informed the GWAS. As such, I'm unsure if the proposed future approach of more sequencing is the best when a more balanced approach integrating diverse methods and population types will be more useful. 

We are puzzled by this comment in return. Our statement about more sequencing (penultimate sentence of discussion) was referring to achieving a better understanding of the history of migration and selection rather than identifying causative loci. Happy for clarification!

References

Brachi, Benjamin, Daniele Filiault, Hannah Whitehurst, Paul Darme, Pierre Le Gars, Marine Le Mentec, Timothy C. Morton, et al. 2022. “Plant Genetic Effects on Microbial Hubs Impact Host Fitness in Repeated Field Trials.” Proceedings of the National Academy of Sciences of the United States of America 119 (30): e2201285119.

Oakley, Christopher G., Douglas W. Schemske, John K. McKay, and Jon Ågren. 2023. “Ecological Genetics of Local Adaptation in Arabidopsis: An 8-Year Field Experiment.” Molecular Ecology, June. https://doi.org/10.1111/mec.17045.

eLife Assessment

This valuable study provides a 3D standardised anatomical atlas of the brain of an orb-weaving spider. The authors describe the brain's shape and its inner compartments - the neuropils - and add information on the distribution of a number of neuroactive substances such as transmitters and neuropeptides. Through the use of histological and microscopy methods, the authors provide a more complete view of an arachnid brain than previous studies and also present convincing evidence about the organisation and homology of brain regions. The work will serve as a reference for future studies on spider brains and will enable comparisons of brain regions with insects so that the evolution of these structures can be inferred across arthropods.

Reviewer #1 (Public review):

Summary:

Artiushin et al. establish a comprehensive 3D atlas of the brain of the orb-web building spider Uloborus diversus. First, they use immunohistochemistry detection of synapsin to mark and reconstruct the neuropils of the brain of six specimens and they generate a standard brain by averaging these brains. Onto this standard 3D brain, they plot immunohistochemical stainings of major transmitters to detect cholinergic, serotonergic, octopaminergic/taryminergic and GABAergic neurons, respectively. Further, they add information on the expression of a number of neuropeptides (Proctolin, AllatostatinA, CCAP, and FMRFamide). Based on this data and 3D reconstructions, they extensively describe the morphology of the entire synganglion, the discernible neuropils, and their neurotransmitter/neuromodulator content.

Strengths:

While 3D reconstruction of spider brains and the detection of some neuroactive substances have been published before, this seems to be the most comprehensive analysis so far, both in terms of the number of substances tested and the ambition to analyze the entire synganglion. Interestingly, besides the previously described neuropils, they detect a novel brain structure, which they call the tonsillar neuropil.<br /> Immunohistochemistry, imaging, and 3D reconstruction are convincingly done, and the data are extensively visualized in figures, schemes, and very useful films, which allow the reader to work with the data. Due to its comprehensiveness, this dataset will be a valuable reference for researchers working on spider brains or on the evolution of arthropod brains.

Weaknesses:

As expected for such a descriptive groundwork, new insights or hypotheses are limited, apart from the first description of the tonsillar neuropil. A more comprehensive labeling in the panels of the mentioned structures would help to follow the descriptions. The reconstruction of the main tracts of the brain would be a very valuable complementary piece of data.

Reviewer #2 (Public review):

Summary

Artiushin et al. created the first three-dimensional atlas of a synganglion in the hackled orb-weaver spider, which is becoming a popular model for web-building behavior. Immunohistochemical analysis with an impressive array of antisera reveals subcompartments of neuroanatomical structures described in other spider species as well as two previously undescribed arachnid structures, the protocerebral bridge, hagstone, and paired tonsillar neuropils. The authors describe the spider's neuroanatomy in detail and discuss similarities and differences from other spider species. The final section of the discussion examines the homology between onychophoran and chelicerate arcuate bodies and mandibulate central bodies.

Strengths

The authors set out to create a detailed 3D atlas and accomplished this goal.

Exceptional tissue clearing and imaging of the nervous system reveal the three-dimensional relationships between neuropils and some connectivity that would not be apparent in sectioned brains.

A detailed anatomical description makes it easy to reference structures described between the text and figures.

The authors used a large palette of antisera which may be investigated in future studies for function in the spider nervous system and may be compared across species.

Weaknesses

It would be useful for non-specialists if the authors would introduce each neuropil with some orientation about its function or what kind of input/output it receives, if this is known for other species. Especially those structures that are not described in other arthropods, like the opisthosomal neuropil. Are there implications for neuroanatomical findings in this paper on the understanding of how web-building behaviors are mediated by the brain?

Likewise, where possible, it would be helpful to have some discussion of the implications of certain neurotransmitters/neuropeptides being enriched in different areas. For example, GABA would signal areas of inhibitory connections, such as inhibitory input to mushroom bodies, as described in other arthropods. In the discussion section on relationships between spider and insect midline neuropils, are there similarities in expression patterns between those described here and in insects?

Reviewer #3 (Public review):

Summary:

This is an impressive paper that offers a much-needed 3D standardized brain atlas for the hackled-orb weaving spider Uloborus diversus, an emerging organism of study in neuroethology. The authors used a detailed immunohistological whole-mount staining method that allowed them to localize a wide range of common neurotransmitters and neuropeptides and map them on a common brain atlas. Through this approach, they discovered groups of cells that may form parts of neuropils that had not previously been described, such as the 'tonsillar neuropil', which might be part of a larger insect-like central complex. Further, this work provides unique insights into the previously underappreciated complexity of higher-order neuropils in spiders, particularly the arcuate body, and hints at a potentially important role for the mushroom bodies in vibratory processing for web-building spiders.

Strengths:

To understand brain function, data from many experiments on brain structure must be compiled to serve as a reference and foundation for future work. As demonstrated by the overwhelming success in genetically tractable laboratory animals, 3D standardized brain atlases are invaluable tools - especially as increasing amounts of data are obtained at the gross morphological, synaptic, and genetic levels, and as functional data from electrophysiology and imaging are integrated. Among 'non-model' organisms, such approaches have included global silver staining and confocal microscopy, MRI, and, more recently, micro-computed tomography (X-ray) scans used to image multiple brains and average them into a composite reference. In this study, the authors used synapsin immunoreactivity to generate an averaged spider brain as a scaffold for mapping immunoreactivity to other neuromodulators. Using this framework, they describe many previously known spider brain structures and also identify some previously undescribed regions. They argue that the arcuate body - a midline neuropil thought to have diverged evolutionarily from the insect central complex - shows structural similarities that may support its role in path integration and navigation.

Having diverged from insects such as the fruit fly Drosophila melanogaster over 400 million years ago, spiders are an important group for study - particularly due to their elegant web-building behavior, which is thought to have contributed to their remarkable evolutionary success. How such exquisitely complex behavior is supported by a relatively small brain remains unclear. A rich tradition of spider neuroanatomy emerged in the previous century through the work of comparative zoologists, who used reduced silver and Golgi stains to reveal remarkable detail about gross neuroanatomy. Yet, these techniques cannot uncover the brain's neurochemical landscape, highlighting the need for more modern approaches-such as those employed in the present study.

A key insight from this study involves two prominent higher-order neuropils of the protocerebrum: the arcuate body and the mushroom bodies. The authors show that the arcuate body has a more complex structure and lamination than previously recognized, suggesting it is insect central complex-like and may support functions such as path integration and navigation, which are critical during web building. They also report strong synapsin immunoreactivity in the mushroom bodies and speculate that these structures contribute to vibratory processing during sensory feedback, particularly in the context of web building and prey localization. These findings align with prior work that noted the complex architecture of both neuropils in spiders and their resemblance (and in some cases greater complexity) compared to their insect counterparts. Additionally, the authors describe previously unrecognized neuropils, such as the 'tonsillar neuropil,' whose function remains unknown but may belong to a larger central complex. The diverse patterns of neuromodulator immunoreactivity further suggest that plasticity plays a substantial role in central circuits.

Weaknesses:

My major concern, however, is that some of the authors' neuroanatomical descriptions rely too heavily on inference rather than what is currently resolvable from their immunohistochemistry stains alone.

eLife Assessment

This manuscript presents an in-depth analysis of gene expression across multiple brown algal species with differing life histories, providing convincing evidence for the conservation of life cycle-specific gene expression. While largely descriptive, the study is an important step forward in understanding the core cellular processes that differ between life cycle phases, and its findings will be of broad interest to developmental and evolutionary biologists.

Reviewer #1 (Public review):

Summary:

The authors have examined gene expression between life cycle stages in a range of brown macroalgae to examine whether there are conserved aspects of biological features.

Strengths:

The manuscript incorporates large gene expression datasets from 10 different species and therefore enables a comprehensive assessment of the degree of conservation of different aspects of gene expression and underlying biology.

The findings represent an important step forward in our understanding of the core aspects of cell biology that differ between life cycle phases and provide a substantial resource for further detailed studies in this area. Convincing evidence is provided for the conservation of life-cycle-specific gene expression between species, particularly in core housekeeping gene modules.

Weaknesses:

I found a few weaknesses in the methodology and experimental design. I think the manuscript could have been clearer when linking the findings to the biology of the brown algae.

Reviewer #2 (Public review):

Summary:

The manuscript by Ratchinski et al presents a comprehensive analysis of developmental and life history gene expression patterns in brown algal species. The manuscript shows that the degree of generation bias or generation-specific gene expression correlates with the degree of dimorphism. It also reports conservation of life cycle features within generations and marked changes in gene expression patterns in Ectocarpus in the transition between gamete and early sporophyte. The manuscript also reports considerable conservation of gene expression modules between two representative species, particularly in genes associated with conserved functional characteristics.

Strengths:

The manuscript represents a considerable "tour de force" dataset and analytical effort. While the data presented is largely descriptive, it is likely to provide a very useful resource for studies of brown algal development and for comparative studies with other developmental and life cycle systems.

Weaknesses:

Notwithstanding the well-known issues associated with inferring function from transcriptomics-only studies, no major weaknesses were identified by this reviewer.

eLife Assessment

This study presents useful findings on how the transient absence of visual input (i.e., darkness) affects tactile neural encoding in the somatosensory cortex. The evidence supporting the authors' claims is incomplete, as key conclusions rely on subtle differences in surface roughness discriminability between sensory conditions, whose physiological underpinnings remain unclear. Potential methodological confounds are also not fully addressed. With additional analyses and methodological clarifications, this work could substantially inform neuroscientists studying cross-modal interactions.

Reviewer #1 (Public review):

Summary:

The authors aimed to investigate how short-term visual deprivation influences tactile processing in the primary somatosensory cortex (S1) of sighted rats. They justify the study based on previous studies that have shown that long-term blindness can enhance tactile perception, and aim to investigate the neural mechanisms underlying rapid, short-term cross-modal plasticity. The authors recorded local field potentials from S1 as rats encountered different tactile textures (smooth and rough sandpaper) under light and dark conditions. They used deep learning techniques to decode the neural signals and assess how tactile representations changed across the four different conditions. Their goal was to uncover whether the absence of visual cues leads to a rapid reorganization of tactile encoding in the brain.

Strengths:

The study effectively integrates high-density local field potential (LFP) recordings with convolutional neural network (CNN) analysis. This combination allows for decoding high-dimensional population-level signals, revealing changes in neural representations that traditional analyses (e.g., amplitude measures) failed to detect. The custom treadmill paradigm permits independent manipulation of visual and tactile inputs under stable locomotion conditions. Gait analysis confirms that motor behavior was consistent across conditions, strengthening the conclusion that neural changes are due to sensory input rather than movement artifacts.

Weaknesses:

(1) While the study interprets the emergence of more distinct texture representations in the dark as evidence of rapid cross-modal plasticity, the claim rests on correlational data from a short-term manipulation and decoding analysis. The authors show that CNN-derived feature embeddings cluster more clearly by texture in the dark, but this does not directly demonstrate plasticity in the classical sense (e.g., synaptic or circuit-level reorganization).

(2) Although gait was controlled, changes in arousal or exploratory behavior in light versus dark conditions might contribute to the observed neural differences. These factors are acknowledged but not directly measured (e.g., via pupillometry or cortical state indicators).

(3) Moreover, the time course of the observed changes (within 10 minutes) is quite rapid, and while intriguing, the study does not include direct evidence that the underlying circuits were reorganized - only that population-level signals become more discriminable. As such, the term "plasticity" may overstate the conclusions and should be interpreted with caution unless validated by additional causal or longitudinal data.

(4) The study highlights the forelimb region of S1 and a post-contact temporal window as particularly important for decoding texture, based on occlusion and integrated gradient analyses. However, this finding may be somewhat circular: The LFPs were aligned to forelimb contact, and the floor textures were sensed primarily via the forelimbs, making it unsurprising that forelimb electrodes were most informative. The observed temporal window corresponds directly to the event-aligned epoch, and while it may shift slightly in duration in the dark, this could reflect general differences in sensory gain or arousal, rather than changes in stimulus-specific encoding. Thus, while these findings are consistent with somatotopy and context-dependent dynamics, they do not provide strong independent evidence for novel spatial or temporal organization.

(5) While the neural data suggest enhanced tactile representations, the study does not assess whether rats' actual tactile perception improved. Without a behavioral readout (e.g., discrimination accuracy), claims about perceptual enhancement remain speculative.

(6) In addition to point 4, the authors discuss implications for sensory rehabilitation, including Braille training and haptic feedback enhancement. However, the lack of actual chronic or even more acute pathological sensory deprivation, behavioral data, or subsequent intervention in this study limits the ability to draw translational conclusions. It remains unknown whether the more distinct neural representations observed actually translate into better tactile performance, discriminability, or perception. Additionally, extrapolating from rats walking on sandpaper in the dark to human rehabilitative contexts is speculative without a clearer behavioral or mechanistic bridge. The potential is certainly there, but the claim is currently aspirational rather than empirically grounded.

(7) While the CNN showed good performance, details on generalization robustness and validation (e.g., cross-validation folds, variance across animals) are not deeply discussed. Also, while explainability tools were used, interpretability of CNNs remains limited, and more transparent models (e.g., linear classifiers or dimensionality reduction) could offer complementary insights.

Therefore, while the authors raise interesting hypotheses around rapid plasticity, somatotopic dynamics, and rehabilitation, the evidence for each is indirect. Stronger claims would require causal experiments, behavioral readouts, and mechanistic specificity beyond what the current data can provide.

Reviewer #2 (Public review):

Summary:

Yamashiro et al. investigated how the transient absence of visual input (i.e., darkness) impacts tactile neural encoding in the rat primary somatosensory cortex (S1). They recorded local field potentials (LFPs) using a 32-channel array implanted in forelimb and hindlimb primary somatosensory cortex while rats walked on smooth or rough textures under illuminated and dark conditions. Employing a convolutional neural network (CNN), they successfully decoded both texture and lighting conditions from the LFPs. The authors conclude that the subtle differences in LFP patterns underlie tactile representation of surface roughness and become more distinct in darkness, suggesting a rapid cross-modal reorganization of the neural code for this sensory feature.

Strengths:

(1) The manuscript addresses a valuable question regarding how sensory cortices adapt dynamically to changes in sensory context.

(2) Utilization of machine learning (CNNs) allowed the authors to go beyond conventional amplitude-based analyses, potentially uncovering a subtle but interesting phenomenon.

Weaknesses:

(1) Despite applying explainability techniques to the CNN-based decoder, the study does not clearly demonstrate the precise "subtle, high-dimensional patterns" exploited by the CNN for surface roughness decoding, limiting the physiological interpretability of the results. Additional analyses (e.g., detailed waveform morphology analysis on grand averages, time-frequency decompositions, or further use of explainability methods) are necessary to clarify the exact nature of the discriminative activity features enabling the CNN to decode surface roughness and how these change with the sensory context (i.e., in light or darkness).

(2) The claim regarding cross-modal representation reorganization heavily relies on a silhouette analysis (Figure 5C), which shows a modest effect size and borderline statistical significance (p≈0.05 with n=9+2). More rigorous statistical quantification, such as permutation tests and reporting underlying cluster distances for all animals, would strengthen confidence in this finding.

(3) While the authors recorded in the somatosensory cortex, primarily known for its tactile responsivity, I would be cautious not to rule out a priori the presence of crossmodal (visual) responses in the area. In this case, the stronger texture separation in darkness might be explained by the absence of some visually-evoked potentials (VEPs) rather than genuine cross-modal reorganization. Clarification is needed to rule out visual interference and this would strengthen the claim.

(4) Behavioural controls are limited to gross gait parameters; more detailed analyses of locomotor behavior and additional metrics (e.g., pupil size or locomotor variance) would robustly rule out potential arousal or motor confounds.

(5) The consistent ordering of trials (10 minutes of light then 10 minutes of dark) could introduce confounds such as fatigue or satiation (and also related arousal state), which should be controlled by analyzing sessions with reversed condition ordering.

(6) The focus on forelimb-aligned LFP analyses raises the possibility that hindlimb-aligned data might yield different conclusions, suggesting alignment effects might bias the results.

(7) The authors' dismissal of amplitude-based metrics as ineffective is inadequately substantiated. A clearer demonstration (e.g., event-related waveforms averaged by conditions, presented both spatially and temporally) would support this claim.

(8) Wording ambiguity regarding "attribution score" versus "activation amplitude" (Figure 5) complicates the interpretation of key findings. This distinction must be clarified for proper assessment of the results.

(9) Generalization across animals remains unaddressed. The current within-subject decoding setup limits conclusions regarding shared neural representations across individuals. Adopting cross-validation strategies and exploring between-animal analyses would add significant value to the manuscript.

eLife Assessment

This important study addresses how wing morphology and kinematics change across hoverflies of different body sizes. The authors provide convincing evidence that there is no significant correlation between body size and wing kinematics across 28 species and instead argue that non-trivial changes in wing size and shape evolved to support flight across the size range. Overall, this paper illustrates the power and beauty of an integrative approach to animal biomechanics and will be of broad interest to biologists, physicists and engineers.

Reviewer #2 (Public review):

Summary

Le Roy et al quantify wing morphology and wing kinematics across twenty eight and eight hoverfly species, respectively; the aim is to identify how weight support during hovering is ensured across body sizes. Wing shape and relative wing size vary non-trivially with body mass, but wing kinematics are reported to be size-invariant. On the basis of these results, it is concluded that weight support is achieved solely through size-specific variations in wing morphology, and that these changes enabled hoverflies to decrease in size. Adjusting wing morphology may be preferable compared to the alternative strategy of altering wing kinematics, because kinematics may be subject to stronger evolutionary and ecological constraints, dictated by the highly specialised flight and ecology of the hoverflies.

Strengths

The study deploys a vast array of challenging techniques, including flight experiments, morphometrics, phylogenetic analyses, and numerical simulations; it so illustrates both the power and beauty of an integrative approach to animal biomechanics. The question is well motivated, the methods appropriately designed, and the discussion elegantly places the results in broad biomechanical, ecological, and evolutionary context. In many ways, this work provides a blueprint for work in evolutionary biomechanics; the breadth of both the methods and the discussion reflects outstanding scholarship.

Weaknesses

The work presents a mechanical analysis that is focused solely on aerodynamics; but these aerodynamic demands impose no less relevant demands on the primary engine that drives wing movement: muscle. The relation between the assumed null hypotheses, the observed empirical allometric relations, and the power and work demand they place on muscle remains unclear. Though this is clearly a minor weakness, future work will have to address the link between aerodynamics, wing shape, wing dynamics, and musculoskeletal system in more detail, as discussed briefly by the authors.

Author response:

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

Reviewer #1 (Public review):

The paper is well written and the figures well laid out. The methods are easy to follow, and the rational and logic for each experiment easy to follow. The introduction sets the scene well, and the discussion is appropriate. The summary sentences throughout the text help the reader.

The authors have done a lot of work addressing my previous concerns and those of the other Reviewers.

We are pleased that the revised manuscript satisfactorily addresses the previous concerns of the reviewer.

Reviewer #2 (Public review):

Summary

Le Roy et al quantify wing morphology and wing kinematics across twenty eight and eight hoverfly species, respectively; the aim is to identify how weight support during hovering is ensured across body sizes. Wing shape and relative wing size vary non-trivially with body mass, but wing kinematics are reported to be size-invariant. On the basis of these results, it is concluded that weight support is achieved solely through size-specific variations in wing morphology, and that these changes enabled hoverflies to decrease in size. Adjusting wing morphology may be preferable compared to the alternative strategy of altering wing kinematics, because kinematics may be subject to stronger evolutionary and ecological constraints, dictated by the highly specialised flight and ecology of the hoverflies.

Strengths

The study deploys a vast array of challenging techniques, including flight experiments, morphometrics, phylogenetic analyses, and numerical simulations; it so illustrates both the power and beauty of an integrative approach to animal biomechanics. The question is well motivated, the methods appropriately designed, and the discussion elegantly places the results in broad biomechanical, ecological, and evolutionary context.

We thank the reviewer for appreciating the strengths of our study.

Weaknesses

(1) In assessing evolutionary allometry, it is key to pinpoint the variation expected from changes in size alone. The null hypothesis for wing morphology is well-defined (isometry), but the equivalent predictions for kinematic parameters, although specified, are insufficiently justified, and directly contradict classic scaling theory. A detailed justification of the "kinematic similarity" assumption, or a change in the null hypothesis, would substantially strengthen the paper, and clarify its evolutionary implications.

We agree with the reviewer that a clearly articulated null hypothesis is crucial for interpreting scaling relationships. In fact, when carefully reviewing our manuscript, we realized that we nowhere did so, and which might have led to a misinterpretation of this. In the revised manuscript, we therefore now explicitly state our newly defined null hypotheses (lines 120–125, 340-352), and how we tested these (lines 359-360).

In fact, we define two alternative null hypotheses: (1) weight support is maintained across sizes using allometric scaling of wing morphology only, and thus wingbeat kinematics are kept constant (kinematic similarity); (2) weight support is maintained across sizes using allometric scaling of wingbeat kinematics, while wing morphology scales isometrically (morphological similarity).

According to the first null hypothesis, the second-moment-of-area of the wing should scale linearly with body mass, resulting in negative allometry of S₂ relative to body mass (S₂∼m¹ <m^4/3). According to the second null hypothesis, the product of wingbeat frequency and amplitude should scale with mass under negative allometry (ω∼ƒ A_ϕ∼m^-1/6). We test these alternative null hypotheses using Phylogenetic Generalized Least Square (PGLS) regressions of the morphology and kinematics metrics against the body mass.

Furthermore, in our revised manuscript, we now also better explain the use of "kinematic similarity" assumption as a theoretical scenario, that is physically, biomechanically nor physiological sustainable across sizes, but that we merely use to define our null hypotheses (lines 340-351). This is made particularly explicit in a new subsection named “Theoretical considerations” (lines 448–461). Note that our second null hypothesis is thus not that hoverflies fly under "kinematic similarity", but that wingbeat kinematics scales under negative allometry (ω∼ƒ A_ϕ∼m^-1/6), which we assume is in line with the classic scaling theory that the reviewer refers to.

We sincerely thank the reviewer for making us aware that we did not explicitly state our null hypotheses, and that introducing these new null hypotheses removed the confusion about the assumptions in our study.

(2) By relating the aerodynamic output force to wing morphology and kinematics, it is concluded that smaller hoverflies will find it more challenging to support their body mass--a scaling argument that provides the framework for this work. This hypothesis appears to stand in direct contrast to classic scaling theory, where the gravitational force is thought to present a bigger challenge for larger animals, due to their disadvantageous surface-to-volume ratios. The same problem ought to occur in hoverflies, for wing kinematics must ultimately be the result of the energy injected by the flight engine: muscle. Much like in terrestrial animals, equivalent weight support in flying animals thus requires a positive allometry of muscle force output. In other words, if a large hoverfly is able to generate the wing kinematics that suffice to support body weight, an isometrically smaller hoverfly should be, too (but not vice versa). Clarifying the relation between the scaling of muscle mechanical input, wing kinematics, and weight support would help resolve the conflict between these two contrasting hypotheses, and considerably strengthen the biomechanical motivation and evolutionary interpretation.

We agree with the reviewer that, due to disadvantageous surface-to-volume ratios, larger animals are more challenged to maintain weight-support, and that this is also the case for hovering hoverflies. In the current manuscript, we do not aim to challenge this universal scaling law of muscle force with body mass.

Instead, we here focus merely on how the flight propulsion system (wing morphology and kinematics) scale with size, and how this allows hovering hoverflies to maintain weight support. We also fully agree with the reviewer that in theory, “if a large hoverfly is able to generate the wing kinematics that suffice to support body weight, an isometrically smaller hoverfly should be, too”. This aligns in fact with our second null hypothesis where wingbeat frequency should scale as ƒ∼m^-1/6, to maintain weight support under morphological isometry.

In our study, we show that this null hypothesis is rejected (lines 511-517, and line 525), and thus hoverflies primarily adjust their wing morphology to maintain in-hovering weight-support across sizes, and wingbeat kinematics is in fact highly conserved. Why this specific flight kinematics is so strongly conserved is not known, and thus a key topic in the discussion section of our manuscript.

We agree with the reviewer that muscle physiology might be an important driver for this conserved kinematics, but also aerodynamic efficiency and maneuverability could be key aspects here. In our revised manuscript, we now discuss these three aspects in more detail (lines 762-775). Also, we here now also mention that we aim to address this outstanding question in future studies, by including muscle physiology in our animal flight studies, and by studying the aerodynamics and maneuver kinematic of hoverflies in more detail. 

Moreover, in our revised introduction section, we now also mention explicitly that the capability for maintaining in-flight weight-support scales inversely with animal size, due to the negative isometric scaling of muscle force with body mass (line 52-56). Furthermore, we removed all statements that might suggest the opposite. We hope that these adjustments helped resolve the apparent conflict between our null hypotheses and general muscle scaling laws.

Finally, in the Discussion section (lines 770-775), we now more explicitly acknowledge that wing motion is ultimately driven by the flight motor musculature, and that a full biomechanical interpretation must consider the scaling of muscle mechanical input alongside wing kinematics and morphology. While we decided to keep the focus primarily on aerodynamic constraints in this study, we agree that future work integrating both aerodynamic and physiological scaling will be essential to fully resolve these contrasting perspectives.

(3) One main conclusion-- that miniaturization is enabled by changes in wing morphology--is insufficiently supported by the evidence. Is it miniaturization or "gigantism" that is enabled by (or drives) the non-trivial changes in wing morphology? To clarify this question, the isolated treatment of constraints on the musculoskeletal system vs the "flapping-wing based propulsion" system needs to be replaced by an integrated analysis: the propulsion of the wings, is, after all, due to muscle action. Revisiting the scaling predictions by assessing what the engine (muscle) can impart onto the system (wings) will clarify whether non-trivial adaptations in wing shape or kinematics are necessary for smaller or larger hovering insects (if at all!).

In many ways, this work provides a blueprint for work in evolutionary biomechanics; the breadth of both the methods and the discussion reflects outstanding scholarship.

In response to the first review round, we have removed all references to “miniaturization,” as our data does not allow us to infer evolutionary trajectories of body size (i.e., whether lineages have become smaller or larger over time). We now frame our conclusion more conservatively: that changes in wing morphology enable small hoverflies to maintain weight support despite the aerodynamic disadvantages imposed by isometric scaling.

We fully agree that an integrated biomechanical framework, explicitly linking muscle mechanical output with wing kinematics and morphology, would significantly strengthen the study. However, we believe that performing an integrated analysis assessing the scaling of muscle input into the wing is beyond the current scope, which focuses specifically on the aerodynamic consequences of morphological and kinematic variation (see reply above).

Reviewer #3 (Public review):

This paper addresses an important question about how changes in wing morphology vs. wing kinematics change with body size across an important group of high-performance insects, the hoverflies. The biomechanics and morphology convincingly support the conclusions that there is no significant correlation between wing kinematics and size across the eight specific species analyzed in depth and that instead wing morphology changes allometrically. The morphological analysis is enhanced with phylogenetically appropriate tests across a larger data set incorporating museum specimens.

The authors have made very extensive revisions that have significantly improved the manuscript and brought the strength of conclusions in line with the excellent data. Most significantly, they have expanded their morphological analysis to include museum specimens and removed the conclusions about evolutionary drivers of miniaturization. As a result, the conclusion about morphological changes scaling with body size rather than kinematic properties is strongly supported and very nicely presented with a strong complementary set of data. I only have minor textual edits for them to consider.

We thank the reviewer for this positive feedback. We are pleased to hear that the revised manuscript is satisfactory.

Reviewer #2 (Recommendations For The Authors):

My main remaining qualm remains the null hypothesis for the scaling of kinematic parameters - all weaknesses come back to this point. I appreciate that the authors now specify an expectation, but they offer no justification. This is a problem, because the expectation dictates the interpretation of the results and is thus crucial to some of the key claims (including one in the paper title!): the choice made by the authors indeed implies that hovering is harder for small hoverflies, so that the reported changes in size-specific wing morphology are to be interpreted as an adaptation that enables miniaturization. However, why is this choice appropriate over alternatives that would predict the exact opposite, namely that hovering is harder for larger hoverflies?

In my original review, I suggested that the authors may address this key question by considering the scaling of muscle mechanical output, and provided a quick sketch of what such an argument would look like, both in classic textbook scaling theory, and in the framework of more recent alternative approaches. The authors have decided against an implementation of this suggestion, providing various version of the following justification in their reply: "our study focuses precisely on this constraint on the wing-based propulsion system, and not on the muscular motor system." I am puzzled by this distinction, which also appears in the paper: muscle is the engine responsible for wing propulsion. How can one be assessed independent of the other? The fact that the two must be linked goes straight to the heart of the difficulty in determining the null hypotheses for the allometry of kinematic and dynamic parameters: they must come from assertions on how muscle mechanical output is expected to vary with size, and so couple muscle mechanical output to the geometry of the wing-based propulsion system. What if not muscle output dictates wing kinematics?

I fully agree with the authors that null hypotheses on kinematic parameters are debatable. But then the authors should debate their choice, and at least assess the plausibility of its implications (note that the idea of "similarity" in scaling does not translate to equal or invariant, but is tied closely to dimensional analysis - so one cannot just proclaim that kinematic similarity implies no change in kinematic parameters). I briefly return to the same line of argument I laid out in the initial review to provide such an assessment:

Conservation of energy implies:

W = 1/2 I ω2

where I is the mass moment of inertia and W is the muscle work output. Under isometry, I ∝m5/3, the authors posit ω ∝m0, and it follows at once that they predict W ∝m5/3. That is, the "kinematic similarity" hypothesis presented in the paper implies that larger animals can do substantially more work per unit body mass than small animals (unless the author have an argument why wing angular velocity is independent of muscle work capacity, and I cannot think of one). This increase in work output is in contradiction with the textbook prediction, going all the way back to Borelli and Hill: isogeometric and isophysiological animals ought to have a constant mass-specific work output. So why, according to the authors, is this an incorrect expectation, ie how do they justify the assumption ω ∝m0 and its implication W ∝m5/3? How can larger animals do more mass-specific work, or, equivalently, what stops smaller animals from delivering the same mass-specific work? If non-trivial adaptations such as larger relative muscle mass enable larger animals to do more work, how does this fit within the interpretation suggested by the authors that the aerodynamics of hovering require changes in small animals?

A justification of the kinematic similarity hypothesis, alongside answers to the above questions, is necessary, not only to establish a relation to classic scaling theory, but also because a key claim of the paper hinges on the assumed scaling relationship: that changes in wing morphology enable hovering in small hoverflies. If I were to believe Borelli, Hill and virtually all biomechanics textbooks, the opposite should be the case: combing constant mass-specific work output with eq. 1, one retrieves F∝m2/3, so that weight support presents a bigger challenge for larger animals; the allometry of wing morphology should then be seen as an adaptation that enables hovering in larger hoverflies - the exact opposite of the interpretation offered by the authors.

Now, as it so happens, I disagree with classic scaling theory on this point, and instead believe that there are good reasons to assume that muscle work output varies non-trivially with size. The authors can find a summary of the argument for this disagreement in the initial review, or in any of the following references:

Labonte, D. A theory of physiological similarity for muscle-driven motion. PNAS, 2023, 120, e2221217120

Labonte, D.; Bishop, P.; Dick, T. & Clemente, C. J. Dynamics similarity and the peculiar allometry of maximum running speed. Nat Comms., 2024, 15, 2181

Labonte, D. & Holt, N. Beyond power limits: the kinetic energy capacity of skeletal muscle. J Exp Bio, 2024, 227, jeb247150

Polet, D. & Labonte, D. Optimal gearing of musculoskeletal systems. Integr Org Biol, 2024, 64, 987-10062024

I am asking neither that the authors agree with the above references nor that they cite them. But I do expect that they critically discuss and justify their definition of kinematic similarity, its relation to expectation from classic scaling theory, and the implications for their claim that hovering is harder for small animals. I do note that the notion of "physiological similarity" introduced in the above references predicts a size-invariant angular velocity for small animals, that small animals should be able to do less mass-specific work, and that average muscle force output can grow with positive allometry even for isogeometric systems. These predictions appear to be consistent with the data presented by the authors.

We agree with the reviewer that our null hypothesis was not clearly articulated in our previous version of the manuscript, and that this might have led to a misinterpretation of the merits and limitations of our study. In the revised manuscript, we therefore now explicitly introduce our null hypotheses in the Introduction (lines 120–125), we define these in the Methods section (lines 340–360), test these in the Results section (lines 511–517), and reflect on the results in the Discussion (lines 602–610). We thank the reviewer for pointing out this unclarity in our manuscript, because revising it clarified the study significantly. See our replies in the “Public Review” section for details.

Minor points

L56: This is somewhat incomplete and simplistic; to just give one alternative option, weight support with equivalent muscle effort could also be ensured by a change in gearing (see eg Biewener's work). It is doubtful whether weight support is a strong selective force, as any animal that can move will be able to support its weight. The impact of scaling on dynamics is thus arguably more relevant.

We thank the reviewer for pointing out that our original sentence may be too simplistic. We now briefly mention alternative mechanisms (suggested by the reviewer) to provide more nuance (line 56-58).

L58: I am not aware of any evidence that smaller animals have reduced the musculature dedicated to locomotion beyond what is expected from isometry; please provide a reference for this claim or remove it.

We removed that claim.

The authors use both isometry and geometric similarity. As they also talk about muscle, solely geometric similarity (or isogeometry) may be preferable, to avoid confusion with isometric muscle contractions.

To avoid confusion, we now use “geometric similarity” wherever the use of isometry might be ambiguous.

L86: negative allometry only makes sense if there is a justified expectation for isometry - I suggest to change to "The assumed increase in wingbeat frequency in smaller animals" or similar, or to clarify the kinematic similarity hypothesis.

We edited the sentence as suggested.

L320: This assertion is somewhat misleading. Musculoskeletal systems are unlikely to be selected for static weight support. Instead, they need to allow movement. Where movement is possible, weight support is trivially possible, and so weight support should rarely, if ever, be a relevant constraint. At most, the negative consequence of isometry on weight support would be that a larger fraction of the muscle mass needs to be active in larger animals to support the weight.

We fully agree with the reviewer that musculoskeletal systems are unlikely not selected for static loads, as the ability to move dynamically in the real world is crucial for survival. That said, we here look at hovering flight, which is far from static. In fact, hovering flight is among the energetic most costly movement patterns found in nature, due to the required high-frequency wingbeat motions (Dudley 2002). Rapid maneuvers are of course more power demanding, but hovering is a good proxy for this. For example, in fruit flies maximum force production in rapid evasive maneuvers are only two times the force produced during hovering (Muijres et al., 2014).

We agree with the reviewer that it is important to explicitly mention the differences in functional demands on the motor system in hovering and maneuvering flight, and thus we now do so in both the introduction and discussion sections (lines 116-118 and 762-765, respectively).

Dudley, Robert. The biomechanics of insect flight: form, function, evolution. Princeton university press, 2002.Muijres, F. T., et al. "Flies evade looming targets by executing rapid visually directed banked turns." Science 344.6180 (2014): 172-177.

Reviewer #3 (Recommendations For The Authors):

Throughout, check use of "constrains" vs. "constraints"

Thank you for pointing this out. We have corrected these errors.

Line 52 do you mean lift instead of thrust?

We agree with the reviewer that the use of “thrust” might be confusing in the context of hovering flight, and thus we replaced “flapping-wing-based aerodynamic thrust-producing system” with the “flapping-wing-based propulsion system”. This way, we no longer use the word thrust in this context, and only use lift as the upward-directed force required for weight-support.

Line 60 "face also constrains" wording

Corrected.

Line 79 Viscous forces only "dominate" at Re<1 and so this statement only refers to very very small insects which I suspect are far below the scale of the hoverflies considered (likely Re ~100) although maybe not for the smallest 3 mg ones?

Indeed, viscous forces do not “dominate” force production at the Reynolds numbers of our flying insects. We thank the reviewer for pointing out this incorrect statement, which we corrected in the revised manuscript.

Line 85 again thrust doesn't seem to be right

Agreed. See reply 3.2.

533 "maximized" should probably be "increased"

We now use “increased”.

Line 705-710 The new study by Darveau might help resolve this a bit because of the reliability of this relationship across and between orders. Darveau, C.-A. (2024). Insect Flight Energetics And the Evolution of Size, Form, And Function. Integrative And Comparative Biology icae028.

We thank the reviewer for this highly relevant reference, which was unfortunately not included in the original manuscript. In connection with this work, we now further discuss the relationship between wing size allometry and deviations from the expected scaling of wingbeat frequency (lines 730-735).

eLife Assessment

This valuable observational study was conducted in Dar es Salaam, Tanzania, to investigate potential associations between genetic variation in Mycobacterium tuberculosis and human host vs. disease severity. The authors conclude that human genetic ancestry did not contribute to tuberculosis severity and the evidence supporting this is generally convincing. The findings have significance for the understanding of the influence of host/bacillary genetics on tuberculosis disease.

Reviewer #2 (Public review):

Summary:

This manuscript reports the results of an observational study conducted in Dar es Salaam, Tanzania, investigating potential associations between genetic variation in M. tuberculosis and human host vs. disease severity. The headline finding is that no such associations were found, either for host / bacillary genetics as main effects or for interactions between them.

Strengths:

Strengths of the study include its large size and rigorous approaches to classification of genetic diversity for host and bacillus.

Comments on revisions:

The authors have responded satisfactorily to comments raised.

Author response:

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

Reviewer #1 (Public review):

Summary:

This Tanzanian study focused on the relationship between human genetic ancestry, Mycobacterium tuberculosis complex (MTBC) diversity, and tuberculosis (TB) disease severity. The authors analyzed the genetic ancestry of 1,444 TB patients and genotyped the corresponding MTBC strains isolated from the same individuals. They found that the study participants predominantly possess Bantu-speaking genetic ancestry, with minimal European and Asian ancestry. The MTBC strains identified were diverse and largely resulted from introductions from South or Central Asia. Unfortunately, no associations were identified between human genetic ancestry, the MTBC strains, or TB severity. The authors suggest that social and environmental factors are more likely to contribute to TB severity in this setting.

Strengths:

In comparison to other studies investigating the role of human genetics in TB phenotypes, this study is relatively large, with more than 1,400 participants.

The matched human-MTBC strain collection is valuable and offers the opportunity to address questions about human-bacterium co-evolution.

Weaknesses:

Although the authors had genome-wide genotyping and whole genome sequencing data, they only compared the associations between human ancestry and MTBC strains. Given the large sample size, they had the opportunity to conduct a genome-wide association study similar to that of Muller et al. (https://doi.org/10.1016/j.ygeno.2021.04.024).

Thank you very much for taking the time to carefully review our manuscript and for your suggestions and comments. In another published study using the same cohort (https://doi.org/10.1101/2023.05.11.23289848), we performed a genome-wide association analysis between the genome-wide SNPS of the host and the genome-wide SNPs from the paired MTBC strains. In the current work we were interested in testing specifically if host ancestry and pathogen genotype family, as well as their interaction, were associated with differences in disease severity, a clinical phenotype with direct consequences for both host and pathogen fitness. The study of Müller et al, referred to by the reviewer, investigates whether MTBC families of strains causing disease in two patient cohorts (South Africa and Ghana) were associated with particular human SNPS assessed genome-wide. In that study, clinical phenotypes were not assessed and human ancestries, in a much broader sense than the ones used in our current study, were used as covariates. To leverage the genome-wide information and the clinical variables collected in our study, we have now added a genome-wide association analysis of all the human SNPs with disease severity measures while adjusting for co-variates (age, sex,  smoking, cough duration, socioeconomic status, history of previous TB, malnutrition, education level, and drug resistance status) and for human population stratification . Yet, no significant statistical associations were detected (L243-249).

The authors tested whether human genetic ancestry is associated with TB severity. However, the basis for this hypothesis is unclear. The studies cited as examples all focused on progression to active TB (from a latent infection state), which should not be conflated with disease severity. It is difficult to ascertain whether the role of genetic ancestry in disease severity would be detectable through this study design, as some participants might simply have been sicker for longer before being diagnosed (despite the inquiry about cough duration). This delay in diagnosis would not be influenced solely by human genetics, which is the conclusion of the study.

Evidence that mortality and natural recovery from TB vary by disease presentation spectrum come from studies carried out before the introduction of anti-TB chemotherapy. Patients with mild disease presentation, as measured by radiology at the time of diagnosis had higher odds of recovering naturally compared to those with advanced disease (doi: 10.5588/ijtld.23.0254, doi: 10.1164/arrd.1960.81.6.839). Given the deleterious effects of an MTBC infection leading to symptomatic disease on human fitness, we hypothesized that natural selection has acted on human traits underlying TB disease severity. If those traits are heritable one would expect to find underlying genetic variation in human populations. In addition, because certain MTBC genotype families and human populations have co-existed since a least a few centuries to a few millennia, we hypothesized that some of that genetic variation could be related to human ancestry. We have added more details to the introduction to make our rational clearer (L118-127).  In our patient cohort, we observed a large variation in disease severity using as approximations; TB-Score, X-Ray score and bacterial burden in sputa (Ct-value as determined with GeneXpert). However, the reviewer is absolutely correct in that patients in our study are being diagnosed at different stages of disease confounding our analysis. This is a limitation of our study which cannot be fully accounted for by including cough duration, as we also acknowledged in the manuscript (L343-346).

Additionally, the study only included participants who attended the TB clinic.

Yes, this is related to the previous point, our study only considers patients that felt ill enough to visit the TB clinic potentially not including patients that had less severe disease as acknowledged.

Including healthy controls from the general population would have provided an interesting comparison to see if ancestry proportions differ.

We agree that it would be interesting to compare the ancestries of healthy controls to the ancestries of TB patients from the same population. However, that would be especially informative with respect to TB susceptibility and would not necessarily be informing disease severity traits and its underlying genetics. The similarities between the ancestry proportions of our cohort with those of neighboring countries such as Kenya, Malawi and Mozambique publicly available genomic data, suggests that there would be no major differences between TB patients and healthy controls.

Although the authors suggest that social and environmental factors contribute to TB severity, only age, smoking, and HIV status were characterised in the study.

Based on the comments of both reviewers, we added the following additional variables as covariates in the regression models: the socioeconomic status representing the ratio between the household income and the number of individuals in the household, malnutrition, the education level and whether it was a relapse/reinfection or a new case.

Reviewer #2 (Public review):

Summary:

This manuscript reports the results of an observational study conducted in Dar es Salaam, Tanzania, investigating potential associations between genetic variation in M. tuberculosis and human host vs. disease severity. The headline finding is that no such associations were found, either for host / bacillary genetics as main effects or for interactions between them.

Strengths:

Strengths of the study include its large size and rigorous approaches to classification of genetic diversity for host and bacillus.

Weaknesses:

(1) There are some limitations of the disease severity read-outs employed: X-ray scores and Xpert cycle thresholds from sputum analysis can only take account of pulmonary disease. CXR is an insensitive approach to assessing 'lung damage', especially when converted to a binary measure. What was the basis for selection of Ralph score of 71 to dichotomise patients? If outcome measures were analysed as continuous variables, would this have been more sensitive in capturing associations of interest?

Thank you very much for taking the time to carefully review our manuscript and for your suggestions and comments.  

We recruited active TB patients with pulmonary TB disease that were sputum smear-positive and GeneXpert-positive. In this study we aimed at obtaining paired samples from both the patient and the strain, and in the current analysis we aimed at testing if human ancestry and its interaction with the strain genotype could explain differences in disease severity. It is often difficult to obtain microbiological cultures from extra-pulmonary cases and including those cases would have not been possible at the scale of this cohort. We believe as well that extra-pulmonary TB is of less relevance for the question we are addressing because in exclusively extrapulmonary cases, disease severity is not linked with bacterial transmission. However, extra-pulmonary TB can be extremely severe, and it would be very interesting to explore the potential role of human genetic variation underlying extra-pulmonary TB in future studies.

As to the insensitivity of CXR to measure lung damage, we would argue that it depends on what is being assed. As a rationale for the Ralph score, its inventors argue that as in other grading methods, the proportion of affected lung and or cavitation is important to assess severity. It has been described as a “validated method for grading CXR severity in adults with smear-positive pulmonary TB that correlates with baseline clinical and microbiological severity and response to treatment, and is suitable for use in clinical trials” (https://thorax.bmj.com/content/thoraxjnl/65/10/863.full.pdf). While the validation of the score is convincing in that study, and the score has been used in several TB studies and trials, the low proportion of HIV co-infections might have been a limitation. Indeed, as shown in our previous publication, in our cohort of patients, chest X-ray scores were significantly lower in HIV infected TB patients https://doi.org/10.1371/journal.ppat.1010893. In the current analysis, regression analyses performed for the CXR severity and for the other severity measures did not include HIV co-infected patients.

We obtained the same pattern of results using a continuous outcome. However, an assumption of linear regression was violated. The residuals were not normally distributed stemming from the bimodal distribution of the scores in our dataset. The threshold of 71 for the Ralph score has been used by others in previous studies; in its original description it has been suggested as the optimal cut-off point for predicting a positive sputum smear status after two months, which in turn has been shown to predict unfavorable outcomes (https://doi.org/10.1136/thx.2010.136242). Another study showed that a Ralph score higher than 71 was significantly associated with a longer duration of symptoms, higher clinical scores and a lower BMI (doi: 10.5603/ARM.2018.0032).

(2) There is quite a lot of missing data, especially for TB scores - could this have introduced bias? This issue should be mentioned in the discussion.

While we have a TB-score available for each patient, the chest X-ray score is missing for many patients. However, this is random and due both to the absence of an X-ray picture or to the bad quality of X-ray pictures that the radiologists could not assess. When stating that there is a lot of missing data for the TB scores, we assume that the reviewer was referring to the “missing N” columns in Table 1. There, the number of observations missing in each of the disease severity measures actually relates to the explanatory variables (i.e MTBC genotype and human ancestries). This table includes all patients that either had a bacterial genome available or a human genome/genotype (N = 1904). As an example for the TB-score as outcome variable, for 1471 patients the MTBC genotype was determined while it was missing for 433 patients. On the other hand for X-ray scores, 177 had a severe X-ray score, 849 a mild one and for 878 patients, there was no X-ray score available.  As for the Ct-value, despite the fact that the patients were recruited based on positive GeneXpert by the clinical team, these results were not always available to us.

(3) The analysis adjusted for age, sex, HIV status, age, smoking and cough duration - but not for socio-economic status. This will likely be a major determinant of disease severity. Was adjustment made for previous TB (i.e. new vs repeat episode) and drug-sensitivity of the isolate? Cough duration will effectively be a correlate/consequence of more severe disease - thus likely highly collinear with disease severity read-outs - not a true confounder. How does removal of this variable from the model affect results? Data on socioeconomic status should be added to models, or if not possible then lack of such data should be noted as a limitation.

Out of the 1904 patients that have either human or bacterial genomic data available, 48 were relapses (2.5%). The mean of the disease severity measures suggest that relapses have a higher CXR score but the TB-score and Ct-values did not differ. Based on the comments of both reviewers, we added the following additional variables as covariates to the regression models: the socioeconomic status representing the ratio between the household income and the number of individuals in the household, malnutrition examined by a doctor, the education level, and whether it was a relapse/reinfection or a new case and if the causative strain had any resistance to any anti-TB drugs. The results did not change. Cough duration could also be a consequence of more severe disease, as pointed out by the reviewer. We present now the results excluding cough duration as a variable from the model, however this also did not affect the results.

(4) Recruitment at hospitals may have led to selection bias due to exclusion of less severe, community cases. The authors already acknowledge this limitation in the Discussion however.

(5) Introduction: References refer to disease susceptibility, but the authors should also consider the influences of host/pathogen genetics on host response - both in vitro (PMIDs 11237411, 15322056) and in vivo (PMID 23853590). The last of these studies encompassed a broader range of ethnic variation than the current study, and showed associations between host ancestry and immune response - null results from the current study may reflect the relative genetic homogeneity of the population studied.

We thank the reviewer for these suggestions which we have added to the introduction. 

Reviewer #1 (Recommendations for the authors):

Minor Comments:

(1) The authors should be careful when using the term "Bantu" as opposed to "Bantu-speaking". (i.e. referring to the language group). The term is considered offensive in some settings.

We thanks the reviewer for this important concern, we have revised throughout the manuscript.

(2) There are several "(Error! Reference source not found)" phrases in the place of references throughout the document.

We thank the reviewer for pointing this out, this has been corrected in the revised version.

(3) Please correct line 365: "... sequencing (WGS) the patient...." to "... sequencing (WGS) of the patient...."

(4) The figures in the supplementary PDF are not numbered and some are cut-off (I think it is Supplementary Figure S2).

This has been corrected in the revised version.

Reviewer #2 (Recommendations for the authors):

Typographical errors

(1) There are multiple instances where references have not pulled through to the text, e.g. line 126 (Error! Reference source not found.)

We thank the reviewer for pointing this out, this has been corrected in the revised version.

(2) Line 239: have been show - have been shown?

Thank you, this mistake has been corrected in the revised version.

eLife Assessment

This important study shows that the activity of hypothalamic hypocretin/orexin neurons (HONs) correlates with body movement over multiple behaviors. Compelling evidence, supported by sophisticated, cutting-edge tools and data analyses, highlights a link that appears to be unique to HONs. This work should be of interest to scientists studying peptidergic neurons, movement, energy regulation, and brain-body coordination.

Reviewer #1 (Public review):

Summary:

This manuscript by Tesmer and colleagues uses fiber photometry recordings, sophisticated analysis of movement, and deep learning algorithms to provide compelling evidence that activity in hypothalamic hypocretin/orexin neurons (HONs) correlates with net body movement over multiple behaviors. By examining projection targets, the authors show that hypocretin/orexin release differs in projection targets to the locus coeruleus and substantia nigra, pars compacta. Ablation of HONs does not cause differences in the power spectra of movements. Movement tracking ability of HONs is independent of HON activity that correlates with blood glucose levels. Finally, the authors show that body movement is not encoded to the same extent in other neural populations.

Strengths:

The major strengths of the study are the combination of fiber photometry recordings, analysis of movement in head-fixed mice, and sophisticated classification of movement using deep learning algorithms. The experiments seem to be well performed, and the data are well presented, visually. The data support the main conclusions of the manuscript.

Weaknesses:

To some degree, it is already known that hypocretin/orexin neurons correlate with movement and arousal, although this manuscript studies this correlation with unprecedented sophistication and scale.

Taken together, this study is likely to be impactful to the field and our understanding of HONs across behavioral states.

Reviewer #4 (Public review):

Summary:

Using head-fixed approach, the authors show a rapid impact of movement on the activity level of hypothalamic orexin/hypocretin neurons.

Strengths:

The head-fixed approach is great to isolate specific movements and their impact on neuronal activity.

Weaknesses:

Many of the weaknesses that were noted in the previous round of review have been addressed.

Reviewer #5 (Public review):

Summary:

Hypothalamic hypocretin/orexin neurons are well-known to be involved in arousal, muscle tone and energy metabolism. Using a combination of fiber photometry, video-based movement assessments, and deep learning algorithms, the authors provide compelling evidence that the activity of these neurons correlates with net body movement over multiple behaviors and is independent of nutritional state. The authors also demonstrate that hypocretin/orexin release differs between two downstream projection sites, the locus coeruleus and substantia nigra, and are able to distinguish the activity in these sites that is due to inputs from these hypothalamic neurons vs. from other subcortical populations. The authors also convincingly show that the correlation between body movement and hypocretin/orexin neuron activity is much stronger compared to other subcortical regions. However, hypocretin/orexin neuron ablation does not affect the power spectra of movements, an observation that appears at odds with their overall conclusions.

Strengths:

The multidisciplinary approach using multiple state-of-the-art tools is supported by a rigorous experimental design and strong statistical analyses. The authors have been highly responsive to previous critiques. Concerns of another reviewer regarding the confound between arousal and movement have been addressed by new pupillometry data as a measure of arousal and multivariate analyses to distinguish between the contributions of arousal vs. movement to hypocretin/orexin neuron activity. The new data in Figure 2H added in response to a suggestion by Reviewer 3 particularly strengthens the paper.

Weaknesses:

Reviewer 2 mentioned that previous studies using orexin antagonists in rodents have largely found inconsistent effect of antagonizing orexin signaling on simple motor activity and points out that these studies are not referenced here. The authors respond that "orexin antagonism - or optogenetic silencing of HONs - evokes either reduced locomotion, or no effect on locomotor movements" and add references to paragraph 4 of the Discussion. Aside from the fact that 2 of the 3 references added are from the senior author, none address the fact that orexin antagonists induce sleep and that optogenetic silencing of these cells creates a condition where sleep can ensue with short latency - results that certainly affect body movement/locomotor activity.

eLife Assessment

This manuscript describes a novel approach for assessing cognitive function in freely moving mice in their home-cage, without human involvement. The authors provide convincing evidence in support of the tasks they developed to capture a variety of complex behaviors and demonstrate the utility of a machine learning approach to expedite the acquisition of task demands. This work is important given its potential utility for other investigators interested in studying mouse cognition.

Reviewer #1 (Public review):

Summary:

This is a new and important system that can efficiently train mice to perform a variety of cognitive tasks in a flexible manner. It is innovative and opens the door to important experiments in the neurobiology of learning and memory.

Strengths:

Strengths include: high n's, a robust system, task flexibility, comparison of manual-like training vs constant training, circadian analysis, comparison of varying cue types, long-term measurement, and machine teaching.

Weaknesses:

I find no major problems with this report.

Comments on revisions:

My concerns have been addressed now.

Reviewer #2 (Public review):

Summary:

The manuscript by Yu et al. describes a novel approach for collecting complex and different cognitive phenotypes in individually housed mice in their home cage. The authors report a simple yet elegant design that they developed for assessing a variety of complex and novel behavioral paradigms autonomously in mice.

Strengths:

The data are strong, the arguments are convincing, and I think the manuscript will be highly cited given the complexity of behavioral phenotypes one can collect using this relatively inexpensive ($100/box) and high-throughput procedure (without the need of human interaction). Additionally, the authors include a machine learning algorithm to correct for erroneous strategies that mice develop which is incredibly elegant and important for this approach, as mice will develop odd strategies when given complete freedom.

Weaknesses:

A limitation to this approach is that it requires mice to be individually housed for days to months. This is now adequately addressed in the discussion.

A major issue with continuous self-paced tasks such as the autonomous d2AFC used by the authors is that the inter-trial intervals can vary significantly. Mice may do a few trials, lose interest and disengage from the task for several hours. This is problematic for data analysis that relies on trial duration to be similar between trials (e.g., reinforcement learning algorithms). The authors now provide information regarding task engagement of the mice across a 24 hour cycle (e.g., trials started, trials finished across a 24 h period).

Movies - it would be beneficial for the authors to add commentary to the video (hit, miss trials). It was interesting watching the mice but not clear whether they were doing the task correctly or not. The new videos adequately address these concerns.

The strength of this paper (from my perspective) is the potential utility it has for other investigators trying to get mice to do behavioral tasks. However, not enough information was provided about the construction of the boxes, interface, and code for running the boxes. If the authors are not willing to provide this information through eLife, GitHub, or their own website then my evaluation of impact and significance of this paper would go down significantly. This information is now available to readers.

Minor concerns

Learning rate is confusing for Figure 3 results as it actually refers to trials to reach criterion, and not the actual rate of learning (e.g., slope). This has been modified in the manuscript.

Comments on revisions:

The authors have addressed all my concerns regarding this very exciting manuscript.

Reviewer #3 (Public review):

Summary:

In this set of experiments, the authors describe a novel research tool for studying complex cognitive tasks in mice, the HABITS automated training apparatus, and a novel "machine teaching" approach they use to accelerate training by algorithmically providing trials to animals that provide the most information about the current rule state for a given task.

Strengths:

There is much to be celebrated in an inexpensively constructed, replicable training environment that can be used with mice, which have rapidly become the model species of choice for understanding the roles of distinct circuits and genetic factors in cognition. Lingering challenges in developing and testing cognitive tasks in mice remain, however, and these are often chalked up to cognitive limitations in the species. The authors' findings, however, suggest that instead we may need to work creatively to meet mice where they live. In some cases it may be that mice may require durations of training far longer than laboratories are able to invest with manual training (up to over 100k trials, over months of daily testing) but that the tasks are achievable. The "machine teaching" approach further suggests that this duration could be substantially reduced by algorithmically optimizing each trial presented during training to maximize learning.

Weaknesses:

Cognitive training and testing in rodent models fill a number of roles. Sometimes, investigators are interested in within-subjects questions - querying a specific circuit, genetically defined neuron population, or molecule/drug candidate, by interrogating or manipulating its function in a highly trained animal. In this scenario, a cohort of highly trained animals which have been trained via a method that aims to make their behavior as similar as possible is a strength.

However, often investigators are interested in between-subjects questions - querying a source of individual differences that can have long term and/or developmental impacts, such as sex differences or gene variants. This is likely to often be the case in mouse models especially, because of their genetic tractability. In scenarios where investigators have examined cognitive processes between subjects in mice who vary across these sources of individual difference, the process of learning a task has been repeatedly shown to be different. The authors recognize that their approach is currently optimized for testing within-subjects questions, but begin to show how between-subjects questions might be addressed with this system.

The authors have perhaps shown that their main focus is highly-controlled within-subjects questions, as their dataset is almost exclusively made up of several hundred young adult male mice, with the exception of 6 females in a supplemental figure. It is notable that these female mice do appear to learn the two-alternative forced choice task somewhat more rapidly than the males in their cohort, and the authors suggest that future work with this system could be used to uncover strategies that differ across individuals.

Considering the implications for mice modeling relevant genetic variants, it is unclear to what extent the training protocols and especially the algorithmic machine teaching approach would be able to inform investigators about the differences between their groups during training. For investigators examining genetic models, it is unclear whether this extensive training experience would mitigate the ability to observe cognitive differences, or select for the animals best able to overcome them - eliminating the animals of interest. Likewise, the algorithmic approach aims to mitigate features of training such as side biases, but it is worth noting that the strategic uses of side biases in mice, as in primates, can benefit learning, rather than side biases solely being a problem. However, the investigators may be able to highlight variables selected by the algorithm that are associated with individual strategies in performing their tasks, and this would be a significant contribution.

A final, intriguing finding in this manuscript is that animal self-paced training led to much slower learning than "manual" training, by having the experimenter introduce the animal to the apparatus for a few hours each day. Manual training resulted in significantly faster learning, in almost half the number of trials on average, and with significantly fewer omitted trials. This finding does not necessarily argue that manual training is universally a better choice, because it led to more limited water consumption. However, it suggests that there is a distinct contribution of experimenter interactions and/or switching contexts in cognitive training, for example, by activating an "occasion setting" process to accelerate learning for a distinct period of time. Limiting experimenter interactions with mice may be a labor saving intervention, but may not necessarily improve performance. This could be an interesting topic of future investigation, of relevance to understanding how animals of all species learn.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

This is a new and important system that can efficiently train mice to perform a variety of cognitive tasks in a flexible manner. It is innovative and opens the door to important experiments in the neurobiology of learning and memory. 

Strengths: 

Strengths include: high n's, a robust system, task flexibility, comparison of manual-like training vs constant training, circadian analysis, comparison of varying cue types, long-term measurement, and machine teaching. 

Weaknesses: 

I find no major problems with this report. 

Minor weaknesses: 

(1)  Line 219: Water consumption per day remained the same, but number of trails triggered was more as training continued. First, is this related to manual-type training? Also, I'm trying to understand this result quantitatively, since it seems counter-intuitive: I would assume that with more trials, more water would be consumed since accuracy should go up over training (so more water per average trial). Am I understanding this right? Can the authors give more detail or understanding to how more trials can be triggered but no more water is consumed despite training? 

Thanks for the comment. We would like to clarify the phenomenon described in Line 219: As the training advanced, the number of trials triggered by mice per day decreased (rather than increased as you mentioned in the comment) gradually for both manual and autonomous groups of mice (Fig. 2H left). The performance, as you mentioned, improved over time (Fig. 2D and 2E), leading to an increased probability of obtaining water and thus relatively stable daily water intake (Fig. 2H middle). We believe the stable daily intake is the minimum amount of water required by the mice under circumstance of autonomous behavioral training. To make the statement more clearly, we indicated the corresponding figure numbers in the text.

Results “… As shown in Fig. 2H, autonomous training yielded significantly higher number of trial/day (980 ± 25 vs. 611 ± 26, Fig. 2H left) and more volume of water consumption/day (1.65 ± 0.06 vs. 0.97 ± 0.03 ml, Fig. 2H middle), which resulted in monotonic increase of body weight that was even comparable to the free water group (Fig.2H right). In contrast, the body weight in manual training group experienced a sharp drop at the beginning of training and was constantly lower than autonomous group throughout the training stage (Fig. 2H right).”

(2) Figure 2J: The X-axis should have some label: at least "training type". Ideally, a legend with colors can be included, although I see the colors elsewhere in the figure. If a legend cannot be added, then the color scheme should be explained in the caption.

Thanks for the suggestion. The labels with corresponding colors for x-axis have been added for Fig. 2J.

(3) Figure 2K: What is the purple line? I encourage a legend here. The same legend could apply to 2J.

Thanks for the suggestion. The legend has been added for Fig. 2K.

(4) Supplementary Figure S2 D: I do not think the phrase "relying on" is correct. Instead, I think "predicted by" or "correlating with" might be better. 

We thank the reviewer for the valuable suggestion. The phrase has been changed to ‘predicted by’ for better suitability.

Figure S2 “(D), percentage of trials significantly predicted by different regressors during task learning. …”

Reviewer #2 (Public review): 

Summary: 

The manuscript by Yu et al. describes a novel approach for collecting complex and different cognitive phenotypes in individually housed mice in their home cage. The authors report a simple yet elegant design that they developed for assessing a variety of complex and novel behavioral paradigms autonomously in mice. 

Strengths: 

The data are strong, the arguments are convincing, and I think the manuscript will be highly cited given the complexity of behavioral phenotypes one can collect using this relatively inexpensive ($100/box) and high throughput procedure (without the need for human interaction). Additionally, the authors include a machine learning algorithm to correct for erroneous strategies that mice develop which is incredibly elegant and important for this approach as mice will develop odd strategies when given complete freedom. 

Weaknesses:

(1) A limitation of this approach is that it requires mice to be individually housed for days to months. This should be discussed in depth. 

Thank you for raising this important point. We agree that the requirement for individual housing of mice during the training period is a limitation of our approach, and we appreciate the opportunity to discuss this in more depth. In the manuscript, we add a section to the Discussion to address this limitation, including the potential impact of individual housing on the mice, the rationale for individual housing in our study, and efforts or alternatives made to mitigate the effects of individual housing.

Discussion “… Firstly, our experiments were confined to single-housed mice, which is known to influence murine behavior and physiology, potentially affecting social interaction and stress levels [76]. In our study, individual housing was necessary to ensure precise behavioral tracking, eliminate competitive interactions during task performance, and maintain consistent training schedules without disruptions from cage-mate disturbances. However, the potential of group-housed training has been explored with technologies such as RFID [28,29,32–34] to distinguish individual mice, which potentially improving the training efficiency and facilitating research of social behaviors [77]. Notably, it has shown that simultaneous training of group-housed mice, without individual differentiation, can still achieve criterion performance [25].”

(2) A major issue with continuous self-paced tasks such as the autonomous d2AFC used by the authors is that the inter-trial intervals can vary significantly. Mice may do a few trials, lose interest, and disengage from the task for several hours. This is problematic for data analysis that relies on trial duration to be similar between trials (e.g., reinforcement learning algorithms). It would be useful to see the task engagement of the mice across a 24-hour cycle (e.g., trials started, trials finished across a 24-hour period) and approaches for overcoming this issue of varying inter-trial intervals. 

Thank you for your insightful comment regarding the variability in inter-trial intervals and its potential impact on data analysis. We agree that this is an important consideration for continuous self-paced tasks.

In our original manuscript, we have showed the general task engagement across 24-hour cycle (Fig. 2K), which revealed two peaks of engagements during the dark cycle with relatively fewer trials during the light cycle. To facilitate analyses requiring consistent trial durations, we defined trial blocks as sequences between two no-response trials. Notably, approximately 66.6% of trials occurred within blocks of >5 consecutive trials (Fig. 2L), which may be particularly suitable for such analyses.

In the revised manuscript, we also added the analysis of the histogram of inter-trial-interval for both the autonomous and manual training paradigms in HABITS (Fig. S2H), which shows that around 55.2% and 77.5% of the intervals are less than 2 seconds in autonomous and manual training, respectively.

Results “… We found more than two-third of the trials was done in >5-trial blocks (Fig. 2L left) which resulted in more than 55% of the trials were with inter-trial-interval less than 2 seconds (Fig. S2H).”

Regarding the approaches to mitigate the issue of varying inter-trial interval, we observed that manual training (i.e., manually transferring to HABITS for ~2 hr/day) in Fig. S2H resulted in more trials with short inter-trial-interval, suggesting that constrained access time promotes task engagement and reduces interval variability. Fig. 2L also indicated that the averaged correct rate increased and the earlylick rate decreased as the length of block increased. This approach could be valuable for studies where consistent trial timing is critical. In the context of our study, we could actually introduce a light, for example, to serve as the cue that prompt the animals to engage during a fixed time duration in a day.

Discussion “… In contrast, the self-paced nature of autonomous training may permit greater variability in attentional engagement 83 and inter-trial-intervals, which could be problematic for data analysis relaying on consistent intervals and/or engagements. Future studies should explore how controlled contextual constraints enhance learning efficiency and whether incorporating such measures into HABITS could optimize its performance.”

(3) Movies - it would be beneficial for the authors to add commentary to the video (hit, miss trials). It was interesting watching the mice but not clear whether they were doing the task correctly or not. 

Thanks for the reminder. We have added subtitles to both of the videos. Since the supplementary video1 was not recorded with sound, the correctness of the trials was hard to judge. We replaced the video with another one with clear sound recordings, and the subtitles were commented in detail.

(4) The strength of this paper (from my perspective) is the potential utility it has for other investigators trying to get mice to do behavioral tasks. However, not enough information was provided about the construction of the boxes, interface, and code for running the boxes. If the authors are not willing to provide this information through eLife, GitHub, or their own website then my evaluation of the impact and significance of this paper would go down significantly. 

Thanks for this important comment. We would like to clarify that the construction methods, GUI, code for our system, PCB and CAD files (newly uploaded) have already been made publicly available on https://github.com/Yaoyao-Hao/HABITS. Additionally, we have open-sourced all the codes and raw data for all training protocols (https://doi.org/10.6084/m9.figshare.27192897). We will continue to maintain these resources in the future.

Minor concerns: 

(5) Learning rate is confusing for Figure 3 results as it actually refers to trials to reach the criterion, and not the actual rate of learning (e.g., slope).

Thanks for pointing this out. The ‘learning rate’ which refers to trial number to reach criterion has been changed to ‘the number of trials to reach criterion’.

Reviewer #3 (Public review): 

Summary: 

In this set of experiments, the authors describe a novel research tool for studying complex cognitive tasks in mice, the HABITS automated training apparatus, and a novel "machine teaching" approach they use to accelerate training by algorithmically providing trials to animals that provide the most information about the current rule state for a given task. 

Strengths: 

There is much to be celebrated in an inexpensively constructed, replicable training environment that can be used with mice, which have rapidly become the model species of choice for understanding the roles of distinct circuits and genetic factors in cognition. Lingering challenges in developing and testing cognitive tasks in mice remain, however, and these are often chalked up to cognitive limitations in the species. The authors' findings, however, suggest that instead, we may need to work creatively to meet mice where they live. In some cases, it may be that mice may require durations of training far longer than laboratories are able to invest with manual training (up to over 100k trials, over months of daily testing) but the tasks are achievable. The "machine teaching" approach further suggests that this duration could be substantially reduced by algorithmically optimizing each trial presented during training to maximize learning. 

Weaknesses: 

(1) Cognitive training and testing in rodent models fill a number of roles. Sometimes, investigators are interested in within-subjects questions - querying a specific circuit, genetically defined neuron population, or molecule/drug candidate, by interrogating or manipulating its function in a highly trained animal. In this scenario, a cohort of highly trained animals that have been trained via a method that aims to make their behavior as similar as possible is a strength. 

However, often investigators are interested in between-subjects questions - querying a source of individual differences that can have long-term and/or developmental impacts, such as sex differences or gene variants. This is likely to often be the case in mouse models especially, because of their genetic tractability. In scenarios where investigators have examined cognitive processes between subjects in mice who vary across these sources of individual difference, the process of learning a task has been repeatedly shown to be different. The authors do not appear to have considered individual differences except perhaps as an obstacle to be overcome. 

The authors have perhaps shown that their main focus is highly-controlled within-subjects questions, as their dataset is almost exclusively made up of several hundred young adult male mice, with the exception of 6 females in a supplemental figure. It is notable that these female mice do appear to learn the two-alternative forced-choice task somewhat more rapidly than the males in their cohort.

Thank you for your insightful comments and for highlighting the importance of considering both within-subject and between-subject questions in cognitive training and testing in rodent models. We acknowledge that our study primarily focused on highly controlled within-subject questions. However, the datasets we provided did show preliminary evidences for the ‘between-subject’ questions. Key observations include:

The large variability in learning rates among mice observed in Fig. 2I;

The overall learning rate difference between male and female subjects (Fig. 2D vs. Fig. S2G);

The varying nocturnal behavioral patterns (Fig. 2K), etc.

We recognize the value of exploring between-subjects differences in mouse model and discussed more details in the Discussion part.

Discussion “Our study was designed to standardize behavior for the precise interrogation of neural mechanisms, specifically addressing within-subject questions. However, investigators are often interested in between-subject differences—such as sex differences or genetic variants—which can have long-term behavioral and cognitive implications [72,74]. This is particularly relevant in mouse models due to their genetic tractability [75]. Although our primary focus was not on between-subject differences, the dataset we generated provides preliminary evidence for such investigations. Several behavioral readouts revealed individual variability among mice, including large disparities in learning rates across individuals (Fig. 2I), differences in overall learning rates between male and female subjects (Fig. 2D vs. Fig. S2G), variations in nocturnal behavioral patterns (Fig. 2K), etc.”

(2) Considering the implications for mice modeling relevant genetic variants, it is unclear to what extent the training protocols and especially the algorithmic machine teaching approach would be able to inform investigators about the differences between their groups during training. For investigators examining genetic models, it is unclear whether this extensive training experience would mitigate the ability to observe cognitive differences, or select the animals best able to overcome them - eliminating the animals of interest. Likewise, the algorithmic approach aims to mitigate features of training such as side biases, but it is worth noting that the strategic uses of side biases in mice, as in primates, can benefit learning, rather than side biases solely being a problem. However, the investigators may be able to highlight variables selected by the algorithm that are associated with individual strategies in performing their tasks, and this would be a significant contribution.

Thank you for the insightful comments. We acknowledge that the extensive training experience, particularly through the algorithmic machine teaching approach, could potentially influence the ability to observe cognitive differences between groups of mice with relevant genetic variants. However, our study design and findings suggest that this approach can still provide valuable insights into individual differences and strategies used by the animals during training. First, the behavioral readout (including learning rate, engagement pattern, etc.) as mentioned above, could tell certain number of differences among mice. Second, detailed modelling analysis (with logistical regression modelling) could further dissect the strategy that mouse use along the training process (Fig. S2B). We have actually highlighted some variables selected by the regression that are associated with individual strategies in performing their tasks (Fig. S2C) and these strategies could be different between manual and autonomous training groups (Fig. S2D). We included these comments in the Discussion part for further clearance.

Discussion “… Furthermore, a detailed logistic regression analysis dissected the strategies mice employed during training (Fig. S2B). Notably, the regression identified variables associated with individual task-performance strategies (Fig. S2C), which also differed between manually and autonomously trained groups (Fig. S2D). Thus, our system could facilitate high-throughput behavioral studies exploring between-subject differences in the future.”

(3) A final, intriguing finding in this manuscript is that animal self-paced training led to much slower learning than "manual" training, by having the experimenter introduce the animal to the apparatus for a few hours each day. Manual training resulted in significantly faster learning, in almost half the number of trials on average, and with significantly fewer omitted trials. This finding does not necessarily argue that manual training is universally a better choice because it leads to more limited water consumption. However, it suggests that there is a distinct contribution of experimenter interactions and/or switching contexts in cognitive training, for example by activating an "occasion setting" process to accelerate learning for a distinct period of time. Limiting experimenter interactions with mice may be a labor-saving intervention, but may not necessarily improve performance. This could be an interesting topic of future investigation, of relevance to understanding how animals of all species learn.

Thank you for your insightful comments. We agree that the finding that manual training led to significantly faster learning compared to self-paced training is both intriguing and important. One of the possible reasons we think is due to the limited duration of engagement provided by the experimenter in the manual training case, which forced the mice to concentrate more on the trials (thus with fewer omitting trials) than in autonomous training. Your suggestion that experimenter interactions might activate an "occasion setting" process is particularly interesting. In the context of our study, we could actually introduce, for example, a light, serving as the cue that prompt the animals to engage; and when the light is off, the engagement was not accessible any more for the mice to simulate the manual training situation. We agree that this could be an interesting topic for future investigation that might create a more conducive environment for learning, thereby accelerating the learning rate.

Discussion “… Lastly, while HABITS achieves criterion performance in a similar or even shorter overall days compared to manual training, it requires more trials to reach the same learning criterion (Fig. 2G). We hypothesize that this difference in trial efficiency may stem from the constrained engagement duration imposed by the experimenter in manual training, which could compel mice to focus more intensely on task execution, resulting in less trial omissions (Fig. 2F). In contrast, the self-paced nature of autonomous training may permit greater variability in attentional engagement 83 and inter-trial-intervals, which could be problematic for data analysis relaying on consistent intervals and/or engagements. Future studies should explore how controlled contextual constraints enhance learning efficiency and whether incorporating such measures into HABITS could optimize its performance.”

Reviewer #2 (Recommendations for the authors):

As I mentioned in the weaknesses, I did not see code or CAD drawings for their home cages and how these interact with a computer.

Thanks for the comment. We would like to clarify that the construction methods, GUI, code for our system, PCB and CAD files (newly uploaded) have already been made publicly available on https://github.com/Yaoyao-Hao/HABITS.

eLife Assessment

This important study explores the power of computational methods to predict lifespan-extending small molecules, demonstrating that while these methods significantly increase hit rates, experimental validation remains essential. The study uses all-trans retinoic acid in Caenorhabditis elegans as a model, providing genetic and transcriptomic insights into its longevity effects. The data are compelling in describing a robust, computationally informed screening process for discovering compounds that extend lifespan in this species.

Reviewer #1 (Public review):

Summary:

This study highlights the strengths of using predictive computational models to inform C. elegans screening studies of compounds' effects on aging and lifespan. The authors primarily focus on all-trans retinoic acid (atRA), one of the 5 compounds (out of 16 tested) that extended C. elegans lifespan in their experiments. They show that atRA has positive effects on C. elegans lifespan and age-related health, while it has more modest and inconsistent effects (i.e., some detrimental impacts) for C. briggsae and C. tropicalis. In genetic experiments designed to evaluate contributing mediators of lifespan extension with atRA exposure, it was found that 150 µM of atRA did not significantly extend lifespan in akt-1 or akt-2 loss-of-function mutants, nor in animals with loss of function of aak-2, or skn-1 (in which atRA had toxic effects); these genes appear to be required for atRA-mediated lifespan extension. hsf-1 and daf-16 loss-of-function mutants both had a modest but statistically significant lifespan extension with 150 µM of atRA, suggesting that these transcription factors may contribute towards mediating atRA lifespan extension, but that they are not individually required for some lifespan extension. RNAseq assessment of transcriptional changes in day 4 atRA-treated adult wild type worms revealed some interesting observations. Consistent with the study's genetic mutant lifespan observations, many of the atRA-regulated genes with the greatest fold-change differences are known regulated targets of daf-2 and/or skn-1 signaling pathways in C. elegans. hsf-1 loss-of-function mutants show a shifted atRA transcriptional response, revealing a dependence on hsf-1 for ~60% of the atRA-downregulated genes. On the other hand, RNAseq analysis in aak-2 loss-of-function mutants revealed that aak-2 is only required for less than a quarter of the atRA transcriptional response. All together, this study is a proof of the concept that computational models can help optimize C. elegans screening approaches that test compounds' effects on lifespan, and provides comprehensive transcriptomic and genetic insights into the lifespan-extending effects of all-trans retinoic acid (atRA).

Strengths:

A clearly described and well-justified account describes the approach used to prioritize and select compounds for screening, based on using the top candidates from a published list of computationally ranked compounds (Fuentealba et al., 2019) that were cross-referenced with other bioinformatics publications to predict anti-aging compounds, after de-selecting compounds previously evaluated in C. elegans as per the DrugAge database. 16 compounds were tested at 4-5 different concentrations to evaluate effects on C. elegans lifespan.

Robust experimental design was undertaken evaluating the lifespan effects of atRA, as it was tested on three strains each of C. elegans, C. briggsae, and C. tropicalis, with trial replication performed at three distinct laboratories. These observations extended beyond lifespan to include evaluations of health metrics related to swimming performance.

In-depth analyses of the RNAseq data of whole-worm transcriptional responses to atRA revealed interesting insights into regulator pathways and novel groups of genes that may be involved in mediating lifespan-extension effects (e.g., atRA-induced upregulation of sphingolipid metabolism genes, atRA-upregulation of genes in a poorly-characterized family of C. elegans paralogs predicted to have kinase-like activity, and disproportionate downregulation of collagen genes with atRA).

Weaknesses:

The authors' computational-based compound screening approach led to a ~30% prediction success rate for compounds that could extend the median lifespan of C. elegans. However, follow-up experiments on the top compounds highlighted the fact that some of these observed "successes" could be driven by indirect, confounding effects of these compounds on the bacterial food source, rather than direct beneficial effects on C. elegans physiology and lifespan. For instance, this appeared to be the case for the "top" hit of propranolol. Other compounds were not tested with metabolically inert or killed bacteria to preclude the possibility of bacteria-produced metabolites exerting observed effects; this might be a useful future direction to consider.

Transcriptomic analyses of atRA effects were extensive in this study, but discussions of potential non-transcriptional effects of key proposed regulators (such as AMPK) were limited. For instance, other outputs of aak-2/AMPK (non-transcriptional changes to metabolic balance, autophagy, etc.) might account for its requirement for mediating lifespan extension effects, since aak-2 was not required for a major proportion of atRA transcriptional responses.

Comments on revisions:

In their revisions, the authors resolved all of my initial recommendations, and I have no additional suggestions.

Reviewer #2 (Public review):

Summary:

In this manuscript, Banse et al. experimentally validate the power of computational approaches that predict anti-aging molecules using the multi-species approach of the Caenorhabditis Intervention Testing Program (CITP). Filtering candidate molecules based on transcriptional profiles, ML models, literature searches, and the DrugAge database, they selected 16 compounds for testing. Of those, eight did not affect C. elegans' lifespan, three shortened it, and five extended C. elegans' lifespan, resulting in a hit rate of over 30%. Of those five, they then focused on all-trans-retinoic acid (atRA), a compound that has previously resulted in contradictory effects. The lifespan-extending effect of atRA was consistent in all C. elegans strains tested, was absent in C. briggsae, and a small effect was observed in some C. tropicalis strains. Similar results were obtained for measures of healthspan. The authors then investigated the mechanism of action of atRA and showed that it was only partially dependent on daf-16 but required akt-1, akt-2, skn-1, hsf-1, and, to some degree, pmk-1. The authors further investigate the downstream effects of atRA exposure by conducting RNAseq experiments in both wild-type and mutant animals to show that some, but surprisingly few, of the gene expression changes that are observed in wild-type animals are lost in the hsf-1 and aak-2 mutants

Strengths:

Overall, this study is well-conceived and executed as it investigates the effect of atRA across different concentrations, strains, and species, including life and health span. Revealing the variability between sites, assays, and the method used is a powerful aspect of this study. It will do a lot to dispel the nonsensical illusion that we can determine a per cent increase in lifespan to the precision of two floating point numbers.

An interesting and potentially important implication arises from this study. The computational selection of compounds was agnostic regarding strain or species differences and was predominantly based on observations made in mammalian systems. The hit rate calculated is based on the results of C. elegans and not on the molecules' effectiveness in Briggsae or Tropicalis. If it were, the hit rate would be much lower. How is that? It would suggest that ML models and transcriptional data obtained from mammals have a higher predictive value for C. elegans than for the other two species. This selectivity for C.elegans over C.tropicalis and C.Briggsae seems both puzzling and unexpected. The predictions for longevity were based on the transcriptional data in cell lines. Would it be feasible to compare the mammalian data to the transcriptional data in Fig. 5 and see how well they match? While this is clear beyond the focus of this study, an implied prediction is that running RNAseqs for all these strains exposed to atRA would reveal that the transcriptional changes observed in the strains where it extends lifespan the most should match the mammalian data best. Otherwise, how could the mammalian datasets be used to predict the effects for C.elegans over C.Briggsae or C.Tropicalis have more predictive for one species than the other? There are a lot of IFs in this prediction, but such an experiment would reconsider and validate the basis on which the original predictions were made.

Weaknesses:

Many of the most upregulated genes, such as cyps and pgps are xenobiotic response genes upregulated in many transcriptional datasets from C.elegans drug studies. Their expression might be necessary to deal with atRA breakdown metabolites to prevent toxicity rather than confer longevity. Because atRA is very light sensitive and has toxicity of breakdown, metabolites may explain some of the differences observed with the lifespan of machine effects compared to standard assay practices. However, the authors provide a potential explanation for that observation.

Comments on revisions:

The authors have adequately addressed my concerns and the paper is suitable for publication.

Reviewer #3 (Public review):

Summary:

In this study, Banse et al., demonstrate that combining computer prediction with genetic analysis in distinct Caenorhabditis species can streamline the discovery of aging interventions by taking advantage of the diverse pool of compounds that are currently available. They demonstrate that through careful prioritization of candidate compounds, they are able to accomplish a 30% positive hit rate for interventions that produce significant lifespan extensions. Within the positive hits, they focus on all-trans retinoic acid (atRA) and discover that it modulates lifespan through conserved longevity pathways such as AKT-1 and AKT-2 (and other conserved Akt-targets such as Nrf2/SKN-1 and HSF1/HSF-1) as well as through AAK-2, a conserved catalytic subunit of AMPK. To better understand the genetic mechanisms behind lifespan extension upon atRA treatment, the authors perform RNAseq experiments using a variety of genetic backgrounds for cross comparison and validation. Using this current state-of-the-art approach for studying gene expression, the authors determine that atRA treatment produces gene expression changes across a broad set of stress-response and longevity-related pathways. Overall, this study is important since it highlights the potential of combining traditional genetic analysis in the genetically tractable organism C. elegans with computational methods that will become even more powerful with the swift advancements being made in artificial intelligence. The study possesses both theoretical and practical implications not only in the field of aging, but also in related fields such as health and disease. Most of the claims in this study are supported by solid evidence, but the conclusions can be refined with a small set of additional experiments or re-analysis of data.

Strengths:

(1) The criteria for prioritizing compounds for screening are well-defined and is easy to replicate (Figure 1), even for scientists with limited experience in computational biology. The approach is also adaptable to other systems or model organisms.

(2) I commend the researchers for doing follow-up experiments with the compound propranolol to verify its effect of lifespan (Figure 2- figure supplement 2), given the observation that it affected the growth of OP50. To prevent false hits in the future, the reviewer recommends the use of inactivated OP50 for future experiments to remove this confounding variable.

(3) The sources of variation (Figure 3-figure supplement 2) are taken into account and demonstrates the need for advancing our understanding of the lifespan phenotype due to inter-individual variation.

(4) The addition of the C. elegans swim test in addition to the lifespan assays provides further evidence of atRA-induced improvement in longevity.

(5) The RNAseq approach was performed in a variety of genetic backgrounds, which allowed the authors to determine the relationship between AAK-2 and HSF-1 regulation of the retinoic acid pathway in C. elegans, specifically, that the former functions downstream of the latter.

Weaknesses:

(1) The authors demonstrate that atRA extends lifespan in a species-specific manner (Figure 3). Specifically, this extension only occurs in the species C. elegans yet, the title implies that atRA-induced lifespan extension occurs in different Caenorhabditis species when it is clearly not the case. While the authors state that failure to observe phenotypes in C. briggsae and C. tropicalis is a common feature of CITP tests, they do not speculate as to why this phenomenon occurs.

(2) There are discrepancies between the lifespan curves by hand (Figure 3-Figure supplement 1) and using the automated lifespan machine (Figure 3-supplement 3). Specifically, in the automated lifespan assays, there are drastic changes in the slope of the survival curve which do not occur in the manual assays and may be suggestive that confounding factors may still operate or produce additional variation in ALM experiments despite relatively well-controlled environmental conditions.

Author response:

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

Reviewer #1 (Public review):

Summary:

This study highlights the strengths of using predictive computational models to inform C. elegans screening studies of compounds' eCects on aging and lifespan. The authors primarily focus on all-trans retinoic acid (atRA), one of the 5 compounds (out of 16 tested) that extended C. elegans lifespan in their experiments. They show that atRA has positive eCects on C. elegans lifespan and age-related health, while it has more modest and inconsistent eCects (i.e., some detrimental impacts) for C. briggsae and C. tropicalis. In genetic experiments designed to evaluate contributing mediators of lifespan extension with atRA exposure, it was found that 150 µM of atRA did not significantly extend lifespan in akt1 or akt-2 loss-of-function mutants, nor in animals with loss of function of aak-2, or skn-1 (in which atRA had toxic eCects); these genes appear to be required for atRA-mediated lifespan extension. hsf-1 and daf-16 loss-of-function mutants both had a modest but statistically significant lifespan extension with 150 µM of atRA, suggesting that these transcription factors may contribute towards mediating atRA lifespan extension, but that they are not individually required for some lifespan extension. RNAseq assessment of transcriptional changes in day 4 atRA-treated adult wild-type worms revealed some interesting observations. Consistent with the study's genetic mutant lifespan observations, many of the atRA-regulated genes with the greatest fold-change diCerences are known regulated targets of daf-2 and/or skn-1 signaling pathways in C. elegans. hsf-1 loss-offunction mutants show a shifted atRA transcriptional response, revealing a dependence on hsf-1 for ~60% of the atRA-downregulated genes. On the other hand, RNAseq analysis in aak-2 loss-of-function mutants revealed that aak-2 is only required for less than a quarter of the atRA transcriptional response. All together, this study is proof of the concept that computational models can help optimize C. elegans screening approaches that test compounds' eCects on lifespan, and provide comprehensive transcriptomic and genetic insights into the lifespan-extending eCects of all-trans retinoic acid (atRA).

Strengths:

(1) A clearly described and well-justified account describes the approach used to prioritize and select compounds for screening, based on using the top candidates from a published list of computationally ranked compounds (Fuentealba et al., 2019) that were crossreferenced with other bioinformatics publications to predict anti-aging compounds, after de-selecting compounds previously evaluated in C. elegans as per the DrugAge database. 16 compounds were tested at 4-5 diCerent concentrations to evaluate eCects on C. elegans lifespan.

(2) Robust experimental design was undertaken evaluating the lifespan eCects of atRA, as

it was tested on three strains each of C. elegans, C. briggsae, and C. tropicalis, with trial replication performed at three distinct laboratories. These observations extended beyond lifespan to include evaluations of health metrics related to swimming performance.

(3) In-depth analyses of the RNAseq data of whole-worm transcriptional responses to atRA revealed interesting insights into regulator pathways and novel groups of genes that may be involved in mediating lifespan-extension eCects (e.g., atRA-induced upregulation of sphingolipid metabolism genes, atRA-upregulation of genes in a poorly-characterized family of C. elegans paralogs predicted to have kinase-like activity, and disproportionate downregulation of collagen genes with atRA).

We thank the reviewer for highlighting the strengths of our paper.

Weaknesses:

(1) The authors' computational-based compound screening approach led to a ~30% prediction success rate for compounds that could extend the median lifespan of C.elegans. However, follow-up experiments on the top compounds highlighted the fact that some of these observed "successes" could be driven by indirect, confounding eCects of these compounds on the bacterial food source, rather than direct beneficial eCects on C. elegans physiology and lifespan. For instance, this appeared to be the case for the "top" hit of propranolol; other compounds were not tested with metabolically inert or killed bacteria. In addition, there are no comparative metrics provided to compare this study's ~30% success rate to screening approaches that do not use computational predictions.

We do test whether compounds have a direct e:ect on bacterial growth. We have the text to clarify that fact. There may be potential lifespan e:ects from atRA due to changes in bacterial metabolites, however exploring that more fully is beyond the scope of the current work. 

We very much appreciate the question regarding relative success. An appropriate benchmark for “hit rate” is perhaps best provided by Petrascheck, Ye & Buck (2007), who conducted a large-scale screen of 88,000 compounds for e:ects on adult lifespan in C. elegans. They found an initial screening hit rate of 1.2% (1083/88000), which were then retested for a verified hit rate of 0.13% (115/88000), with a retest failure rate of 89% (968/1083). Similarly, Lucanic et al. (2016) screened 30,000 compounds, with an initial hit rate of approximately 1.7% (~500/30000), or these 180 were selected for retesting, resulting in a final verified hit rate of 0.19% (57/29680), which is comparable to the Petrascheck et al. result. The text in the discussion has been modified to include these studies.

(2)Transcriptomic analyses of atRA eCects were extensive in this study, but evaluations and discussions of non-transcriptional eCects of key proposed regulators (such as AMPK) were limited. For instance, non-transcriptional eCects of aak-2/AMPK might account for its requirement for mediating lifespan extension eCects, since aak-2 was not required for a major proportion of atRA transcriptional responses.

We naturally agree with the reviewer that non-transcriptional e:ects are possible and well worth pursuing in future work. However, these e:ects will still show within our study, as any upstream non-transcriptional e:ects are likely to reveal themselves in downstream transcriptional changes, as measured here.  

Reviewer #2 (Public review):

Summary:

In this manuscript, Banse et al. experimentally validate the power of computational approaches that predict anti-aging molecules using the multi-species approach of the Caenorhabditis Intervention Testing Program (CITP). Filtering candidate molecules based on transcriptional profiles, ML models, literature searches, and the DrugAge database, they selected 16 compounds for testing. Of those, eight did not aCect C.elegan's lifespan, three shortened it, and five extended C.elegan's lifespan, resulting in a hit rate of over 30%. Of those five, they then focused on all-trans-retinoic acid (atRA), a compound that has previously resulted in contradictory eCects. The lifespan-extending eCect of atRA was consistent in all C. elegans strains tested, was absent in C. briggsae, and a small eCect was observed in some C. tropicalis strains. Similar results were obtained for measures of healthspan. The authors then investigated the mechanism of action of atRA and showed that it was only partially dependent on daf-16 but required akt-1, akt-2, skn-1, hsf-1, and, to some degree, pmk-1. The authors further investigate the downstream eCects of atRA exposure by conducting RNAseq experiments in both wild-type and mutant animals to show that some, but surprisingly few, of the gene expression changes that are observed in wild-type animals are lost in the hsf-1 and aak-2 mutants.

Strengths:

Overall, this study is well conceived and executed as it investigates the eCect of atRA across diCerent concentrations, strains, and species, including life and health span. Revealing the variability between sites, assays, and the method used is a powerful aspect of this study. It will do a lot to dispel the nonsensical illusion that we can determine a percent increase in lifespan to the precision of two floating point numbers.

An interesting and potentially important implication arises from this study. The computational selection of compounds was agnostic regarding strain or species diCerences and was predominantly based on observations made in mammalian systems. The hit rate calculated is based on the results of C. elegans and not on the molecules' eCectiveness in Briggsae or Tropicalis. If it were, the hit rate would be much lower. How is that? It would suggest that ML models and transcriptional data obtained from mammals have a higher predictive value for C. elegans than for the other two species. This selectivity for C.elegans over C.tropicalis and C.Briggsae seems both puzzling and unexpected. The predictions for longevity were based on the transcriptional data in cell lines.

This is a common observation in the CITP for which we do not currently have a satisfying explanation. For whatever reason, C. elegans is much more responsive to compounds than other species, much like it is more responsive to RNAi and other environmental interventions. It may be less active in detoxifying external agents than the other species, although this is just speculation at the moment. We continue to investigate this question, but that work is beyond the scope of the present paper.

Would it be feasible to compare the mammalian data to the transcriptional data in Figure 5 and see how well they match? While this is clear beyond the focus of this study, an implied prediction is that running RNAseqs for all these strains exposed to atRA would reveal that the transcriptional changes observed in the strains where it extends lifespan the most should match the mammalian data best. Otherwise, how could the mammalian datasets be used to predict the eCects of C.elegans over C.Briggsae or C.Tropicalis have more predictive for one species than the other? There are a lot of IFs in this prediction, but such an experiment would reconsider and validate the basis on which the original predictions were made.

These questions are worth pursuing in the future but are beyond the scope of the current work.

Weaknesses:

Many of the most upregulated genes, such as cyps and pgps are xenobiotic response genes upregulated in many transcriptional datasets from C. elegans drug studies. Their expression might be necessary to deal with atRA breakdown metabolites to prevent toxicity rather than confer longevity. Because atRA is very light sensitive and has toxicity of breakdown, metabolites may explain some of the diCerences observed with the lifespan of machine eCects compared to standard assay practices.

This is certainly a possibility, although we often observe longer lifespans on the ALM, perhaps because they themselves are stressful, thereby providing a more sensitive background environment for detecting positive stress response modulators.

Reviewer #3 (Public review):

Summary:

In this study, Banse et al., demonstrate that combining computer prediction with genetic analysis in distinct Caenorhabditis species can streamline the discovery of aging interventions by taking advantage of the diverse pool of compounds that are currently available. They demonstrate that through careful prioritization of candidate compounds, they are able to accomplish a 30% positive hit rate for interventions that produce significant lifespan extensions. Within the positive hits, they focus on all-trans retinoic acid (atRA) and discover that it modulates lifespan through conserved longevity pathways such as AKT-1 and AKT-2 (and other conserved Akt-targets such as Nrf2/SKN-1 and HSF1/HSF-1) as well as through AAK-2, a conserved catalytic subunit of AMPK. To better understand the genetic mechanisms behind lifespan extension upon atRA treatment, the authors perform RNAseq experiments using a variety of genetic backgrounds for cross-comparison and validation. Using this current state-of-the-art approach for studying gene expression, the authors determine that atRA treatment produces gene expression changes across a broad set of stress-response and longevity-related pathways. Overall, this study is important since it highlights the potential of combining traditional genetic analysis in the genetically tractable organism C. elegans with computational methods that will become even more powerful with the swift advancements being made in artificial intelligence. The study possesses both theoretical and practical implications not only in the field of aging but also in related fields such as health and disease. Most of the claims in this study are supported by solid evidence, but the conclusions can be refined with a small set of additional experiments or re-analysis of data.

Strengths:

(1) The criteria for prioritizing compounds for screening are well-defined and easy to replicate (Figure 1), even for scientists with limited experience in computational biology. The approach is also adaptable to other systems or model organisms.

(2) I commend the researchers for doing follow-up experiments with the compound propranolol to verify its eCect on lifespan (Figure 2 Supplement 2), given the observation that it aCected the growth of OP50. To prevent false hits in the future, the reviewer recommends the use of inactivated OP50 for future experiments to remove this confounding variable.

(3) The sources of variation (Figure 3, Figure Supplement 2) are taken into account and demonstrate the need for advancing our understanding of the lifespan phenotype due to inter-individual variation.

(4) The addition of the C. elegans swim test in addition to the lifespan assays provides further evidence of atRA-induced improvement in longevity.

(5) The RNAseq approach was performed in a variety of genetic backgrounds, which allowed the authors to determine the relationship between AAK-2 and HSF-1 regulation of the retinoic acid pathway in C. elegans, specifically, that the former functions downstream of the latter.

We thank the reviewer for highlighting these strengths.

Weaknesses:

(1) The filtering of compounds for testing using the DrugAge database requires that the database is consistently updated. In this particular case, even though atRA does not appear in the database, the authors themselves cite literature that has already demonstrated atRA-induced lifespan extension, which should have precluded this compound from the analysis in the first place.

As often happens in science, this work was initiated before Statzer et al. (2021) was published. As such, it is included in the test set.

(2) The threshold for determining positive hits is arbitrary, and in this case, a 30% positive hit rate was observed when the threshold is set to a lifespan extension of around 5% based on Figure 1B (the authors fail to explicitly state the cut-oC for what is considered a positive hit).

Any compound that statistically increases lifespan is considered a positive hit by the CITP. The CITP in general is powered to detect minimum e:ect sizes of 5%.

(3) The authors demonstrate that atRA extends lifespan in a species-specific manner (Figure 3). Specifically, this extension only occurs in the species C. elegans yet, the title implies that atRA-induced lifespan extension occurs in diCerent Caenorhabditis species when it is clearly not the case. While the authors state that failure to observe phenotypes in C. briggsae and C. tropicalis is a common feature of CITP tests, they do not speculate as to why this phenomenon occurs.

Please see the comment above.

(4) There are discrepancies between the lifespan curves by hand (Figure 3 Figure Supplement 1) and using the automated lifespan machine (Figure 3 Supplement 3). Specifically, in the automated lifespan assays, there are drastic changes in the slope of the survival curve which do not occur in the manual assays. This may be due to improper filtering of non-worm objects, improper annotation of death times, or improper distribution of plates in each scanner.

Our storyboarding SOP ensures that discrepancies in the shape of the curve are unlikely to be due to annotation errors. We check every page of the storyboard by hand, so all non-worm objects are excluded. Furthermore, the first and last ~10% of deaths are checked by hand (as we observed that these time points are the most likely to be wrongly called by the software), with a few deaths chosen at random from the middle to ensure that the software is calling death times accurately. If we find a high amount of inaccurately called deaths, the entire plate is annotated by hand. For this specific experiment, 18% of the total deaths were hand annotated. Plates are randomly distributed across each scanner in an e:ort to prevent bias. As noted above, it does appear that the ALM environment and the “by hand” environment are somewhat di:erent.

(5) The authors miss an opportunity to determine whether the lifespan extension phenotype attributed to the retinoic acid pathway is mostly transcriptional in nature or whether some of it is post-transcriptional. The authors even state "that while aak-2 is absolutely required for the longevity eCects of atRA, aak-2 is required only for a small proportion (~1/4) of the transcriptional response", suggesting that some of the eCects are post-transcriptional. Further information could have been obtained had the authors also performed RNAseq analysis on the tol-1 mutant which exhibited an enhanced response to atRA compared to wild-type animals, and comparing the magnitude of gene expression changes between the tol-1 mutant and all other genetic backgrounds for which RNAseq was performed.

Reviewer #1 (Recommendations for the authors):

(1) Will the raw RNA-seq data be publicly deposited? Please clarify. This would strengthen the value of the study.

All data is available. We have clarified this in the text.

(2) Since all-trans retinoic acid is a metabolite of vitamin A, it seems important to include a discussion of and reference to the recent study SKN-1/NRF2 upregulation by vitamin A is conserved from nematodes to mammals and is critical for lifespan extension in Caenorhabditis elegans (Sirakawin et al Cell Reports 2024). Sirakawin et al include data that corroborates and expands on the findings of the current study, including the observation that vitamin A reduces whole-body lipid deposition (agrees with some of the transcriptional findings in the current study); that vitamin A protects against oxidative stress; that vitamin A elevates expression of gst-5, skn-1, and pmk-1; and that loss-offunction mutation of skn-1 has similar eCects to the current study, in terms of suppressing lifespan-extending eCects of vitamin A. In addition, adding some discussion of oxidative stress would strengthen this work, in light of widespread perceptions of the antioxidant properties of vitamin A (and its metabolites).

Thank you for this suggestion. We have added this citation to the discussion.

(3) Minor typo: Lines 341-342 - After a sentence that contains the phrase "collagen and neuropeptide related genes", the next sentence uses the term "the latter" in reference to the collagen genes (should be "the former").

Edited in text.

(4) Minor correction: In Figure 6, the information in the figure legend is swapped for figure panels A) and B).

Edited in figure caption.

(5) To me, the subtitle heading "Loss of AMPK leads to a unique transcriptional profile in response to atRA treatment" (Line 403) is misleading, considering the contents of the text in that section, and the data presented in Figure 6.

We have altered this heading to reflect this comment.

Reviewer #2 (Recommendations for the authors):

Using diCerent colors for the diCerent testing sites would make Figure 3 more readable.

Edited so that each lab is represented by a di:erent shade of green.

Reviewer #3 (Recommendations for the authors):

It would be interesting to investigate the eCect of even higher concentrations of atRA as it has been reported that atRA accumulation is associated with deleterious phenotypes in mice (Snyder et al., 2020, FASEB J).

We tested the highest concentration (150 uM) based on the solubility of the compound using our standardized plate treatment protocol, so we are unable to test higher concentrations.  

A good first guess for a downstream retinoid receptor is nhr-23 which is the homolog of the vertebrate ROR genes. Stehlin-Gaon et al. (2003, Nat Struct Mol Biol) have shown that atRA is a ligand for the orphan nuclear receptor RORβ. It might be interesting to study the eCects of atRA on an nhr-23::AID (auxin inducible degron) background. This would allow you to circumvent the developmental phenotypes as a result of nhr-23 knockdown. Patrick/Stephen

A few notes on the text/figures:

Line 342: I believe the authors meant "former" instead of "latter".

Corrected in text.

Line 346: Can you also highlight col-144 in Fig. 5 S1?

This is not really feasible, as it is in the cluster near the where the axes meet (red arrow).

Line 400: CUB pathogen - based on Figure 6 Supp 1, this occurs in aak-2 and not in hsf-1.

Great catch by the reviewer. We have updated the figure with the correct information.

Line 414: hedgehog-like signaling - occurs in hsf-1 instead of aak-2. Similar inconsistencies occur in lines 415 (sterol), 417 (C-type lectin), and 418 (unassigned pathogens)

We have updated the text to eliminate potential conflicts/confusion in the presentation here.

Line 434: I believe the authors meant Figure "6" instead of "7"

Edited in text.

Line 475: Is it "fifteen" or "sixteen" compounds initially targeted?

Edited in text.

Can you please include the population sizes for the lifespan assays if not yet included in the detailed protocol to be published in FigShare (to which I currently do not have access to)?

Added “50 animals per petri plate” to Lifespan Assay methods section; additionally, all sample sizes are included as a summary tab in each dataset on figshare.com (10.6084/m9.figshare.c.6320690).

eLife Assessment

The authors of this important study investigate how telomere length regulates hTERT expression via non-telomeric binding of the telomere-associated protein TRF2. They conclusively show that TRF2 binding to long telomeres results in a reduction in its binding to the hTERT promoter, while short telomeres restore TRF2 binding in the hTERT promoter, recruiting repressor complexes like PRC2, and suppressing hTERT expression. There is convincing support for the claims and the findings should be of broad interest for cell biologists and those working in fields where telomeres alter function, such as cancer and aging.

Reviewer #1 (Public review):

Summary:

The authors in this study extensively investigate how telomere length (TL) regulates hTERT expression via non-telomeric binding of the telomere-associated protein TRF2. They conclusively show that TRF2 binding to long telomeres results in a reduction in its binding to the hTERT promoter. In contrast, short telomeres restore TRF2 binding in the hTERT promoter, recruiting repressor complexes like PRC2, and suppressing hTERT expression. The study presents several significant findings revealing a previously unknown mechanism of hTERT regulation by TRF2 in a TL-dependent manner

Strengths:

(1) A previously unknown mechanism linking telomere length and hTERT regulation through the non-telomeric TRF2 protein has been established, strengthening our understanding of telomere biology.

(2) The authors used both cancer cell lines and iPSCs to showcase their hypothesis and multiple parameters to validate the role of TRF2 in hTERT regulation.

(3) Comprehensive integration of the recent literature findings and implementation in the current study.

(4) In vivo validation of the findings.

(5) Rigorous controls and well-designed assays have been used.

Comments on current version:

The current version of the manuscript has addressed all the reviewers' concerns to the best of its ability. However, understanding the limitations of the authors, exploring ALT cell lines for the current mechanism would be desirable in the future.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors in this study extensively investigate how telomere length (TL) regulates hTERT expression via non-telomeric binding of the telomere-associated protein TRF2. They conclusively show that TRF2 binding to long telomeres results in a reduction in its binding to the hTERT promoter. In contrast, short telomeres restore TRF2 binding in the hTERT promoter, recruiting repressor complexes like PRC2, and suppressing hTERT expression. The study presents several significant findings revealing a previously unknown mechanism of hTERT regulation by TRF2 in a TL-dependent manner

Strengths:

(1) A previously unknown mechanism linking telomere length and hTERT regulation through the non-telomeric TRF2 protein has been established strengthening the telomere biology understanding.

(2) The authors used both cancer cell lines and iPSCs to showcase their hypothesis and multiple parameters to validate the role of TRF2 in hTERT regulation.

(3) Comprehensive integration of the recent literature findings and implementation in the current study.

(4) In vivo validation of the findings.

(5) Rigorous controls and well-designed assays have been use.

Weaknesses:

(1) The authors should comment on the cell proliferation and morphology of the engineered cell lines with ST or LT.

The cell proliferation and morphology of the engineered cells were monitored during experiments. With a doubling time within 16-18 hours, all the cancer cell line pairs used in the study were counted and seeded equally before experiments.

No significant difference in morphology or cell count (before harvesting for experiments) was noted for the stable cell lines, namely, HT1080 ST-HT1080 LT, HCT116 p53 null scrambled control-HCT116 p53 null hTERC knockdown.

MDAMB 231 cells which were treated with guanine-rich telomere repeats (GTR) over a period of 12 days, as per the protocol mentioned in Methods. Due to the alternate day of GTR treatment in serum-free media followed by replenishment with serum-supplemented media, we noted that cells would undergo periodic delay in their proliferation (or transient arrest) aligning with the GTR oligo-feeding cycles and appeared somewhat larger in comparison to their parental untreated cells.

Next, the cells with Cas9-telomeric sgRNA mediated telomere trimming were maintained transiently (till 3 days after transfection). During this time, no significant change in morphology or cell proliferation was observed in any of the cell lines, namely HCT116 or HEK293T Gaussia Luciferase reporter cells. iPSCs were also monitored. However, no change in morphology or cellular proliferation was observed during the 5 days post-transfection and antibiotic selection.  

(2) Also, the entire study uses engineered cell lines, with artificially elongated or shortened telomeres that conclusively demonstrate the role of hTERT regulation by TRF2 in telomere-length dependent manner, but using ALT negative cell lines with naturally short telomere length vs those with long telomeres will give better perspective. Primary cells can also be used in this context.

The reviewer correctly highlights (as we also acknowledge in the Discussion) that our study primarily utilizes engineered cell lines with artificially elongated or shortened telomeres. We agree that using ALT-negative cells with naturally short versus long telomeres would provide additional perspective. However, a key challenge in this experimental setup is the inherent variation in TRF2 protein levels among these cell types—a parameter central to our hypothesis. Comparing observations across such non-isogenic cell line pairs presents experimental limitations as these would require extensive normalization for multiple factors and introduce additional complexities, which would be difficult to interpret with clarity.

We had also explored primary cells, specifically foreskin fibroblasts and MRC5 lung fibroblasts, as suggested by the reviewer. However, we encountered two significant challenges. To achieve a notable telomere length difference of at least 20%, these primary cells had to undergo a minimum of 25 passages. During this period, we observed a substantial decline in their proliferation capacity and an increased tendency toward replicative senescence. Additionally, we noted a significant reduction in TRF2 protein levels as the primary cells aged, consistent with findings from Fujita K et al., 2010 (Nat Cell Biol.), which reported p53-induced, Siah-1-mediated proteasomal degradation of TRF2. Due to these practical limitations, we focused on cancer cell lines with respective isogenic backgrounds, ensuring a controlled experimental framework. On the other hand, this opens new avenues for future research to explore broader implications. Investigating other primary cell types that may not present these challenges could be a valuable direction for future studies.

(3) The authors set up time-dependent telomere length changes by dox induction, which may differ from the gradual telomere attrition or elongation that occurs naturally during aging, disease progression, or therapy. This aspect should be explored.

In this study, we utilized a Doxycycline-inducible hTERT expression system to modulate telomere length in cancer cells, aiming to capture any gradual changes that might occur upon steady telomerase induction or overexpression—an event frequently observed in cancer progression. We monitored telomere length and telomerase activity at regular intervals (Supplementary Figure 2), noting a gradual increase until a characteristic threshold was reached, followed by a reversal to the initial telomere length.

While this model provides interesting insights in context of cancer cells, it does not replicate the conditions of aging or therapeutic intervention. We agree that exploring telomere length-dependent regulation of hTERT in normal aging cells is an important avenue for future research. Investigating TRF2 occupancy on the hTERT promoter in response to telomere length alterations through therapeutic interventions—such as telomestatin or imetelstat (telomerase inhibitors) and 6-thio-2’-deoxyguanosine (telomere damage inducer)—would provide valuable insights and warrants further exploration.

(4) How does the hTERT regulation by TRF2 in a TL-dependent manner affect the ETS binding on hTERT mutant promoter sites?

In our previous study (Sharma et al., 2021, Cell Reports), we have experimentally demonstrated that GABPA and TRF2 do not compete for binding at the mutant hTERT promoter (Figure 4M-R). Silencing GABPA in various mutant hTERT promoter cells did not increase TRF2 binding. While GABPA has been reported to show increased binding at the mutant promoter compared to the wild-type (Bell et al., 2015, Science), no telomere length (TL) sensitivity has been noted yet. In the current manuscript we show that telomere alterations in hTERT mutant cells (that do not form promoter G-quadruplex) does not significantly affect TRF2 occupancy at the promoter, reinforcing our earlier findings that G-quadruplex formation is crucial for TRF2 recruitment. Since TRF2 binding is not affected this would not impact GABPA binding. Therefore change in TL is unlikely to influence ETS binding by GABPA.

(5) Stabilization of the G-quadruplex structures in ST and LT conditions along with the G4 disruption experimentation (demonstrated by the authors) will strengthen the hypothesis.

We agree with the reviewer’s suggestion that stabilizing G-quadruplex (G4) structures in mutant promoter cells under ST and LT conditions would further strengthen our hypothesis. From our ChIP experiments on hTERT promoter mutant cells following G4 stabilization with ligands, as reported in Sharma et al. 2021 (Figure 5G), we observed that TRF2 occupancy was regained in the telomere-length unaltered versions of -124G>A and -146G>A HEK293T Gaussia luciferase cells (referred to as LT cells in the current manuscript).

(6) The telomere length and the telomerase activity are not very consistent (Figure 2A, and S1A, Figure 4B and S3). Please comment.

In this study, we employed both telomerase-dependent and independent methods for telomere elongation.

HT1080 model: Telomere elongation resulted from constitutive overexpression of hTERC and hTERT, leading to a direct correlation with telomerase activity.

HCT116 (p53-null) model: hTERC silencing in ST cells, a known limiting factor for telomerase activity, resulted in significantly lower telomerase activity and a 1.5-fold telomere length difference.

MDAMB231 model: Guanine-rich telomeric repeat (GTR) feeding induced telomere elongation through recombinatorial mechanisms (Wright et al., 1996), leading to significant telomere length gain but no notable change in telomerase activity.

HCT116 Cas9-telomeric sgRNA model: Telomere shortening occurred without modifying telomerase components, resulting in a minor, insignificant increase in telomerase activity (Figure 2A, S1).

Regarding xenograft-derived HT1080 ST and LT cells (Figure 4B, S3), the observed variability in telomere length and telomerase activity may stem from infiltrating mouse cells, which naturally have longer telomeres and higher telomerase activity than human cells. Since in the reported assay tumour masses were not sorted to exclude mouse cells, using species-specific markers or fluorescently labelled HT1080 cells in future experiments would minimize bias. However, even though telomere length and telomerase activity assays cannot differentiate for cross-species differences, mRNA analysis and ChIP experiments performed specifically for hTERT and hTERC mRNA levels, TRF2 occupancy, and H3K27me3 enrichment on hTERT promoter (Figure 4B–E) strongly support our conclusions.

(7) Please comment on the other telomere-associated proteins or regulatory pathways that might contribute to hTERT expression based on telomere length.

The current study provides experimental evidence that TRF2, a well-characterized telomere-binding protein, mediates crosstalk between telomeres and the regulatory region of the hTERT gene in a telomere length-dependent manner. Given the observed link between hTERT expression and telomere length, it is likely that additional telomere-associated proteins and regulatory pathways contribute to this regulation.

The remaining shelterin complex components—POT1, hRap1, TRF1, TIN2, and TPP1—may play crucial roles in this context, as they are integral to telomere maintenance and protection (Stewart J et al., 2012 Mutat Res.). Additionally, several DNA damage response (DDR) proteins, which interact with telomere-binding factors and help preserve telomere integrity, could potentially influence hTERT regulation in a telomere length-dependent manner (Longhese M, 2008 Genes & Development). However, direct interactions or regulatory roles would require further experimental validation. Another group of proteins with potential relevance in this mechanism are the sirtuins, which directly associate with telomeres and are known to positively regulate telomere length, undergoing repression upon telomere shortening (Amano H et al., 2019 Cell Metabolism, Amano H, Sahin E 2019 Molecular & Cellular Oncology). Notably, SIRT1 has been reported to interact with telomerase (Lee SE et al., 2024, Biochem Biophys Res Commun.), while SIRT6 has been implicated in TRF2 degradation (Rizzo et al. 2017) and telomerase activation (Chen J et al. 2021, Aging) . Given their roles in telomere homeostasis, sirtuins may serve as key mediators of telomere length-dependent hTERT regulation.

Based on this suggestion, we have included the above in Discussion.

Reviewer #2 (Public review):

Summary:

Telomeres are key genomic structures linked to everything from aging to cancer. These key structures at the end of chromosomes protect them from degradation during replication and rely on a complex made up of human telomerase RNA gene (hTERC) and human telomerase reverse transcriptase (hTERT). While hTERC is expressed in all cells, the amount of hTERT is tightly controlled. The main hypothesis being tested is whether telomere length itself could regulate the hTERT enzyme. The authors conducted several experiments with different methods to alter telomere length and measured the binding of key regulatory proteins to this gene. It was generally observed that the shortening of telomere length leads to the recruitment of factors that reduce hTERT expression and lengthening of telomeres has the opposite effect. To rule out direct chromatin looping between telomeres and hTERT as driving this effect artificial constructs were designed and inserted a significant distance away and similar results were obtained.

Overall, the claims of telomere length-dependent regulation of hTERT are supported throughout the manuscript.

Strengths:

The paper has several important strengths. Firstly, it uses several methods and cell lines that consistently demonstrate the same directionality of the findings. Secondly, it builds on established findings in the field but still demonstrates how this mechanism is separate from that which has been observed. Specifically, designing and implementing luciferase assays in the CCR5 locus supports that direct chromatin looping isn't necessary to drive this effect with TRF2 binding. Another strength of this paper is that it has been built on a variety of other studies that have established principles such as G4-DNA in the hTERT locus and TRF2 binding to these G4 sites.

Weaknesses:

The largest technical weakness of the paper is that minimal replicates are used for each experiment. I understand that these kinds of experiments are quite costly, and many of the effects are quite large, however, experiments such as the flow cytometry or the IPSC telomere length and activity assays appear to be based on a single sample, and several are based upon two maximum three biological replicates. If samples were added the main effects would likely hold, and many of the assays using GAPDH as a control would result in significant differences between the groups. This unnecessarily weakens the strength of the claims.

We appreciate the reviewer’s recognition of the resource-intensive nature of our experiments, and we are confident in the robustness of the observed results. Due to the project’s timeline constraints and the need for consistency across experiments, we have reported findings based on 3 biological replicates with appropriate statistical analysis.

Regarding the fibroblast-iPSC model, we would like to clarify that we have presented data from two independent biological replicates, each consisting of a fibroblast and its derived iPS cell pair, rather than a single sample. Additionally, the Tel-FACS assays involved analysing at least 10,000 events, ensuring statistical significance in all cases.

Another detail that weakens the confidence in the claims is that throughout the manuscript there are several examples of the control group with zero variance between any of the samples: e.g. Figure 2K, Figure 3N, and Figure 6G. It is my understanding that a delta delta method has been used for calculation (though no exact formula is reported and would assist in understanding). If this is the case, then an average of the control group would be used to calculate that fold change and variance would exist in the group. The only way I could understand those control group samples always set to 1 is if a tube of cells was divided into conditions and therefore normalized to the control group in each case. A clearer description in the figure legend and methods would be required if this is what was done and repeated measures ANOVA and other statistics should accompany this.

The above point has been raised by the reviewer in the 'Recommendations for Authors' section as well. We have addressed it in detail in that section, citing each figure where the reviewer noted a concern regarding the lack of variance. Changes made in the manuscript have also been highlighted there.

We would like to clarify that, throughout the manuscript, fold changes were previously calculated independently for each biological replicate by normalizing treated conditions to their corresponding control (untreated or Day 0) sample within the same replicate. This means that the control group is normalized to 1 individually in each replicate, resulting in an apparent lack of variance in the control when plotted. The normalization was not performed using an averaged control value across replicates. As such, the absence of visible variance in the control group reflects the normalization method rather than a true lack of variability in the underlying data.

In the revised version of the manuscript, we have carefully considered the reviewer’s comments and applied changes wherever appropriate. For example (detailed response in the ‘Recommendations for Authors’ section), in datasets where two distinct stable cell lines are compared (e.g., HT1080 ST/LT and HCT p53-null ST/LT), unpaired statistical analysis is more appropriate. Hence, we have updated these panels accordingly and indicated the statistical methods used in the figure legends and Methods section. However, in experiments where cells were indeed seeded separately and subsequently subjected to experimental conditions—representing paired samples—we have chosen not to make any changes. A clearer description of this procedure has, however, been added to the Methods and figure legends to ensure full transparency.

We believe this approach accurately reflects the experimental design, appropriately addresses the reviewer’s concerns regarding variance and statistical analysis, and ensures clarity and rigor in data reporting.

A final technical weakness of the paper is the data in Figure 5 where the modified hTERT promoter was inserted upstream of the luciferase gene. Specifically, it is unclear why data was not directly compared between the constructs that could and could not form G4s to make this point. For this reason, the large variance in several samples, and minimal biological replicates, this data was the least convincing in the manuscript (though other papers from this laboratory and others support the claim, it is not convincing standalone data).

We appreciate the reviewer's thoughtful feedback on the presentation of the luciferase assay data in Figure 5. The data for the wild-type hTERT promoter (capable of forming G4 structures) was previously reported in Figure 2G-K. To avoid redundancy in data presentation, we initially chose to report the results of the mutated promoter separately. However, we recognize that directly comparing the wild-type and mutated promoter constructs within the same figure would provide clearer context and strengthen the interpretation of the results. In light of this, we have updated Figure 5 in the revised manuscript to include the data for both constructs, ensuring a more comprehensive and informative comparison.

The second largest weakness of the paper is formatting.

When I initially read the paper without a careful reading of the methods, I thought that the authors did not have appropriate controls meaning that if a method is applied to lengthen, there should be one that is not lengthened, and when a method is applied to shorten, one which is not shortened should be analysed as well. In fact, this is what the authors have done with isogenic controls. However, by describing all samples as either telomere short or telomere long, while this simplifies the writing and the colour scheme, it makes it less clear that each experiment is performed relative to an unmodified. I would suggest putting the isogenic control in one colour, the artificially shortened in another, and the artificially lengthened in another.

Similarly, the graphs, in general, should be consistent with labelling. Figure 2 was the most confusing. I would suggest one dotted line with cell lines above it, and then the method of either elongation or shortening below it. I.e. HT1080 above, hTERC overexpression below, MDAMB-231 above guanine terminal repeats below, like was done on the right. Figure 2 readability would also be improved by putting hTERT promoter GAPDH (-ve control) under each graph that uses this (Panel B and Panel C not just Panel C). All information is contained in the manuscript but one must currently flip between figure legends, methods, and figures to understand what was done and this reduces clarity for the reader.

We thank the reviewer again for their thoughtful suggestions regarding figure formatting and colour coding to improve clarity. We fully understand the rationale for proposing separate colours for unmodified, telomere-shortened, and telomere-lengthened groups, as this could make the experimental design more immediately apparent. However, after careful consideration, we believe that implementing this change across all figures may unintentionally reduce clarity in other aspects  (presented in other figures) of the data presentation. This is further explained below.

Specifically, applying three distinct colours throughout would make it harder to visually track key biological trends—such as changes in chromatin occupancy—across different models. For instance, the same colour could represent opposing regulatory patterns in distinct contexts (e.g., upregulation in one model and downregulation in another), which will make these figures difficult to understand. We feel that maintaining a consistent colour scheme based on telomere status—i.e., long telomeres (LT) vs short telomeres (ST)—across figures facilitates better comparison of biological outcomes across different experimental systems.

Nevertheless, to address the reviewer’s concern about clarity in experimental design, we have added more detailed descriptions of the methodology and model systems used, in both the Methods and figure legend sections. These updates aim to make it easier for the reader to follow which groups serve as isogenic controls versus modified samples, without disrupting the consistency of data visualization.

We hope this strikes a balance between improving clarity and preserving the interpretability of the broader biological trends presented in our manuscript.

Please note, we have incorporated the reviewer’s suggestion to indicate details of model generation for HT1080 and MDAMB 231 cell lines in Figure 2. To quote the reviewer,  

“I would suggest one dotted line with cell lines above it, and then the method of either elongation or shortening below it. I.e. HT1080 above, hTERC overexpression below, MDAMB-231 above guanine terminal repeats below, like was done on the right.”

We have also put hTERT promoter GAPDH (-ve control) under each graph and not at the end of Panel C in Figure 2, as suggested by reviewer.

Reviewer #1 (Recommendations for the authors):

(1) Please check for grammatical errors throughout the manuscript.

We have gone through the manuscript thoroughly, checked and corrected it for grammatical errors if and where detected.

(2) Please use both the FACS and qPCR-based assays to check telomere length in all the experiments to strengthen the observations.

We would like to thank the reviewer for this valuable suggestion. We confirm that both FACS- and qPCR-based assays were performed to assess telomere length in our experiments. In the original submission, we chose to present primarily the FACS-based data in the main figures. This decision was based on the inherent differences in the measurement principles of the two methods, which can lead to discrepancies in the reported fold changes. We were concerned that presenting both datasets side by side in the main figures might lead to confusion for readers who are not directly familiar with the nuances of telomere length assays.

However, in light of the reviewer’s suggestion, we have now included the qPCR-based data as Supplementary Figure 1A, and updated the manuscript text and figure legends accordingly to reflect this addition.

(3) Correct the labeling in the legend (Figure 2).

We have corrected legend of Figure 2. Thanks to the reviewer for pointing it out.

(4) In Figure 6B, why TRF WT condition have higher hTERT expression than the UT condition?

We thank the reviewer for noting that the hTERT mRNA levels, as estimated by FISH in Figure 6B, appear slightly higher in TRF2 WT overexpressing HT1080 cells compared to the untransfected (UT) condition. Specifically, the average mean intensity values (a.u.) were 53 for UT and 57 for WT. Although this difference was not statistically significant, we acknowledge the reviewer's observation. Currently, we do not have a clear explanation for this small, non-significant variation.

Importantly, using the same FISH-based method, we observed a significant upregulation of hTERT mRNA levels upon TRF2 R17H overexpression compared to both UT and TRF2 WT conditions, supporting our key conclusions.

Additionally, qRT-PCR analysis of hTERT mRNA levels in cells stably expressing TRF2 WT (induced by doxycycline) consistently showed a significant downregulation compared to the uninduced (equivalent to UT in the microscopy experiments) state. These results were robust and reproducible across three different cell lines, including HT1080. Consistently, TRF2 R17H expression led to significant upregulation of hTERT mRNA levels upon induction.

Together, these complementary findings strengthen the validity of our observations.

(5) In telomere length between ST and LT in Fig. 5B significant? (especially the right panel -146G>A).

We consistently worked with approximately 20–30% telomere shortening in HEK293 cells across all three cell types (WT promoter, -124G>A, and -146G>A), as this range was reproducibly achieved within the experimental timeframe without risking excessive telomere trimming. The reported telomere length differences are based on FACS analysis of more than 10,000 events per condition, providing strong statistical significance. Importantly, while the absolute differences in telomere length may appear modest, their biological impact is evident in the distinct cellular characteristics observed between ST and LT cell pairs.

Reviewer #2 (Recommendations for the authors):

As mentioned above it was somewhat unclear why so many instances of control groups had no variance between them. A more complete reporting of the formulas used to calculate the results, and methods (if samples were divided from a single source into different conditions) would be appreciated.

We thank the reviewer for their valuable and detailed feedback. The instances where the control groups appeared to lack variance were mainly mRNA data (Figure 2D, 3G,3N), luciferase activity (Figure 2K), and in vitro methyltransferase activity (Figure 6G). We shall try to categorically address them all. 

In Figure 2D, for the MDA-MB-231  GTR oligo and HCT116 telomere trimming datasets, the untreated cells were seeded separately and subsequently used to generate the treated conditions within the same experiment. Thus, these two datasets represent paired experimental conditions. Fold changes were calculated independently for each replicate (paired samples), and the fold changes across replicates were plotted. Because the control group serves as a common baseline within each pair and fold changes are normalized individually, minimal variance appears across controls. Given the experimental design, we believe no change is necessary for these panels. However, we have provided additional clarification regarding the calculation formulas and sample handling in the Methods section to avoid any ambiguity.

For the ST/LT versions in HT1080 and HCT p53-null background cells, while each replicate could technically be treated as paired, these could be treated as four distinct stable cell lines. Hence, we agree it would be appropriate to apply unpaired statistical analysis for these datasets. We have updated the plots accordingly and described the statistical methods in detail in the figure legends and Methods section.

Figure 3G and 3N depict the doxycycline-induced cells which follow the design: untreated and dox-treated conditions were seeded from the same batch of cells into separate flasks and treated differently. Hence, these are also paired cases, and fold changes were calculated per replicate before plotting. Therefore, we believe no changes are necessary for these panels. However, we have provided more details regarding sample handling in the Methods section to avoid any ambiguity.

In Figure 2K, previously we had plotted fold change in luciferase activity over short telomere (ST) cells, for each independent biological replicates. However, to address the reviewer’s concern of not showing variance in control group, we have now plotted the luminescence signal (normalised over total protein). We have also updated Figure 5E accordingly, and also included WT promoter data along with the mutant cell line data- as was suggested in public reviewer’s comment.

In Figure 6G, as each replicate of the in vitro methyltransferase activity used different batches of purified protein, there are inherent batch differences that were accounted for by normalizing each replicate internally. Fold changes were then determined for each replicate separately, as previously described. The fold changes across replicates were plotted, and significance between different conditions was tested using two-way ANOVA. To address the reviewer’s comment to show variance in the control, we have now plotted individual replicates.

We believe these revisions, along with the expanded methods clarification, will fully address the reviewer's concerns and accurately reflect the experimental design and statistical analysis applied.

Many times, in the manuscript a / is used to indicate both directions. For example: "Genes distal from telomeres (for instance 60 Mb from the nearest telomere) were activated/repressed in a TL-dependent way"... "Resulting increase/decrease in non-telomeric promoter-bound TRF2 affected gene expression". For readability, either this can be replaced with a directionless word like altered, changed, etc, or the writer can list both directions.

We thank the reviewer for the careful reading and thoughtful suggestions. In the manuscript, we have used the ‘/’ symbol to indicate opposing directions, followed by the word ‘respectively’ to relate these directions to their corresponding outcomes, wherever appropriate. However, as rightly pointed out, certain sentences would benefit from alternative constructions for improved clarity and readability. We have therefore reviewed the manuscript and revised such sentences, making minor modifications wherever necessary, as outlined below.

We found hTERT was transcriptionally altered depending on telomere length (TL).

Notably, another conceptually distinct mechanism of TL-dependent gene regulation was reported which influenced genes spread throughout the genome: expression of genes distal from telomeres (for instance 60 Mb from the nearest telomere) was altered in a TL-dependent way, but without physical telomere looping interactions.

Second, the shortening or elongation of telomeres led to the release or sequestration of telomeric TRF2, respectively, thereby increasing or decreasing the availability of TRF2 at non-telomeric promoters and affecting gene expression.

A non-necessary, but potentially extra convincing experiment to perform would be to use a combination of light-activated, or ligand-activated cas9 telomere trimming and guanine terminal repeat additions in the same cell line. Like the dox experiments, this would show over time how altering telomere length alters the recruitment of heterochromatin factors and hTERT levels. Executing the experiment this way would be more definitive as it does not rely on changing hTERT itself. Authors do already have examples that support their claims.

We thank the reviewer for suggesting this additional experiment (reviewer mentions as non-necessary), which would indeed provide valuable insights into the relationship between telomere length, heterochromatin factor recruitment, and hTERT levels. While we recognize the potential of this approach, due to constraints on resources, we are currently unable to execute this experiment. However, we believe that the existing data presented in the manuscript already supports our conclusions effectively.

eLife Assessment

This study provides valuable insights into the anti-senescence effects of enalapril, identifying pSmad1/5/9 signaling and associated antioxidant pathways as key mediators of its physiological benefits in aged mice. The authors present solid experimental evidence across both in vitro and in vivo systems, demonstrating improved organ function and reduced senescence markers following treatment. Overall, the work supports the repurposing potential of enalapril in aging research and expands understanding of its molecular targets.

Reviewer #1 (Public review):

Summary:

In this study, the authors showed that enalapril was able to reduce cellular senescence and improve health status in aged mice. The authors further showed that phosphorylated Smad1/5/9 was significantly elevated and blocking this pathway attenuated the protection of cells from senescence. When middle-aged mice were treated with enalapril, the physiological performance in several tissues, including memory capacity, renal function and muscle strength, exhibited significant improvement.

Strengths:

The strength of the study lies in the identification of pSMAD1/5/9 pathway as the underlying mechanism mediating the anti-senescence effects of enalapril with comprehensive evaluation both in vitro and in vivo.

Weaknesses:

The major weakness of the study is the in vivo data. Despite the evidence shown in the in vitro study, there is no data to show that blocking the pSmad1/5/9 pathway is able to attenuate the anti-aging effects of enalapril in the mice. In addition, the aging phenotypes mitigation by enalapril is not evidenced by the extension of lifespan. If it is necessary to show that NAC is able to attenuate enalapril effects in the aging mice. In addition, it would be beneficial to test if enalapril is able to achieve similar rescue in a premature aging mouse model.

Comments on revisions:

The revised manuscript provided additional in vivo data that addressed my questions accordingly. I think the authors have done an excellent job in demonstrating that enalapril improved physiological phenotypes in aged mice through pSmad1/5/9 pathway.

Their response to my question regarding the test in HGPS mice was not satisfactory. Premature aging and physiological aging share substantial similarities in their pathways. Given that this is not the focus of current study and the manuscript does not provide data on HGPS mice, I think this does not affect the conclusion of the current study.

Reviewer #2 (Public review):

This manuscript presents an interesting study of enalapril for its potential impact on senescence through the activation of Smad1/5/9 signaling with a focus on antioxidative gene expression. Repurposing enalapril in this context provides a fresh perspective on its effects beyond blood pressure regulation. The authors make a strong case for the importance of Smad1/5/9 in this process, and the inclusion of both in vitro and in vivo models adds value to the findings. Below, I have a few comments and suggestions which may help improve the manuscript.

A major finding in the study is that phosphorylated Smad1/5/9 mediates the effects of enalapril. However, the manuscript focused on the Smad pathway relatively abruptly, and the rationale behind targeting this specific pathway is not fully explained. What makes Smad1/5/9 particularly relevant to the context of this study?

Furthermore, their finding that activation of Smad1/5/9 leads to a reduction of senescence appears somewhat contradictory to the established literature on Smad1/5/9 in senescence. For instance, studies have shown that BMP4-induced senescence involves activation of Smad1/5/8 (Smad1/5/9), leading to the upregulation of senescence markers like p16 and p21 (JBC, 2009, 284, 12153). Similarly, phosphorylated Smad1/5/8 has been shown to promote and maintain senescence in Ras-activated cells (PLOS Genetics, 2011, 7, e1002359). Could the authors provide more detailed mechanistic insights into why enalapril seems to reverse the typical pro-senescent role of Smad1/5/9 in their study?

While the authors showed that enalapril increases pSmad1/5/9 phosphorylation, what are the expression levels of other key and related factors like Smad4, pSmad2, pSmad3, BMP2, and BMP4 in both senescent and non-senescent cells? These data will help clarify the broader signaling effects.

They used BMP receptor inhibitor LDN193189 to pharmacologically inhibit BMP signaling, but it would be more convincing to also include genetic validation (e.g., knockdown or knockout of BMP2 or BMP4). This will help confirm that the observed effects are truly due to BMP-Smad signaling and not off-target effects of the pharmacological inhibitor LDN.

I don't see the results on the changes in senescence markers p16 and p21 in the mouse models treated with enalapril. Similarly, the effects of enalapril treatment on some key SASP factors, such as TNF-α, MCP-1, IL-1β, and IL-1α, are missing, particularly in serum and tissues. These are important data to evaluate the effect of enalapril on senescence.

Given that enalapril is primarily known as an antihypertensive, it would be helpful to include data on how it affects blood pressure in the aged mouse models, such as systolic and diastolic blood pressure. This will clarify whether the observed effects are independent of or influenced by changes in blood pressure.

Author response:

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

Reviewer #1 (Public review):

Summary:

In this study, the authors showed that enalapril was able to reduce cellular senescence and improve health status in aged mice. The authors further showed that phosphorylated Smad1/5/9 was significantly elevated and blocking this pathway attenuated the protection of cells from senescence. When middle-aged mice were treated with enalapril, the physiological performance in several tissues, including memory capacity, renal function, and muscle strength, exhibited significant improvement.

Strengths:

The strength of the study lies in the identification of the pSMAD1/5/9 pathway as the underlying mechanism mediating the anti-senescence effects of enalapril with comprehensive evaluation both in vitro and in vivo.

Thank you for your patient reading and great efforts to advance our research! Your comments are shown in bold font below, and specific concerns have been numbered. Our point-by-point answers are provided in standard blue font, with all modifications and additions to the MS highlighted in red text.

Weaknesses:

(1) The major weakness of the study is the in vivo data. Despite the evidence shown in the in vitro study, there is no data to show that blocking the pSmad1/5/9 pathway is able to attenuate the anti-aging effects of enalapril in the mice. In addition, the aging phenotypes mitigation by enalapril is not evidenced by the extension of lifespan.

Many thanks for your careful reading and valuable comments! We fully agree with this comment. In accordance with your suggestion, we administered LDN193189 to investigate its suppressive effects on pSmad1/5/9 signaling in vivo. Notably, pharmacological inhibition of pSmad1/5/9 resulted in upregulation of enalapril-suppressed SASP factors, while conversely leading to marked decrease of downstream antioxidant genes expression across multiple organ systems (Revised Fig. S7). These analyses and corresponding sentences have been added in the Result section of the revised MS (Revised Fig.S7, Lines 222–223, 444–448).

Additionally, aging-related behavioral phenotypes were also examined following pSmad1/5/9 inhibition, including decreased muscle strength and endurance, impaired spatial memory and increased anxiety behaviors (Revised Fig. S8). These analyses and corresponding sentences have been added in the Result section of the revised MS (Revised Fig.S8, Lines 476–480). Collectively, these findings demonstrate that the anti-aging effects of enalapril in mice are mediated through the pSmad1/5/9 pathway.

In this study, we focused exclusively on assessing the improvement in the health status of aged mice, which indicates that enalapril can extend the healthspan of aged mice. While we agree that lifespan extension is an important indicator of anti-aging potential, recent studies have emphasized that healthspan, rather than lifespan alone, provides a more relevant and translational measure of aging interventions, particularly in the context of chronic disease and quality of life in aged individuals (Kennedy et al., 2014; Lopez-Otin et al., 2023). Moreover, given the strong influence of genetic background, environmental factors and stochastic events on lifespan, focusing on functional rejuvenation and delayed onset of aging-related pathologies may offer a more practical and mechanistically informative approach. Our study aims to elucidate how enalapril enhances healthy phenotypes in aged mice, however, we acknowledge the critical need for direct lifespan evaluation and intend to address this limitation in subsequent research. We sincerely hope that these explanations address your concerns.

(2) If it is necessary to show that NAC is able to attenuate enalapril effects in the aging mice. In addition, it would be beneficial to test if enalapril is able to achieve similar rescue in a premature aging mouse model.

Thanks for your suggestion. We apologize for any confusion that may have arisen due to the wording in the original manuscript. N-acetylcysteine (NAC) is widely reported as an antioxidant that scavenges reactive oxygen species (ROS) (Huang et al., 2020; Zafarullah et al., 2003). In our study, enalapril was also observed to reduce ROS levels. Therefore, NAC is unlikely to antagonize the effects of enalapril in this context, as both compounds act in a similar direction with respect to oxidative stress mitigation. To avoid potential misunderstanding, we have carefully reviewed the relevant statements in the MS and revised the text to clarify this point.

We sincerely appreciate this valuable suggestion to evaluate enalapril in a premature aging mouse model; however, the premature aging mouse models represent a pathological form of aging, whereas the naturally aged mouse models used in our study reflect physiological aging processes. While we observed beneficial effects of enalapril in naturally aged mice, these effects may not necessarily extend to premature aging models due to fundamental differences in the underlying mechanisms and progression of aging. Natural aging is characterized by the gradual accumulation of cellular damage, driven by multifactorial processes such as inflammaging and mitochondrial dysfunction. In this context, enalapril appears effective, in part by modulating SASP factors and reducing oxidative stress through the BMP-Smad signaling axis (Revised Fig. 4, 5) (Lopez-Otin et al., 2023). In contrast, premature aging models are driven by distinct mechanisms like nuclear lamina defects, which may not respond similarly to BMP-Smad axis. Moreover, genetic background, strain variability, and specific model characteristics can significantly influence treatment outcomes (Mitchell et al., 2016). For instance, rapamycin extends lifespan in wild-type mice but shows limited effects on aging, underscoring the challenge of extrapolating findings across distinct aging models (Neff et al., 2013). We sincerely hope that these explanations address your concerns. Thank you again for your great efforts in advancing our research!

Reviewer #2 (Public review):

This manuscript presents an interesting study of enalapril for its potential impact on senescence through the activation of Smad1/5/9 signaling with a focus on antioxidative gene expression. Repurposing enalapril in this context provides a fresh perspective on its effects beyond blood pressure regulation. The authors make a strong case for the importance of Smad1/5/9 in this process, and the inclusion of both in vitro and in vivo models adds value to the findings. Below, I have a few comments and suggestions which may help improve the manuscript.

We appreciate your great efforts in advancing our research! Your comments are shown in bold font below, and specific concerns have been numbered. Our point-by-point answers are provided in standard blue font, with all modifications and additions to the MS highlighted in red text.

(1) A major finding in the study is that phosphorylated Smad1/5/9 mediates the effects of enalapril. However, the manuscript focused on the Smad pathway relatively abruptly, and the rationale behind targeting this specific pathway is not fully explained. What makes Smad1/5/9 particularly relevant to the context of this study?

Thank you for your informative guidance, and we regret for the unclear description. As stated in the MS, after we found that enalapril could improve the cellular senescence phenotype, we screened and examined key targets in important aging-related signaling pathways, such as AKT, mTOR, ERK, Smad2/3 and Smad1/5/9 (Revised Fig. S2A, Revised Fig. 2A). We found that only the phosphorylation levels of Smad1/5/9 significantly increased after enalapril treatment. Therefore, the subsequent focus of this study is on pSmad1/5/9. We sincerely hope that these explanations address your concerns.

(2) Furthermore, their finding that activation of Smad1/5/9 leads to a reduction of senescence appears somewhat contradictory to the established literature on Smad1/5/9 in senescence. For instance, studies have shown that BMP4-induced senescence involves the activation of Smad1/5/8 (Smad1/5/9), leading to the upregulation of senescence markers like p16 and p21 (JBC, 2009, 284, 12153). Similarly, phosphorylated Smad1/5/8 has been shown to promote and maintain senescence in Ras-activated cells (PLOS Genetics, 2011, 7, e1002359). Could the authors provide more detailed mechanistic insights into why enalapril seems to reverse the typical pro-senescent role of Smad1/5/9 in their study?

Many thanks for your helpful comments! The downstream regulatory network of BMP-pSmad1/5/9 is highly complex. The BMP-SMAD-ID axis has been mentioned in many studies, and its downstream signaling inhibits the expression of p16 and p21 (Hayashi et al., 2016; Ying et al., 2003). Additionally, studies have also found that the Smad1-Stat1-P21 axis inhibits osteoblast senescence (Xu et al., 2022). In our study, enalapril was found to increase the expression of ID1, which is a classic downstream target of pSmad1/5/9 (Genander et al., 2014). Therefore, pSmad1/5/9 inhibits cellular senescence markers such as p16, p21 and SASP through ID1, thereby promoting cell proliferation (Revised Fig. 3). Furthermore, we also found that pSmad1/5/9 increases the expression of antioxidant genes and reduces ROS levels, exerting antioxidant effects (Revised Fig. 4). Together, ID1 and antioxidant genes enable pSmad1/5/9 to exert its anti-senescence effects. We sincerely hope that these explanations address your concerns.

(3) While the authors showed that enalapril increases pSmad1/5/9 phosphorylation, what are the expression levels of other key and related factors like Smad4, pSmad2, pSmad3, BMP2, and BMP4 in both senescent and non-senescent cells? These data will help clarify the broader signaling effects.

Thanks for your insightful suggestions. We observed an increase in pSmad1/5/9 and Smad4 expression, while the levels of pSmad2 and pSmad3 remained unchanged after enalapril treatment (Revised Fig. 2A). Consistently, we found that the levels of pSmad1/5/9 and Smad4 were markedly reduced in senescent cells, aligning with the upregulation of these proteins by enalapril (Revised Fig. S2B). In contrast, pSmad2 and pSmad3 showed a slight increase during senescence, while BMP2 and BMP4 were slightly decreased, though these changes were not statistically significant (Revised Fig. S2B). These findings suggest that enalapril primarily exerts its effects by enhancing pSmad1/5/9 and Smad4 levels, thereby regulating downstream target genes and contributing to the restoration of a more youthful cellular state. These analyses and corresponding sentences have been added in the Result section of the revised MS (Revised Fig.S2B, Lines 303–306, 311–313).

(4) They used BMP receptor inhibitor LDN193189 to pharmacologically inhibit BMP signaling, but it would be more convincing to also include genetic validation (e.g., knockdown or knockout of BMP2 or BMP4). This will help confirm that the observed effects are truly due to BMP-Smad signaling and not off-target effects of the pharmacological inhibitor LDN.

Many thanks for your careful reading and valuable comments! We used shRNA to knockdown the BMP receptor BMPR1A, which led to a reduction in Smad1/5/9 phosphorylation (Revised Fig. S4D, E). This was accompanied by senescence-associated phenotypes, including increased expression of p16 and SA-β-gal and decreased Ki67 staining (Revised Fig. S4F, G). Notably, the addition of enalapril failed to reverse these senescence phenotypes under BMPR1A knockdown conditions, mirroring the results observed with the BMP receptor inhibitor LDN193189 (Revised Fig. S4F, G, Revised Fig. 2F, G). Furthermore, knockdown of BMPR1A also resulted in a marked decrease in the expression of downstream targets, such as ID1 and antioxidative genes (Revised Fig. S4D). These findings strongly support the notion that enalapril exerts its anti-senescence effects through BMP-Smad signaling. These analyses and corresponding sentences have been added in the Result section of the revised MS (Revised Fig.S4D–G, Lines 323–329, 335–337, 348–351, 416–418).

(5) I don't see the results on the changes in senescence markers p16 and p21 in the mouse models treated with enalapril. Similarly, the effects of enalapril treatment on some key SASP factors, such as TNF-α, MCP-1, IL-1β, and IL-1α, are missing, particularly in serum and tissues. These are important data to evaluate the effect of enalapril on senescence.

Thanks for your comments. As for the markers p16 and p21, we observed no change in p16, while the changes in p21 varied across different organs and tissues. Nevertheless, behavioral experiments and physiological and biochemical indicators at the individual level consistently demonstrated the significant anti-aging effects of enalapril (Revised Fig. 6).

We also examined the changes in SASP factors in the serum of mice after enalapril treatment. Notably, SASP factors such as CCL (MCP), CXCL and TNFRS11B showed significant decreases (Revised Fig. 5C). The expression changes of SASP factors varied across different organs. In the liver, kidneys and spleen, the expression of IL1a and IL1b decreased, while TNFRS11B expression decreased in both the liver and muscles (Revised Fig. 5B). Additionally, CCL (MCP) levels decreased in all organs (Revised Fig. 5B). We sincerely hope that these explanations address your concerns.

(6) Given that enalapril is primarily known as an antihypertensive, it would be helpful to include data on how it affects blood pressure in the aged mouse models, such as systolic and diastolic blood pressure. This will clarify whether the observed effects are independent of or influenced by changes in blood pressure.

Thanks for your comments. While enalapril is primarily recognized for its antihypertensive properties, in our experimental setting involving aged, normotensive mice, we did not observe notable changes in systolic or diastolic blood pressure following enalapril administration. This observation aligns with previous reports indicating that enalapril does not significantly affect blood pressure in similar non-hypertensive aging models (Keller et al., 2019). Based on these findings, we cautiously interpret that the beneficial effects of enalapril observed in our study are unlikely to be driven by changes in blood pressure. We sincerely hope that these explanations address your concerns. Again, thank you for the constructive comments to advance the understanding of our work!

Reviewer #1 (Recommendations for the authors):

This is an interesting study that reveals enalapril is able to elevate the pSmad1/5/9 pathway to reduce ROS and inflammation to improve the health status in vitro and in vivo. While the pathway is clearly shown in cells to be involved in the enalarpril-mediated mitigation of aging, little was done to demonstrate this pathway is responsible for the in vivo effects in the physiological improvements. This can be done by ROS-reduction chemicals such as NAC and also the use of BMP receptor inhibitor LDN193189 (LDN). It is critical to show the lifespan extension in enalapril-treated animals given that the significantly improved physiological functions.

Thanks very much for your constructive recommendations. This part has already been addressed in our response to the public review.

Reviewer #2 (Recommendations for the authors):

The term "anti-aging" appears frequently throughout the manuscript, including in the title. However, the study doesn't directly address lifespan or a comprehensive range of aging symptoms, which are also difficult to define and measure. Many of the observed effects appeared to be driven by senescence. To be more accurate, I recommend avoiding terms like "anti-aging" and "mitigates aging", and instead replacing them with more specific phrases such as "anti-senescence", "senescence reduction/suppression", or "mitigates age-related symptoms" to better reflect the scope of the study and avoid overstating the findings.

Thanks very much for your constructive recommendations. In accordance with your suggestion, we have revised all uses of the term “aging” in the MS. To facilitate review, all changes have been clearly marked in red text.

Please provide detailed information on the antibodies used, particularly those targeting pSmad1/5/9 and other Smads.

Thanks for your helpful comment. In response, we have now provided detailed information regarding the antibodies used in this study in Revised Table S4 (Revised MS, Page 120–121).

eLife Assessment

This valuable study provides solid evidence that MgdE, a conserved mycobacterial nucleomodulin, downregulates inflammatory gene transcription by interacting with the histone methyltransferase COMPASS complex and altering histone H3 lysine methylation. There are areas where the evidence could be strengthened, for example, GFP immunoblotting and examining MgdE localization during infection. To enhance impact, the authors could consider Mycobacterium tuberculosis infection experiments and/or reworking the manuscript to emphasize general relevance to microbiologists and cell biologists.

Reviewer #1 (Public review):

Summary:

This fundamental study identifies a new mechanism that involves a mycobacterial nucleomodulin manipulation of the host histone methyltransferase COMPASS complex to promote infection. Although other intracellular pathogens are known to manipulate histone methylation, this is the first report demonstrating the specific targeting of the COMPASS complex by a pathogen. The rigorous experimental design using state-of-the art bioinformatic analysis, protein modeling, molecular and cellular interaction, and functional approaches, culminating with in vivo infection modeling, provides convincing, unequivocal evidence that supports the authors' claims. This work will be of particular interest to cellular microbiologists working on microbial virulence mechanisms and effectors, specifically nucleomodulins, and cell/cancer biologists that examine COMPASS dysfunction in cancer biology.

Strengths:

(1) The strengths of this study include the rigorous and comprehensive experimental design that involved numerous state-of-the-art approaches to identify potential nucleomodulins, define molecular nucleomodulin-host interactions, cellular nucleomodulin localization, intracellular survival, and inflammatory gene transcriptional responses, and confirmation of the inflammatory and infection phenotype in a small animal model.

(2) The use of bioinformatic, cellular, and in vivo modeling that are consistent and support the overall conclusions is a strength of the study. In addition, the rigorous experimental design and data analysis, including the supplemental data provided, further strengthen the evidence supporting the conclusions.

Weaknesses:

(1) This work could be stronger if the MgdE-COMPASS subunit interactions that negatively impact COMPASS complex function were better defined. Since the COMPASS complex consists of many enzymes, examining the functional impact on each of the components would be interesting.

(2) Examining the impact of WDR5 inhibitors on histone methylation, gene transcription, and mycobacterial infection could provide additional rigor and provide useful information related to the mechanisms and specific role of WDR5 inhibition on mycobacterial infection.

(3) The interaction between MgdE and COMPASS complex subunit ASH2L is relatively undefined, and studies to understand the relationship between WDR5 and ASH2L in COMPASS complex function during infection could provide interesting molecular details that are undefined in this study.

(4) The AlphaFold prediction results for all the nuclear proteins examined could be useful. Since the interaction predictions with COMPASS subunits range from 0.77 for WDR5 and 0.47 for ASH2L, it is not clear how the focus on COMPASS complex over other nuclear proteins was determined.

Reviewer #2 (Public review):

Summary:

The manuscript by Chen et al addresses an important aspect of pathogenesis for mycobacterial pathogens, seeking to understand how bacterial effector proteins disrupt the host immune response. To address this question, the authors sought to identify bacterial effectors from M. tuberculosis (Mtb) that localize to the host nucleus and disrupt host gene expression as a means of impairing host immune function.

Strengths:

The researchers conducted a rigorous bioinformatic analysis to identify secreted effectors containing mammalian nuclear localization signal (NLS) sequences, which formed the basis of quantitative microscopy analysis to identify bacterial proteins that had nuclear targeting within human cells. The study used two complementary methods to detect protein-protein interaction: yeast two-hybrid assays and reciprocal immunoprecipitation (IP). The combined use of these techniques provides strong evidence of interactions between MgdE and SET1 components and suggests that the interactions are, in fact, direct. The authors also carried out a rigorous analysis of changes in gene expression in macrophages infected with the mgdE mutant BCG. They found strong and consistent effects on key cytokines such as IL6 and CSF1/2, suggesting that nuclear-localized MgdE does, in fact, alter gene expression during infection of macrophages.

Weaknesses:

There are some drawbacks in this study that limit the application of the findings to M. tuberculosis (Mtb) pathogenesis. The first concern is that much of the study relies on ectopic overexpression of proteins either in transfected non-immune cells (HEK293T) or in yeast, using 2-hybrid approaches. Some of their data in 293T cells is hard to interpret, and it is unclear if the protein-protein interactions they identify occur during natural infection with mycobacteria. The second major concern is that pathogenesis is studied using the BCG vaccine strain rather than virulent Mtb. However, overall, the key findings of the paper - that MgdE interacts with SET1 and alters gene expression are well-supported.

Reviewer #3 (Public review):

In this study, Chen L et al. systematically analyzed the mycobacterial nucleomodulins and identified MgdE as a key nucleomodulin in pathogenesis. They found that MgdE enters into host cell nucleus through two nuclear localization signals, KRIR108-111 and RLRRPR300-305, and then interacts with COMPASS complex subunits ASH2L and WDR5 to suppress H3K4 methylation-mediated transcription of pro-inflammatory cytokines, thereby promoting mycobacterial survival. This study is potentially interesting, but there are several critical issues that need to be addressed to support the conclusions of the manuscript.

(1) Figure 2: The study identified MgdE as a nucleomodulin in mycobacteria and demonstrated its nuclear translocation via dual NLS motifs. The authors examined MgdE nuclear translocation through ectopic expression in HEK293T cells, which may not reflect physiological conditions. Nuclear-cytoplasmic fractionation experiments under mycobacterial infection should be performed to determine MgdE localization.

(2) Figure 2F: The authors detected MgdE-EGFP using an anti-GFP antibody, but EGFP as a control was not detected in its lane. The authors should address this technical issue.

(3) Figure 3C-3H: The data showing that the expression of all detected genes in 24 h is comparable to that in 4 h (but not 0 h) during WT BCG infection is beyond comprehension. The issue is also present in Figure 7C, Figure 7D, and Figure S7. Moreover, since Il6, Il1β (pro-inflammatory), and Il10 (anti-inflammatory) were all upregulated upon MgdE deletion, how do the authors explain the phenomenon that MgdE deletion simultaneously enhanced these gene expressions?

(4) Figure 5: The authors confirmed the interactions between MgdE and WDR5/ASH2L. How does the interaction between MgdE and WDR5 inhibit COMPASS-dependent methyltransferase activity? Additionally, the precise MgdE-ASH2L binding interface and its functional impact on COMPASS assembly or activity require clarification.

(5) Figure 6: The authors proposed that the MgdE-regulated COMPASS complex-H3K4me3 axis suppresses pro-inflammatory responses, but the presented data do not sufficiently support this claim. H3K4me3 inhibitor should be employed to verify cytokine production during infection.

(6) There appears to be a discrepancy between the results shown in Figure S7 and its accompanying legend. The data related to inflammatory responses seem to be missing, and the data on bacterial colonization are confusing (bacterial DNA expression or CFU assay?).

(7) Line 112-116: Please provide the original experimental data demonstrating nuclear localization of the 56 proteins harboring putative NLS motifs.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

This fundamental study identifies a new mechanism that involves a mycobacterial nucleomodulin manipulation of the host histone methyltransferase COMPASS complex to promote infection. Although other intracellular pathogens are known to manipulate histone methylation, this is the first report demonstrating the specific targeting of the COMPASS complex by a pathogen. The rigorous experimental design using state-of-the art bioinformatic analysis, protein modeling, molecular and cellular interaction, and functional approaches, culminating with in vivo infection modeling, provides convincing, unequivocal evidence that supports the authors' claims. This work will be of particular interest to cellular microbiologists working on microbial virulence mechanisms and effectors, specifically nucleomodulins, and cell/cancer biologists that examine COMPASS dysfunction in cancer biology. 

Strengths: 

(1) The strengths of this study include the rigorous and comprehensive experimental design that involved numerous state-of-the-art approaches to identify potential nucleomodulins, define molecular nucleomodulin-host interactions, cellular nucleomodulin localization, intracellular survival, and inflammatory gene transcriptional responses, and confirmation of the inflammatory and infection phenotype in a small animal model. 

(2) The use of bioinformatic, cellular, and in vivo modeling that are consistent and support the overall conclusions is a strength of the study. In addition, the rigorous experimental design and data analysis, including the supplemental data provided, further strengthen the evidence supporting the conclusions. 

Weaknesses: 

(1) This work could be stronger if the MgdE-COMPASS subunit interactions that negatively impact COMPASS complex function were better defined. Since the COMPASS complex consists of many enzymes, examining the functional impact on each of the components would be interesting. 

We thank the reviewer for this insightful comment. A biochemistry assays could be helpful to interpret the functional impact on each of the components by MgdE interaction. However, the purification of the COMPASS complex could be a hard task itself due to the complexity of the full COMPASS complex along with its dynamic structural properties and limited solubility. 

(2) Examining the impact of WDR5 inhibitors on histone methylation, gene transcription, and mycobacterial infection could provide additional rigor and provide useful information related to the mechanisms and specific role of WDR5 inhibition on mycobacterial infection. 

We thank the reviewer for the comment. A previous study showed that WIN-site inhibitors, such as compound C6, can displace WDR5 from chromatin, leading to a reduction in global H3K4me3 levels and suppression of immune-related gene expression (Hung et al., Nucleic Acids Res, 2018; Bryan et al., Nucleic Acids Res, 2020). These results closely mirror the functional effects we observed for MgdE, suggesting that MgdE may act as a functional mimic of WDR5 inhibition. This supports our proposed model in which MgdE disrupts COMPASS activity by targeting WDR5, thereby dampening host pro-inflammatory responses.

(3) The interaction between MgdE and COMPASS complex subunit ASH2L is relatively undefined, and studies to understand the relationship between WDR5 and ASH2L in COMPASS complex function during infection could provide interesting molecular details that are undefined in this study. 

We thank the reviewer for the comment. In this study, we constructed single and multiple point mutants of MgdE at residues S⁸⁰, D²⁴⁴, and H²⁴⁷ to identify key amino acids involved in its interaction with ASH2L (Figure 5A and B; Figure S5). However these mutations did not interrupt the interaction with MgdE, suggesting that more residues are involved in the interaction.

ASH2L and WDR5 function cooperatively within the WRAD module to stabilize the SET domain and promote H3K4 methyltransferase activity with physiological conditions (Couture and Skiniotis, Epigenetics, 2013; Qu et al., Cell, 2018; Rahman et al., Proc Natl Acad Sci U S A, 2022). ASH2L interacts with RbBP5 via its SPRY domain, whereas WDR5 bridges MLL1 and RbBP5 through the WIN and WBM motifs (Chen at al., Cell Res, 2012; Park et al., Nat Commun, 2019). The interaction status between ASH2L and WDR5 during mycobacterial infection could not be determined in our current study. 

(4) The AlphaFold prediction results for all the nuclear proteins examined could be useful. Since the interaction predictions with COMPASS subunits range from 0.77 for WDR5 and 0.47 for ASH2L, it is not clear how the focus on COMPASS complex over other nuclear proteins was determined.  

We thank the reviewer for the comment. We employed AlphaFold to predict the interactions between MgdE and the major nuclear proteins. This screen identified several subunits of the SET1/COMPASS complex as high-confidence candidates for interaction with MgdE (Supplementary Figure 4A). This result is consistent with a proteomic study by Penn et al. which reported potential interactions between MgdE and components of the human SET1/COMPASS complex based on affinity purification-mass spectrometry analysis (Penn et al., Mol Cell, 2018).

Reviewer #2 (Public review): 

Summary: 

The manuscript by Chen et al addresses an important aspect of pathogenesis for mycobacterial pathogens, seeking to understand how bacterial effector proteins disrupt the host immune response. To address this question, the authors sought to identify bacterial effectors from M. tuberculosis (Mtb) that localize to the host nucleus and disrupt host gene expression as a means of impairing host immune function. 

Strengths: 

The researchers conducted a rigorous bioinformatic analysis to identify secreted effectors containing mammalian nuclear localization signal (NLS) sequences, which formed the basis of quantitative microscopy analysis to identify bacterial proteins that had nuclear targeting within human cells. The study used two complementary methods to detect protein-protein interaction: yeast two-hybrid assays and reciprocal immunoprecipitation (IP). The combined use of these techniques provides strong evidence of interactions between MgdE and SET1 components and suggests that the interactions are, in fact, direct. The authors also carried out a rigorous analysis of changes in gene expression in macrophages infected with the mgdE mutant BCG. They found strong and consistent effects on key cytokines such as IL6 and CSF1/2, suggesting that nuclear-localized MgdE does, in fact, alter gene expression during infection of macrophages. 

Weaknesses: 

There are some drawbacks in this study that limit the application of the findings to M. tuberculosis (Mtb) pathogenesis. The first concern is that much of the study relies on ectopic overexpression of proteins either in transfected non-immune cells (HEK293T) or in yeast, using 2-hybrid approaches. Some of their data in 293T cells is hard to interpret, and it is unclear if the protein-protein interactions they identify occur during natural infection with mycobacteria. The second major concern is that pathogenesis is studied using the BCG vaccine strain rather than virulent Mtb. However, overall, the key findings of the paper - that MgdE interacts with SET1 and alters gene expression are well-supported. 

We thank the reviewer for the comment. We agree that the ectopic overexpression could not completely reflect a natural status, although these approaches were adopted in many similar experiments (Drerup et al., Molecular plant, 2013; Chen et al., Cell host & microbe, 2018; Ge et al., Autophagy, 2021). Further, the MgdE localization experiment using Mtb infected macrophages will be performed to increase the evidence in the natural infection.

We agree with the reviewer that BCG strain could not fully recapitulate the pathogenicity or immunological complexity of M. tuberculosis infection.  We employed BCG as a biosafe surrogate model since it was acceptable in many related studies (Wang et al., Nat Immunol, 2025; Wang et al., Nat Commun, 2017; Péan et al., Nat Commun, 2017; Li et al., J Biol Chem, 2020). 

Reviewer #3 (Public review): 

In this study, Chen L et al. systematically analyzed the mycobacterial nucleomodulins and identified MgdE as a key nucleomodulin in pathogenesis. They found that MgdE enters into host cell nucleus through two nuclear localization signals, KRIR^108-111 and RLRRPR^300-305, and then interacts with COMPASS complex subunits ASH2L and WDR5 to suppress H3K4 methylation-mediated transcription of pro-inflammatory cytokines, thereby promoting mycobacterial survival. This study is potentially interesting, but there are several critical issues that need to be addressed to support the conclusions of the manuscript.

(1) Figure 2: The study identified MgdE as a nucleomodulin in mycobacteria and demonstrated its nuclear translocation via dual NLS motifs. The authors examined MgdE nuclear translocation through ectopic expression in HEK293T cells, which may not reflect physiological conditions. Nuclear-cytoplasmic fractionation experiments under mycobacterial infection should be performed to determine MgdE localization. 

We thank the reviewer for the comment. The MgdE localization experiment using Mtb infected macrophages will be performed.

(2) Figure 2F: The authors detected MgdE-EGFP using an anti-GFP antibody, but EGFP as a control was

We thank the reviewer for pointing this out. The new uncropped blots containing the EGFP band will be provided in Supplementary Information.

(3) Figure 3C-3H: The data showing that the expression of all detected genes in 24 h is comparable to that in 4 h (but not 0 h) during WT BCG infection is beyond comprehension. The issue is also present in Figure 7C, Figure 7D, and Figure S7. Moreover, since Il6, Il1β (proinflammatory), and Il10 (anti-inflammatory) were all upregulated upon MgdE deletion, how do the authors explain the phenomenon that MgdE deletion simultaneously enhanced these gene expressions? 

We thank the reviewer for the comment. A relative quantification method was used in our qPCR experiments to normalize the WT expression levels in Figure 3C–3H, Figure 7C, 7D, and Figure S7. 

The concurrent induction of both types of cytokines likely represents a dynamic host strategy to fine-tune immune responses during infection. This interpretation is supported by previous studies (Podleśny-Drabiniok et al., Cell Rep, 2025; Cicchese et al., Immunological Reviews, 2018).

(4) Figure 5: The authors confirmed the interactions between MgdE and WDR5/ASH2L. How does the interaction between MgdE and WDR5 inhibit COMPASS-dependent methyltransferase activity? Additionally, the precise MgdE-ASH2L binding interface and its functional impact on COMPASS assembly or activity require clarification. 

We thank the reviewer for this insightful comment. We cautiously speculate that the MgdE interaction inhibits COMPASS-dependent methyltransferase activity by interfering with the integrity and stability of the COMPASS complex. Accordingly, we have incorporated the following discussion into the revised manuscript (Lines 298-310):

“The COMPASS complex facilitates H3K4 methylation through a conserved assembly mechanism involving multiple core subunits. WDR5, a central scaffolding component, interacts with RbBP5 and ASH2L to promote complex assembly and enzymatic activity (Qu et al., 2018; Wysocka et al., 2005). It also recognizes the WIN motif of methyltransferases such as MLL1, thereby anchoring them to the complex and stabilizing the ASH2L-RbBP5 dimer (Hsu et al., Cell, 2018). ASH2L further contributes to COMPASS activation by interacting with both RbBP5 and DPY30 and by stabilizing the SET domain, which is essential for efficient substrate recognition and catalysis (Qu et al., Cell, 2018; Park et al., Nat Commun, 2019). Our work shows that MgdE binds both WDR5 and ASH2L and inhibits the methyltransferase activity of the COMPASS complex. Site-directed mutagenesis revealed that residues D²²⁴ and H²⁴⁷ of MgdE are critical for WDR5 binding, as the double mutant MgdE-D²²⁴A/H²⁴⁷ A fails to interact with WDR5 and shows diminished suppression of H3K4me3 levels (Figure 5D).”

Regarding the precise MgdE-ASH2L binding interface, we attempted to identify the key interaction site by introducing point mutations into ASH2L. However, these mutations did not disrupt the interaction (Figure 5A and B; Figure S5), suggesting that more residues are involved in the interaction.

(5) Figure 6: The authors proposed that the MgdE-regulated COMPASS complex-H3K4me3 axis suppresses pro-inflammatory responses, but the presented data do not sufficiently support this claim. H3K4me3 inhibitor should be employed to verify cytokine production during infection. 

We thank the reviewer for the comment. We have now revised the description in lines 824825 “MgdE may suppresses COMPASS complex-mediated inflammatory responses by inhibiting H3K4 methylation” and in lines 219-220 "MgdE suppresses host inflammatory responses probably by inhibition of COMPASS complex-mediated H3K4 methylation." 

(6) There appears to be a discrepancy between the results shown in Figure S7 and its accompanying legend. The data related to inflammatory responses seem to be missing, and the data on bacterial colonization are confusing (bacterial DNA expression or CFU assay?). 

We thank the reviewer for the comment. Figure S7 specifically addresses the effect of MgdE on bacterial colonization in the spleens of infected mice, which was assessed by quantitative PCR rather than by CFU assay. 

We have now revised the legend of Figure S7 as below (Lines 934-938):

“MgdE facilitates bacterial colonization in the spleens of infected mice. Bacterial colonization was assessed in splenic homogenates from infected mice (as described in Figure 7A) by quantifying bacterial DNA using quantitative PCR at 2, 14, 21, 28, and 56 days post-infection.”

(7) Line 112-116: Please provide the original experimental data demonstrating nuclear localization of the 56 proteins harboring putative NLS motifs. 

We thank the reviewer for the comment. We will provide this data in the new Supplementary Table 2.

eLife Assessment

This study addresses an important question in sensory neuroscience: how the olfactory system distinguishes decreases in stimulus intensity from decreases in neural responses due to adaptation. Based on a combination of electrophysiological and behavioral analyses, solid evidence establishes that neural coding changes differently between intensity reductions and adaptation, with intensity changes altering which neurons are activated while adaptation preserves the active ensemble but reduces response magnitude. Intriguingly, behavioral responses tend to increase as the neural responses decrease, suggesting that core features of the odor response persist through adaptation. While the experimental results are convincing overall, the conclusions will be strengthened by future work recording behavior and neural dynamics in the same animals.

Reviewer #1 (Public review):

The authors use electrophysiological and behavioral measurements to examine how animals could reliably determine odor intensity/concentration across repeated experience. Because stimulus repetition leads to short-term adaptation evidenced by reduced overall firing rates in the antennal lobe and firing rates are otherwise concentration-dependent, there could be an ambiguity in sensory coding between reduced concentration or more recent experience. This would have a negative impact on the animal's ability to generate adaptive behavioral responses that depend odor intensities. The authors conclude that changes in concentration alter the constituent neurons contributing to the neural population response, whereas adaptation maintains the 'activated ensemble' but with scaled firing rates. This provides a neural coding account of the ability to distinguish odor concentrations even after extended experience. Additional analyses attempt to distinguish hypothesized circuit mechanisms for adaptation. A larger point that runs through the manuscript is that overall spiking activity has an inconsistent relationship with behavior and that the structure of population activity may be the more appropriate feature to consider.

To my knowledge, the dissociation of effects of odor concentration and adaptation on olfactory system population codes was not previously demonstrated. This is a significant contribution that improves on any simple model based on overall spiking activity. The primary result is most strikingly supported by visualization of a principal components analysis in Figure 4. Additional experiments and analysis complement and provide context for this finding regarding the relationship between neural population changes and behavior. There are some natural limitations on the interpretation of these data imposed by the methodology.

(1) Because individual recordings do not acquire a sufficient cell population to carry our population analyses, the cells must be combined into pseudopopulations for many analyses. This is common practice but it limits the ability to test the repeatability of findings across animals or populations. One potential additional solution would be to subsample the pseudopopulation, which would reveal the importance of individual sampled cells in the overall result. The utility of this additional testing is suggested by, for example, the benzaldehyde responses in supplementary figure 5, where two cells differentiate high and low concentration responses and would be expected to strongly impact correlation and classifier analyses.

(2) I do not think the analysis in Figure 2e can be strongly interpreted in terms of the vesicle depletion model. The hard diagonal bound on the lower part of each scatter plot indicates that features of the data/analysis necessarily exclude data in the lower left quadrant. I think this could be possibly explained by a floor effect wherein lower-response neurons cannot possibly express a large deltaResponse. To strengthen this case, one would need to devise a control analysis for the case where neural responses are simply all going as far down as they can go.

(3) Very minor, but it is confusing and not well-described how the error is computed in Figure 1f. One can imagine that the mean p(POR) is arrived at by averaging the binary values across locusts. Is this the case? If so, the same estimation of variance could be applied to Figures 1d and e

Reviewer #3 (Public review):

Summary:

How does the brain distinguish stimulus intensity reduction from response reductions due to adaptation? Ling et al study whether and how the locust olfactory system encodes stimulus intensity and repetition differently. They show that these stimulus manipulations have distinguishable effects on population dynamics.

Strengths:

(1) Provides a potential strategy with which the brain can distinguish intensity decrease from adaptation. -- while both conditions reduce overall spike counts, intensity decrease can also changes which neurons are activated and adaptation only changes the response magnitude without changing the active ensemble.

(2) By interleaving a non-repeated odor, they show that these changes are odor-specific and not a non-specific effect.

(3) Describes how proboscis orientation response (POR) changes with stimulus repetition., Unlike the spike counts, POR increases in probability with stimulus. The data portray the variability across subjects in a clear way.

Weaknesses:

While POR and physiology can show a nice correlation when measured in different animals, additional insight would be gained from acquiring behavior and physiology simultaneously.

eLife Assessment

The manuscript is an important study which aims to demonstrate the conserved and crucial role of IgM in both systemic and mucosal antiviral immunity in teleost, challenging the established differential roles of IgT and IgM. The strength of the evidence is solid and supported by a combination of in vivo studies, viral infection models, and complementary in vitro assays. In the current version, authors validate the MoAb against IgM

Reviewer #2 (Public review):

Summary:

In this manuscript, Weiguang Kong et al. investigate the role of immunoglobulin M (IgM) in antiviral defense in the teleost largemouth bass (Micropterus salmoides). The authors employ an in vivo IgM depletion system and viral infection models, complemented by in vitro assays, histology, and gene expression analysis. Assuming the specificity of the MoAb, their findings demonstrate that largemouth bass IgM functions in both systemic and mucosal immunity and exhibits viral neutralization capabilities by acting on viral particles.

Strengths:

The authors utilize multiple complementary methods, including an innovative teleost immunoglobulin depletion approach, to provide strong evidence for the important and conserved role of IgM in anti-viral resistance. The study also highlights the dual role of teleost IgM at both systemic and mucosal levels, challenging the established idea that IgT primarily mediates mucosal protection. Despite variability in IgM depletion levels, the authors demonstrate that fish with depleted IgM+ B cells exhibit significantly higher viral loads, more severe pathological changes, and increased mortality compared to control fish. These results have evolutionary and practical implications, suggesting that IgM's role as an antiviral effector has been conserved across jawed vertebrates for over 500 million years. Insights into IgM's role could inform vaccine strategies targeting mucosal immunity in fish, addressing a key challenge in aquaculture.

Weaknesses:

While the authors validate the specificity of MoAb against IgM and address most of the aspects suggested by the reviewer. Some aspects are missing, mainly concerning the overstatement of the findings' novelty.

eLife Assessment

This study presents important findings on the insecticidal mechanism of betulin, a plant-derived metabolite, in controlling the aphid Myzus persicae and it provides a demonstration that betulin targets the GABA receptor in aphids, with strong supporting evidence from transcriptomic, biochemical, electrophysiological, and genetic approaches. In particular, the identification of a specific conserved residue (THR228) critical for betulin binding advances our understanding of insect neuropharmacology and offers translational potential for pest management strategies. The evidence supporting the primary claims is solid, with well-integrated methodologies and appropriate controls; however, some interpretative and methodological limitations remain, including the option to further explore off-target effects, as well as the broader evolutionary and ecological context. Addressing these points would strengthen the broader implications of the study.

Reviewer #1 (Public review):

Wang, Junxiu et al. investigated the underlying molecular mechanisms of the insecticidal activity of betulin against the peach aphid, Myzus persicae. There are two important findings described in this manuscript: (a) betulin inhibits the gene expression of GABA receptor in the aphid, and (b) betulin binds to the GABA receptor protein, acting as an inhibitor. The first finding is supported by RNA-Seq and RNAi, and the second one is convinced with MST and electrophysiological assays. Further investigations on the betulin binding site on the receptor protein provided a fundamental discovery that T228 is the key amino acid residue for its affinity, thereby acting as an inhibitor, backed up by site-directed mutagenesis of the heterologously-expressed receptor in E. coli and by CRISPR-genome editing in Drosophila.

Although the manuscript does have strengths in principle, the weaknesses do exist: the manuscript would benefit from more comprehensive analyses to fully support its key claims in the manuscript. In particular:

(1) The Western blotting results in Figure 5A & B appear to support the claim that betulin inhibits GABR gene expression (L26), as a decrease in target protein levels is often indicative of suppressed gene expression. The result description for Figure 5A & B is found in L312-L316, within Section 3.6 ("Responses of MpGABR to betulin"), where MST and voltage-clamp assays are also presented. It seems the observed decrease in MpGABR protein content is due to gene downregulation, rather than a direct receptor protein-betulin interaction. However, this interpretation lacks discussion or analysis in either the corresponding results section or the Discussion. In contrast, Figures 5C-F are specifically designed to illustrate protein-betulin interactions. Presenting Figure 5A & B alongside these panels might lead to confusion, as they support distinct claims (gene expression vs. protein binding/inhibition). Therefore, I recommend moving Figure 5A & B either to the end of Figure 3 or to a separate figure altogether to improve clarity and logical flow. A minor point in the Western blotting experiment is that although GAPDH was used as a reference protein, there is no explanation in the corresponding M&M section.

(2) The description of the electrophysiological recording experiment is unclear regarding the use of GABA. I didn't realize that GABA, the true ligand of the GABA receptor, was used in this inhibition experiment until I reached the Results section (L321), which states, "In the presence of only GABA, a fast inward current was generated." Crucially, no details are provided on the experiment itself, including how GABA was applied (e.g., concentration, duration, whether GABA was treated, followed by betulin, or vice versa). This information is essential for reproducibility. Please ensure these details are thoroughly described in the corresponding M&M section.

(3) The phylogenetic analysis, particularly concerning Figures 4 and 6B, needs significant attention for clarity and representativeness. First, your claim that MpGABR is only closely related to CAI6365831.1 (L305-L310) is inconsistent with the provided phylogenetic tree, which shows MpGABR as equally close to Metopolophium dirhodum (XP_060864885.1) and Acyrthosiphon pisum (XP_008183008.2). Therefore, singling out only Macrosiphum euphorbiae (CAI6365831.1) is not supported by the data. Second, the representation of various insect orders is insufficient. All 11 sequences in the Hemiptera category (in both Figure 4 and Figure 6B) are exclusively from the Aphididae family. This small subset cannot represent the highly diverse Order Hemiptera. Consequently, statements like "only THR228 was conserved in Hemiptera" (L338), "The results of the sequence alignment revealed that only THR228 was conserved in Hemiptera" (L430), or "THR228... is highly conserved in Hemiptera" (L486) are not adequately supported. Third, similar concerns apply to the Diptera order, which includes 10 Drosophila and 2 mosquito samples (not diverse or representative enough), and likely to other orders as well. Thereby, the Figure 6B alignment should be revised accordingly to reflect a more accurate representation or to clarify the scope of the analysis. Fourth, there's a discrepancy in the phylogenetic method used: the M&M section (L156) states that MEGA7, ClustalW, and the neighbor-joining method were used, while the Figure 4 caption mentions that MEGA X, MUSCLE, and the Maximum likelihood method were employed. This inconsistency needs to be clarified and made consistent throughout the manuscript. Fifth, I have significant concerns about the phylogenetic tree itself (Figure 4). A small glitch was observed at the Danaus plexippus node, which raises suspicion regarding potential manipulation after tree construction. More critically, the tree, especially within Coleoptera, does not appear to be clearly resolved. I am highly concerned about whether all included sequences are true GABR orthologs or if the dataset includes partial or related sequences that could distort the phylogeny. Finally, for Figure 6B, both protein (XP_) and nucleotide (XM_) sequences were mix used. I recommend using the protein sequences instead of nucleotide sequences in this figure panel, as protein sequences are more directly informative.

(4) The Discussion section requires significant revision to provide a more insightful and interpretative analysis of the results. Currently, much of the section primarily restates findings rather than offering deeper discussion. For instance, L409-L419 restate the results, followed by the short sentence "Collectively, these results suggest that betulin may have insecticidal effects on aphids by inhibiting MpGABR expression". It could be further expanded to make it beneficial to elaborate on proposed mechanisms by which gene expression might be suppressed, including any potential transcription factors involved. In contrast, while L422-L442 also initially summarize results, the subsequent paragraph (L445-L472) effectively discusses the potential mechanisms of inhibitory action and how mortality is triggered, which is a good model for other parts of the section. However, all the discussion ends up with a short statement, "implying that betulin acts as a CA of MpGABR" (L472), which appears to be a leap. The inference that betulin acts as a competitive antagonist (CA) is solely based on the location of its extracellular binding site, which does not exactly overlap with the GABA binding site. It needs stronger justification or actually requires further experimental validation. The authors should consider rephrasing this statement to acknowledge the need for additional studies to definitively confirm this mechanism of action.

Reviewer #2 (Public review):

Summary:

This important study shows that betulin from wild peach trees disrupts neural signaling in aphids by targeting a conserved site in the insect GABA receptor. The authors present a nicely integrated set of molecular, physiological, and genetic experiments to establish the compound's species-specific mode of action. While the mechanistic evidence is solid, the manuscript would benefit from a broader discussion of evolutionary conservation and potential off-target ecological effects.

Strengths:

The main strengths of the study lie in its mechanistic clarity and experimental rigor. The identification of a betulin-binding single threonine residue was supported by (1) site-directed mutagenesis and (2) functional assays. These experiments strongly support the specificity of action. Furthermore, the use of comparative analyses between aphids and fruit flies demonstrates an important effort to explore species specificity, and the integration of quantitative data further enhances the robustness of the conclusions.

Weaknesses:

There are several important limitations that need to be addressed. The manuscript does not explore whether the observed sensitivity to betulin reflects a broadly conserved feature of GABA receptors across animal lineages or a more lineage-specific adaptation. This evolutionary context is crucial for understanding the broader significance of the findings.

In addition, while the compound's aphicidal effect is well established, the potential for off-target effects in non-target organisms - especially vertebrates - remains unaddressed, despite prior evidence that betulin interacts with mammalian GABAa receptors. There is little discussion on the ecological or environmental safety of exogenous betulin application, such as persistence, degradation, or exposure risks.

eLife Assessment

This valuable study provides evidence supporting a critical role of the axonemal protein ANKRD5 in male infertility. The data generally supports the conclusions and is considered solid, although there are concerns about the cryo-ET analysis. This work will be of interest to biomedical researchers studying ciliogenesis and fertility.

Reviewer #1 (Public review):

Summary:

Asthenospermia, characterized by reduced sperm motility, is one of the major causes of male infertility. The "9 + 2" arranged MTs and over 200 associated proteins constitute the axoneme, the molecular machine for flagellar and ciliary motility. Understanding the physiological functions of axonemal proteins, particularly their links to male infertility, could help uncover the genetic causes of asthenospermia and improve its clinical diagnosis and management. In this study, the authors generated Ankrd5 null mice and found that ANKRD5-/- males exhibited reduced sperm motility and infertility. Using FLAG-tagged ANKRD5 mice, mass spectrometry, and immunoprecipitation (IP) analyses, they confirmed that ANKRD5 is localized within the N-DRC, a critical protein complex for normal flagellar motility. However, transmission electron microscopy (TEM) and cryo-electron tomography (cryo-ET) of sperm from Ankrd5 null mice did not reveal significant structural abnormalities.

Strengths:

The phenotypes observed in ANKRD5-/- mice, including reduced sperm motility and male infertility, are conversing. The authors demonstrated that ANKRD5 is an N-DRC protein that interacts with TCTE1 and DRC4. Most of the experiments are well designed and executed.

Weaknesses:

The last section of cryo-ET analysis is not convincing. "ANKRD5 depletion may impair buffering effect between adjacent DMTs in the axoneme".

"In WT sperm, DMTs typically appeared circular, whereas ANKRD5-KO DMTs seemed to be extruded as polygonal. (Fig. S9B,D). ANKRD5-KO DMTs seemed partially open at the junction between the A- and B-tubes (Fig. S9B,D)." In the TEM images of 4E, ANKRD5-KO DMTs look the same as WT. The distortion could result from suboptimal sample preparation, imaging or data processing. Thus, the subsequent analyses and conclusions are not reliable.

This paper still requires significant improvements in writing and language refinement. Here is an example: "While N-DRC is critical for sperm motility, but the existence of additional regulators that coordinate its function remains unclear" - ill-formed sentences.

Reviewer #2 (Public review):

Summary:

The manuscript investigates the role of ANKRD5 (ANKEF1) as a component of the N-DRC complex in sperm motility and male fertility. Using Ankrd5 knockout mice, the study demonstrates that ANKRD5 is essential for sperm motility and identifies its interaction with N-DRC components through IP-mass spectrometry and cryo-ET. The results provide insights into ANKRD5's function, highlighting its potential involvement in axoneme stability and sperm energy metabolism.

Strengths:

The authors employ a wide range of techniques, including gene knockout models, proteomics, cryo-ET, and immunoprecipitation, to explore ANKRD5's role in sperm biology.

Weaknesses:

Limited Citations in Introduction: Key references on the role of N-DRC components (e.g.,DRC2, DRC4) in male infertility are missing, which weakens the contextual background.

Author response:

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

Reviewer #1 (Public review):

Summary:

Asthenospermia, characterized by reduced sperm motility, is one of the major causes of male infertility. The "9 + 2" arranged MTs and over 200 associated proteins constitute the axoneme, the molecular machine for flagellar and ciliary motility. Understanding the physiological functions of axonemal proteins, particularly their links to male infertility, could help uncover the genetic causes of asthenospermia and improve its clinical diagnosis and management. In this study, the authors generated Ankrd5 null mice and found that ANKRD5-/- males exhibited reduced sperm motility and infertility. Using FLAG-tagged ANKRD5 mice, mass spectrometry, and immunoprecipitation (IP) analyses, they confirmed that ANKRD5 is localized within the N-DRC, a critical protein complex for normal flagellar motility. However, transmission electron microscopy (TEM) and cryo-electron tomography (cryo-ET) of sperm from Ankrd5 null mice did not reveal any structural abnormalities.

Strengths:

The phenotypes observed in ANKRD5-/- mice, including reduced sperm motility and male infertility, are conversing. The authors demonstrated that ANKRD5 is an N-DRC protein that interacts with TCTE1 and DRC4. Most of the experiments are thoughtfully designed and well executed.

Weaknesses:

The cryo-FIB and cryo-ET analyses require further investigation, as detailed below. The molecular mechanism by which the loss of ANKRD5 affects sperm flagellar motility remains unclear. The current conclusion that Ankrd5 knockout reduces axoneme stability is not well-supported. Specifically, are other axonemal proteins diminished in Ankrd5 knockout sperm? Conducting immunofluorescence analyses and revisiting the quantitative proteomics data may help address these questions.

Reviewer #2 (Public review):

Summary:

The manuscript investigates the role of ANKRD5 (ANKEF1) as a component of the N-DRC complex in sperm motility and male fertility. Using Ankrd5 knockout mice, the study demonstrates that ANKRD5 is essential for sperm motility and identifies its interaction with N-DRC components through IP-mass spectrometry and cryo-ET. The results provide insights into ANKRD5's function, highlighting its potential involvement in axoneme stability and sperm energy metabolism.

Strengths:

The authors employ a wide range of techniques, including gene knockout models, proteomics, cryo-ET, and immunoprecipitation, to explore ANKRD5's role in sperm biology.

Weaknesses:

(1) Limited Citations in Introduction: Key references on the role of N-DRC components (e.g., DRC1, DRC2, DRC3, DRC5) in male infertility are missing, which weakens the contextual background.

(2) Lack of Functional Insights: While interacting proteins outside the N-DRC complex were identified, their potential roles and interactions with ANKRD5 are not adequately explored or discussed.

(3) Mitochondrial Function Uncertainty: Immunofluorescence suggests possible mitochondrial localization for ANKRD5, but experiments on its role in energy metabolism (e.g., ATP production, ROS) are insufficient, especially given the observed sperm motility defects.

(4) Glycolysis Pathway Impact: Proteomic analysis indicates glycolysis pathway disruptions in Ankrd5-deficient sperm, but the link between these changes and impaired motility is not well explained.

(5) Cryo-ET Data Limitations: The structural analysis of the DMT lacks clarity on how ANKRD5 influences N-DRC or RS3. The low quality of RS3 data hinders the interpretation of ANKRD5's impact on axoneme structure.

(6) Discussion of Findings: The manuscript could benefit from a deeper discussion on the broader implications of ANKRD5's interactions and its role in sperm energy metabolism and motility mechanisms.

Reviewer #1 (Recommendations for the authors):

EMD-35210/35211 are 16-nm maps while the Ankrd5 null map is 8-nm repeat. To generate a difference map, the authors should use maps of the same periodicity.

Thank you for your suggestion. We have replaced the old 16-nm maps with an 8nm map and updated the images (Fig. 7). The 8nm repeats DMT density map we used was obtained by summing two 16nm repeats DMTs that were staggered 8nm apart from each other (EMD-35229). The replacement of the 16nm repeats DMT density map with the 8nm repeats DMT density map has no effect on our scientific findings and experimental conclusions.

"We were able to detect the N-DRC structure in WT sperm, but we failed to find the density of N-DRC adjacent to RS3 in Ankrd5 null sperm". Do the authors imply that the N-DRC is lost in Ankrd5 null sperm? To draw a conclusion, they need to compare the 96-nm map of WT sperm axoneme with that of Ankrd5 null sperm axoneme. Quantitative proteomics shows that the levels of most N-DRC components in Ankrd5 null sperm are comparable with those of WT sperm. Why are the quantitative proteomics results not consistent with the structural observation?

We are very sorry for this improper description. Our original description was not rigorous, which led to misunderstanding. Our original intention is to say that the quality of the density map causes the N-DRC to be difficult to recognize, rather than that the N-DRC has disappeared. In addition, attempts to classify 96nm repeats DMT structure during our data processing failed. In the process of classification, we found that the density of RS was not good. So we changed the picture and the description.

We have changed the description in the text: "During the STA process, many particles were misaligned or deformed in the classification results, revealing various degrees of deformation—particularly affecting the B-tube (Figure 9,Fig. S9E). We could retain only ~10% of the DMT particles to obtain the final density map for ANKRD5-KO sperm (Fig. S9E), whereas ~70% were usable in WT dataset as reported previously [59]. The mutant DMT density map also displayed roughness at its periphery, indicating substantial structural heterogeneity (Fig. S9E). Even after discarding a large fraction of deformed particles, the final density map still showed evident artifacts, implying that although the mutant DMT preserves the fundamental features of both tubes, its shape is highly heterogeneous (Fig. S9E). Furthermore, attempts to classify the 96-nm repeats did not yield a clear density for radial spokes (RSs) (Fig. S9F), indicating that ANKRD5 deficiency may affect the stability of other accessory structures, such as RSs [24-26]. In the raw tomograms, RSs in ANKRD5-KO sperm appeared less regularly arranged than those in WT(Fig. S9A and C)."

Figure S9. The states of DMT particles in sperm of Ankrd5-KO mouse. (A) and (C) Tomogram slices of WT and Ankrd5-KO in Dynamo (The data for WT mouse sperm was EMPIARC-200007). DMT and RS are marked with white dashed lines and white arrows, respectively. (B) and (D) Comparison of DMT particle states between WT and Ankrd5-KO in Dynamo. The visual angles of the DMT particles shown in (B) and (D) show that the DMT fibers within the white box in (A) and (B) are divided equally into 10 slices along the direction of the white arrow, respectively. The DMT particle shapes of WT and Ankrd5-KO are marked by white dashed lines on the right of (B) and (D). The white arrow in (D) identifies the junction of A-tube and B-tube that is suspected to be disconnected. (E) Deformed particles discarded in 3D classification and final aligned DMT artifacts. (F) 3D classification of attempted RS locations.

In the process of obtaining DMT with a period of 8nm, we discarded about 90% of the particles (some were mis-aligned particles and some were deformed particles). Although the final DMT density showed complete A-tube and B-tube, both the particles in our calculation process and the projection of the final structure showed strong particle heterogeneity.

Our results show that in ANKRD5-KO mice, the structure of sperm DMT itself has no apparent effect in tube A and tube B, and we found that DMT in the original tomography were not smooth. We speculate that loss of ANKRD5 may reduce the interaction between N-DRC and neighboring DMTs, resulting in nonuniform force on the axoneme during sperm swimming, which may limit our ability to obtain an average structure of the more dynamic components (RS, N-DRC, ODA, IDA). Therefore, when trying to classify 96nm repeat DMTS, we can only see the density of suspected RS3 and RS2, but it is difficult to obtain the confident 96nm repeat DMT density. It is difficult to further discuss the effects of ANKRD5 on RS3 and N-DRC. To test this conjecture, we further classified the density of suspected RS3, and the results obtained exhibited a variety of mixed states (Fig. S9). To avoid confusion, we have already removed the discussion of RS3 and the related images from the original text.

It's not clear whether N-DRC proteins and ODA, IDA, RS proteins are affected in DMT of Ankrd5 null sperm. Immunofluorescence staining would help to resolve this problem.

Thank you for your suggestion. The levels of N-DRC proteins and ODA, IDA, RS were detected by immunofluorescence, and no difference was found between ANKRD5-null sperm and control. We added figure S6 as a new figure and added the following description in red font on page 7 of the article:

Figure S6. Immunofluorescence results of ANKRD5-null sperm and control. DRC11 serves as a marker protein for N-DRC (nexin-dynein regulatory complex), NME5 as a marker for RS (radial spoke), DNALI1 as a marker for IDA (inner dynein arm), and DNAI1 as a marker for ODA (outer dynein arm).

In addition, ODA and RS were also marked in the figure when we further analyzed the Cryo-ET data (Figure 7 and Figure S9).

Does Ankrd5 express in other cilia cells except for sperm?

We stained mouse respiratory cilia using immunofluorescence and found that the protein was also expressed in mouse respiratory cilia. To support this finding, we added Figure S3 as a new figure and included a description in red font on page 6 of the article.

Page 7, "However, in the process of manual selection of DMT fibers, we found that they were not as smooth as WT particles." This description is too subjective. Please show the data.

Thank you for your suggestion. We have added a supplementary figure showing the difference between mutant samples and WT samples during particle picking (Fig. S9).

Abstract, "These findings establish that ANKRD5 is critical for maintaining axoneme stability, "Page 7, "This suggests that the knockout of Ankrd5 may affect the structural stability of the axoneme," I do not see direct evidence that Ankrd5 KO reduces the axoneme stability.

Our phrasing was not sufficiently precise. These findings suggest that ANKRD5 plays a crucial role in limiting the relative sliding between adjacent microtubule doublets during axoneme bending, rather than directly contributing to the stability of the axoneme. This sentence has already been modified in the abstract and marked in red. We have added the description in the text: "These findings suggest that ANKRD5 may weaken the N-DRC’s "car bumper" role, reducing the buffering effect between adjacent DMTs and thereby destabilizing axoneme structures during intense axoneme motility." and "To further investigate the RS, IDA, and ODA structures of the axonemes, we conducted immunofluorescence assays in both Ankrd5^-/- mice and the control group. No significant differences were detected between the two groups (Fig. S6)."

Page 8, "but our study offers new perspectives for male contraceptive research". Could the authors expand this a bit - how this study may offer new perspectives for male contraceptive research?

We sincerely appreciate the reviewer's insightful feedback regarding the translational potential of our findings. This is indeed a critical aspect that we sought to highlight. In response, we have added a paragraph on page 9 (marked in red) to further emphasize this point. We have added the description in the text: "The potential for male contraceptive development arises from ANKRD5's critical structural role mediated through its ANK domain, which facilitates interaction with the N-DRC complex in sperm flagella. Recent structural evidence suggests the protein's positively charged surface may engage with glutamylated tubulin in adjacent microtubules[41], presenting a druggable interface. Targeted disruption of this interaction through small-molecule inhibitors could transiently impair sperm motility. Sperm function relies more on ANKRD5 than respiratory cilia, so inhibiting ANKRD5 has less impact on the latter. This makes ANKRD5 a promising drug target. This tissue-specific phenotypic uncoupling is not uncommon among axonemal-associated proteins, such as DNAH17 and IQUB[65，66]."

Abstract, "reveals its interaction with TCTE1 and DRC4/GAS8", please provide the alias symbol DRC5 for TCTE1 for clarity.

Thank you for your suggestion, I have revised the abstract by replacing "TCTE1" with "DRC5/TCTE1" to clarify the alias. The changes have been highlighted in red in the manuscript for easy reference.

Introduction, "Fertilization relies on successful spermatogenesis and normal sperm motility (4), which occurs in the testes." Does spermatogenesis or normal sperm motility occur in the testes?

Thank you for pointing out the ambiguity in the sentence. We have revised the sentence in the Introduction and highlighted it in red as follows: Fertilization relies on successful spermatogenesis and normal sperm motility..

Introduction, "The axoneme exhibits a 9+2 microtubule doublet structure". The description is not accurate. The "2" are singlet microtubules.

Thank you for your suggestion. We have revised the sentence to accurately describe the axoneme structure and highlight in red as follows: The axoneme features a 9+2 architecture, comprising nine doublet microtubules encircling a central pair of singlet microtubules, with the N-DRC forming cross-bridges between adjacent doublets.

Page 4, "control sperm successfully fertilized both cumulus-intact eggs". "control" should be a capital "C".

We thank the reviewer for noting this oversight. The correction has been implemented on page 5 with the term highlighted in red (now reading: "Control sperm successfully fertilized both cumulus-intact eggs"), and we have verified capitalization consistency throughout the manuscript.

Page 6, "applied RELION, M, and other software". "other software" is not an appropriate description, please be precise.

We have revised the description as suggested. Specifically, on page 7, the phrase "and other software" has been replaced with "Dynamo and Warp/M," and this change is highlighted in red for clarity.

Reviewer #2 (Recommendations for the authors):

Several components of the N-DRC complex (e.g., DRC1, DRC2, DRC3, DRC5) have been reported to be associated with male infertility in both humans and mice. However, the introduction lacks proper citations for these studies. Adding these references would provide a more comprehensive background for readers.

Thank you for your suggestion to strengthen the comprehensiveness of the research background by incorporating additional literatures. More literatures related to DRC1, DRC2, DRC3, and DRC5 were cited in the background of this paper. We have rewritten and reorganized the language of the last paragraph of the introduction, and the entire paragraph is highlighted in red. The content of the paragraph is as follows:

"It was previously believed that N-DRC comprised 11 protein components[13，18]. However, a new component CCDC153 (DRC12) was found to interact with DRC1[19]. In situ cryoelectron tomography (cryo-ET) has significantly advanced understanding of the N-DRC architecture in Chlamydomonas, demonstrating that DRC1, DRC2/CCDC65, and DRC4/GAS8 constitute its core framework[16], while proteins DRC3/5/6/7/8/11 associate with this framework and engage with other axonemal complexes[20]. Biochemical experiments corroborate these findings and validate this structural model[12，21，22]. The N-DRC functions between the DMTs to convert sliding into axonemal bending motion by restricting the relative sliding of outer microtubule doublets[23，24，25]. Mutations of N-DRC subunits demonstrate that the structural integrity of the N-DRC is crucial for flagellar movements. Mutations in DRC1, DRC2/CCDC65, and DRC4/GAS8 are linked to ciliary motility disorders, causing primary ciliary dyskinesia (PCD)[12，26]. Biallelic truncating mutations in DRC1 induce multiple morphological abnormalities of sperm flagella (MMAF), including outer DMT disassembly, mitochondrial sheath disorganization, and incomplete axonemal structures in human sperm[22，27，28]. Similarly, CCDC65 loss disrupts N-DRC stability, leading to disorganized axonemes, global microtubule dissociation, and complete asthenozoospermia[12，29].  Homozygous frameshift mutations in DRC3 impair N-DRC assembly and intraflagellar transport (IFT), resulting in severe motility defects despite normal sperm morphology[30，31]. TCTE1 knockout mice maintain normal sperm axoneme structure but show impaired glycolysis, leading to reduced ATP levels, lower sperm motility, and male infertility[32]. Both Drc7 and Iqcg (Drc9) knockout mice exhibit disrupted '9+2' axonemal architecture, sperm immotility, and male infertility[21，33]. Drc7 knockout sperm also display head deformities and shortened tails[21]. While N-DRC is critical for sperm motility, but the existence of additional regulators that coordinate its function remains unclear. Our findings indicate that ANKRD5 (Ankyrin repeat domain 5; also known as ANK5 or ANKEF1) interacts with N-DRC structure, serving as an auxiliary element to facilitate collaboration among DRC members. The absence of ANKRD5 results in diminished sperm motility and consequent male infertility."

While many N-DRC components were identified as interacting with ANKRD5, other proteins outside the N-DRC complex were also detected. Notably, GAS8 (DRC4) ranked 165th among the identified proteins. What are the functions of the higher-ranking proteins, and why do they interact with ANKRD5? Discussing their potential roles would enhance the mechanistic understanding of ANKRD5's function.

We thank the reviewer for highlighting the importance of non-N-DRC proteins interacting with ANKRD5 (ANKEF1). Below, we provide a detailed analysis of the roles and interaction mechanisms of the top-ranked non-N-DRC proteins (Krt77, Rab2a, Gm7429) to elucidate their functional relevance to ANKRD5. We have added the following text to page 6 to clarify and highlight this in red:

As for other proteins in the LC-MS results, KRT77 is a classic protein that maintains cytoskeletal stability. It may enhance the physical connection between the N-DRC and adjacent DMTs through interaction with ANKRD5. Recent studies indicate that ANKRD5, a newly identified component in the distal lobe of the N-DRC, has a positively charged surface, which may facilitate binding to glutamylated tubulin on adjacent DMTs[41]. Thus, KRT77 may also regulate its interaction with ANKRD5 via post-translational modifications (PTMs, e.g., phosphorylation), thereby strengthening sperm resistance to shear forces during flagellar movement. Rab family proteins participate in intraflagellar transport and membrane dynamics. RAB2A may promote targeted transport of ANKRD5 or other N-DRC components to axonemal assembly sites by recruiting vesicles, and its GTPase activity might link cellular signals to ANKRD5-mediated axoneme remodeling. However, the observed signals could be false positives due to nonspecific factors such as electrostatic adsorption, high-abundance protein interference, detergent-induced membrane disruption, or protein aggregation tendencies.

The immunofluorescence localization of ANKRD5-Flag appears more aligned with the mitochondrial sheath rather than the axoneme. There is a finer red fluorescent signal extending from the mitochondrial sheath that might correspond to the axoneme. Could this suggest that ANKRD5 has a functional role in the mitochondria? While the authors measured ROS levels, this might not fully clarify whether ANKRD5 is involved in sperm energy metabolism. Considering the motility defects in Ankrd5 knockout mice, further experiments to explore ANKRD5's potential involvement in energy metabolism are necessary.

The increased detection of ANKRD5 in the midpiece region of the sperm axoneme does not necessarily indicate its localization in mitochondria. Immunofluorescence signals of multiple axonemal Nexin-Dynein Regulatory Complex (N-DRC) components (e.g., TCTE1, DRC1, CCDC65, DRC3, GAS8, and DRC7) are also non-uniformly distributed along the entire flagellum[1]. Similar localization patterns are observed in other structural components, such as radial spoke protein NME5[2] and outer dynein arm protein DNAH5[3]. Furthermore, mitochondria are membrane-bound organelles, and ANKRD5 predominantly resides in the SDS-soluble fraction under varying lysis conditions, confirming its association with the axoneme rather than mitochondria. Thus, the spatial distribution of ANKRD5 does not support a functional role in mitochondria. Importantly, we validated intact mitochondrial function through measurements of reactive oxygen species (ROS) levels (Figure S5C, D), ATP content (Figure 6E), and mitochondrial membrane potential (Figure S5A, B).

Proteomic analysis of Ankrd5-deficient sperm revealed disruptions in the glycolysis pathway. While these changes do not appear to affect ATP production, the mechanism by which these disruptions impact sperm motility remains unclear. Further investigation into how glycolysis pathway alterations contribute to impaired motility is warranted.

We appreciate the reviewer's careful consideration of our proteomic data. However, our Gene Set Enrichment Analysis (GSEA) of glycolysis/gluconeogenesis pathways showed no significant enrichment (p-value=0.089, NES=0.708; Fig.6D), which does not meet the statistical thresholds for biological significance (|NES|>1, pvalue<0.05). This observation is further corroborated by our direct ATP measurements showing no difference between genotypes (Fig.6E). We agree that further studies on metabolic regulation could be valuable, but current evidence does not support glycolysis disruption as a primary mechanism for the motility defects observed in Ankrd5-null sperm. This misinterpretation likely arose from the reviewer's overinterpretation of non-significant proteomic trends. We request that this specific claim be excluded from the assessment to avoid misleading readers.

Weaknesses:

Cryo-ET Data Limitations: The structural analysis of the DMT lacks clarity on how ANKRD5 influences NDRC or RS3. The low quality of RS3 data hinders the interpretation of ANKRD5's impact on axoneme structure.

We tried to further calculate the DMT at 96nm period using the present data to analyze the effect of ANKRD5 deletion on RS and N-DRC, however, due to the heterogeneity of the data, we were only able to obtain DMT at 8nm period (we have added a figure in the supplementary material for presentation). And in the process of obtaining DMT with a period of 8nm, we throw away about 90% of the particles (some are misaligned particles, some are deformed particles). Although we were not able to obtain the structure of 96nm repeats DMT, we noticed the enhanced heterogeneity of DMT caused by ANKRD5 knockout, as shown by the 3D classification and other results of the new supplementary images (Fig. S9), and the graphic description was added in the original article.

We have changed the description in the text: "During particle picking of DMT fibers, we observed that transverse sections of axonemal DMT particles from ANKRD5-KO sperm differ markedly from those in WT sperm. Although both A- and B-tubes were visible in both samples, the DMTs in ANKRD5-KO sperm showed a more irregular profile. In WT sperm, DMTs typically appeared circular, whereas ANKRD5-KO DMTs seemed to be extruded as polygonal. (Fig. S9B,D). Notably, ANKRD5-KO DMTs seemed partially open at the junction between the A- and B-tubes (Fig. S9B,D).

During the STA process, many particles were misaligned or deformed in the classification results, revealing various degrees of deformation—particularly affecting the B-tube (Fig. S9E). We could retain only ~10% of the DMT particles to obtain the final density map for ANKRD5-KO sperm (Fig. S9E), whereas ~70% were usable in WT dataset as reported previously [59]. The mutant DMT density map also displayed roughness at its periphery, indicating substantial structural heterogeneity (Fig. S9E). Even after discarding a large fraction of deformed particles, the final density map still showed evident artifacts, implying that although the mutant DMT preserves the fundamental features of both tubes, its shape is highly heterogeneous (Fig. S9E). Furthermore, attempts to classify the 96-nm repeats did not yield a clear density for radial spokes (RSs) (Fig. S9F), indicating that ANKRD5 deficiency may affect the stability of other accessory structures, such as RSs [23，24，25]. In the raw tomograms, RSs in ANKRD5-KO sperm appeared less regularly arranged than those in WT (Fig. S9A and C).

Most recently, following the submission of this work, ANKRD5 was reported to localize at the head of the N-DRC, simultaneously binding DRC11, DRC7, DRC4, and DRC5 [46]. This structural insight agrees with our in vitro findings that ANKRD5 interacts with DRC4 and DRC5 (Fig. 8C-F). However, that study used isolated and purified DMT samples, leaving the precise positioning of ANKRD5 between adjacent axonemal DMTs unconfirmed. We therefore fitted the published structure (PDB entry: 9FQR) into the in situ DMT structure of mouse sperm 96-nm repeats (EMD-27444), revealing that ANKRD5 lies a mere ~3 nm from the adjacent DMT (Fig. 8G). Notably, the N-DRC is often likened to a "car bumper", buffering two neighboring DMTs during vigorous axonemal motion. Given the extensive DMT deformation observed in our cryo-ET data (Fig. S9E), we propose that ANKRD5 contributes to this buffering function at the N-DRC. The loss of ANKRD5 may weaken the "bumper" effect and consequently increase structural damage to adjacent DMTs under intense conditions, while also compromising the stability of associated DMT accessory structures [19，46，60]."

Figure S9. The states of DMT particles in sperm of Ankrd5-KO mouse. (A) and (C) Tomogram slices of WT and Ankrd5-KO in Dynamo (The data for WT mouse sperm was EMPIARC-200007). DMT and RS are marked with white dashed lines and white arrows, respectively. (B) and (D) Comparison of DMT particle states between WT and Ankrd5-KO in Dynamo. The visual angles of the DMT particles shown in (B) and (D) show that the DMT fibers within the white box in (A) and (B) are divided equally into 10 slices along the direction of the white arrow, respectively. The DMT particle shapes of WT and Ankrd5-KO are marked by white dashed lines on the right of (B) and (D). The white arrow in (D) identifies the junction of A-tube and B-tube that is suspected to be disconnected. (E) Deformed particles discarded in 3D classification and final aligned DMT artifacts. (F) 3D classification of attempted RS locations.

Although the loss of ANKRD5 did not affect the density of DMT itself in A Tube and B Tube, we found that DMT particles were not smooth in the original tomogram. We speculate that the loss of ANKRD5, a component of the N-DRC that is close to the neighboring DMT, may reduce the interaction between N-DRC and the neighboring DMT, resulting in uneven force on the axoneme during sperm swimming, which may limit our ability to obtain the average structure of the more dynamic components (RS, N-DRC, ODA, IDA). Therefore, when trying to classify 96nm repeat DMT, we could only see the density of suspected RS3 and RS2, but it was difficult to obtain the complete 96nm repeat DMT density, so that we could not further analyze the effect of ANKRD5 deletion on RS and N-DRC. To test this conjecture, we further classified the density of suspected RS3, and the results obtained exhibited a variety of mixed states (which have been added to the supplementary material). To avoid confusion, we have already removed the discussion of RS3 and the related images from the original text.

The cryo-ET data on the internal structure of the DMT seems to have limited relevance to the N-DRC complex. Additionally, the quality of the RS3 data appears suboptimal, making it difficult to understand how the absence of ANKRD5 influences RS3. Further refinement of the data or alternative approaches may be needed to address this question.

Thank you very much for your suggestions. For the 96 nm periodic DMT, we have conducted multiple rounds of classification, including applying different masks at the positions of ODA, RS, and DMT. We have also tried classifying with both a single reference and multiple references. However, we were unable to obtain a suitable 96 nm periodic DMT. Regarding the heterogeneity of the particles, we have added a discussion in the manuscript. Following your advice, we have reanalyzed the data, but unfortunately, we still could not further optimize the experimental results.

In the process of obtaining the 8 nm periodic DMT, we discarded approximately 90 percent of the particles through multiple rounds of classification and alignment, in order to obtain high-quality 8 nm periodic DMT. We classified the remaining particles and found that the densities of RS3 and RS2 were not in their normal states. RS3 might be a mixture of different states of RS3, which makes it difficult for us to further discuss the effects of ANKRD5 on RS3.

To avoid confusion, we have already removed the discussion of RS3 and the related images from the original text.

Regarding the effects of ANKRD5 deficiency, we speculate that as the head of the N-DRC, its absence might affect the interaction between the N-DRC and the adjacent DMT, thereby influencing the forces experienced by the DMT during sperm movement. The uneven and irregular forces on the nine pairs of DMTs do not affect the structure of the A and B tubes of the DMT itself, but result in some heterogeneity in the peripheral microtubule parts of the DMT particles. We have added a discussion on these hypotheses in the manuscript. In addition, our 3D classification results demonstrate the structural heterogeneity of DMT caused by ANKRD5 knockdown. We have changed the description in the text:"During particle picking of DMT fibers, we observed that transverse sections of axonemal DMT particles from ANKRD5-KO sperm differ markedly from those in WT sperm. Although both A- and B-tubes were visible in both samples, the DMTs in ANKRD5-KO sperm showed a more irregular profile. In WT sperm, DMTs typically appeared circular, whereas ANKRD5-KO DMTs seemed to be extruded as polygonal. (Fig. S9B,D). Notably, ANKRD5-KO DMTs seemed partially open at the junction between the A- and B-tubes (Fig. S9B,D).

During the STA process, many particles were misaligned or deformed in the classification results, revealing various degrees of deformation—particularly affecting the B-tube (Figure 9, Fig. S9E). We could retain only ~10% of the DMT particles to obtain the final density map for ANKRD5-KO sperm (Fig. S9E), whereas ~70% were usable in WT dataset as reported previously [59]. The mutant DMT density map also displayed roughness at its periphery, indicating substantial structural heterogeneity (Fig. S9E). Even after discarding a large fraction of deformed particles, the final density map still showed evident artifacts, implying that although the mutant DMT preserves the fundamental features of both tubes, its shape is highly heterogeneous (Fig. S9E). Furthermore, attempts to classify the 96-nm repeats did not yield a clear density for radial spokes (RSs) (Fig. S9F), indicating that ANKRD5 deficiency may affect the stability of other accessory structures, such as RSs [23，24，25]. In the raw tomograms, RSs in ANKRD5-KO sperm appeared less regularly arranged than those in WT (Fig. S9A and C).

Most recently, following the submission of this work, ANKRD5 was reported to localize at the head of the N-DRC, simultaneously binding DRC11, DRC7, DRC4, and DRC5 [46]. This structural insight agrees with our in vitro findings that ANKRD5 interacts with DRC4 and DRC5 (Fig. 8C-F). However, that study used isolated and purified DMT samples, leaving the precise positioning of ANKRD5 between adjacent axonemal DMTs unconfirmed. We therefore fitted the published structure (PDB entry: 9FQR) into the in situ DMT structure of mouse sperm 96-nm repeats (EMD-27444), revealing that ANKRD5 lies a mere ~3 nm from the adjacent DMT (Fig. 8G). Notably, the N-DRC is often likened to a "car bumper", buffering two neighboring DMTs during vigorous axonemal motion. Given the extensive DMT deformation observed in our cryo-ET data (Fig. S9E), we propose that ANKRD5 contributes to this buffering function at the N-DRC. The loss of ANKRD5 may weaken the "bumper" effect and consequently increase structural damage to adjacent DMTs under intense conditions, while also compromising the stability of associated DMT accessory structures [19，46，60]."

To further enhance the readability of our manuscript, we created a Graphic Abstract to visually illustrate the biological functions of ANKRD5. The figure is placed immediately after the Abstract section and has been designated as Figure 9.

eLife Assessment

The formation of the Z-ring at the time of bacterial cell division interests researchers working towards understanding cell division across all domains of life. The manuscript by Jasnin et al reports the cryoET structure of toroid assembly formation of FtsZ filaments driven by ZapD as the cross linker. The findings are important and have the potential to open a new dimension in the field, and the evidence to support these exciting claims is solid.

Reviewer #1 (Public review):

Summary:

The major result in the manuscript is the observation of the higher order structures in a cryoET reconstruction that could be used for understanding the assembly of toroid structures. The cross-linking ability of ZapD dimers result in bending of FtsZ filaments to a constant curvature. Many such short filaments are stitched together to form a toroid like structure. The geometry of assembly of filaments - whether they form straight bundles or toroid like structures - depends on the relative concentrations of FtsZ and ZapD.

Strengths:

In addition to a clear picture of the FtsZ assembly into ring-like structures, the authors have carried out basic biochemistry and biophysical techniques to assay the GTPase activity, the kinetics of assembly, and the ZapD to FtsZ ratio.

Weaknesses:

Future scope of work includes the molecular basis of curvature generation and how molecular features of FtsZ and ZapD affect the membrane binding of the higher order assembly.

Reviewer #3 (Public review):

Summary:

Previous studies have analyzed the binding of ZapD to FtsZ and provided images of negatively stained toroids and straight bundles, where FtsZ filaments are presumably crosslinked by ZapD dimers. Toroids without ZapD have also been previously formed by treating FtsZ with crowding agents. The present study is the first to apply cryoEM tomography, which can resolve the structure of the toroids in 3D. This shows a complex mixture of filaments and sheets irregularly stacked in the Z direction and spaced radially. The most important interpretation would be to distinguish FtsZ filaments from ZapD crosslinks, This is less convincing. The authors seem aware of the ambiguity: "However, we were unable to obtain detailed structural information about the ZapD connectors due to the heterogeneity and density of the toroidal structures, which showed significant variability in the conformations of the connections between the filaments in all directions." Therefore, the reader may assume that the crosslinks identified and colored red are only suggestions, and look for their own structural interpretations.

Strengths:

This is the first cryoEM tomography to image toroids and straight bundles of FtsZ filaments bound to ZapD. A strength is the resolution, which. at least for the straight bundles. is sufficient to resolve the ~4.5 nm spacing of ZapD dimers attached to and projecting subunits of an FtsZ filament. Another strength is the pelleting assay to determine the stoichiometry of ZapD:FtsZ (although this also leads to weaknesses of interpretation).

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

The major result in the manuscript is the observation of the higher order structures in a cryoET reconstruction that could be used for understanding the assembly of toroid structures. The cross-linking ability of ZapD dimers result in bending of FtsZ filaments to a constant curvature. Many such short filaments are stitched together to form a toroid like structure. The geometry of assembly of filaments - whether they form straight bundles or toroid like structures - depends on the relative concentrations of FtsZ and ZapD.

Strengths:

In addition to a clear picture of the FtsZ assembly into ring-like structures, the authors have carried out basic biochemistry and biophysical techniques to assay the GTPase activity, the kinetics of assembly, and the ZapD to FtsZ ratio.

Weaknesses:

The discussion does not provide an overall perspective that correlates the cryoET structural organisation of filaments with the biophysical data. The current version has improved in terms of addressing this weakness and clearly states the lacuna in the model proposed based on the technical limitations.

Future scope of work includes the molecular basis of curvature generation and how molecular features of FtsZ and ZapD affect the membrane binding of the higher order assembly.

Reviewer #3 (Public review):

Summary:

Previous studies have analyzed the binding of ZapD to FtsZ and provided images of negatively stained toroids and straight bundles, where FtsZ filaments are presumably crosslinked by ZapD dimers. Toroids without ZapD have also been previously formed by treating FtsZ with crowding agents. The present study is the first to apply cryoEM tomography, which can resolve the structure of the toroids in 3D. This shows a complex mixture of filaments and sheets irregularly stacked in the Z direction and spaced radially. The most important interpretation would be to distinguish FtsZ filaments from ZapD crosslinks, This is less convincing. The authors seem aware of the ambiguity: "However, we were unable to obtain detailed structural information about the ZapD connectors due to the heterogeneity and density of the toroidal structures, which showed significant variability in the conformations of the connections between the filaments in all directions." Therefore, the reader may assume that the crosslinks identified and colored red are only suggestions, and look for their own structural interpretations. But readers should also note some inconsistencies in stoichiometry and crosslinking arrangements that are detailed under "weaknesses."

Strengths.

This is the first cryoEM tomography to image toroids and straight bundles of FtsZ filaments bound to ZapD. A strength is the resolution, which. at least for the straight bundles. is sufficient to resolve the ~4.5 nm spacing of ZapD dimers attached to and projecting subunits of an FtsZ filament. Another strength is the pelleting assay to determine the stoichiometry of ZapD:FtsZ (although this also leads to weaknesses of interpretation).

Weaknesses

The stoichiometry presents some problems. Fig. S5 uses pelleting to convincingly establish the stoichiometry of ZapD:FtsZ. Although ZapD is a dimer, the concentration of ZapD is always expressed as that of its subunit monomers. Fig. S5 shows the stoichiometry of ZapD:FtsZ to be 1:1 or 2:1 at equimolar or high concentrations of ZapD. Thus at equimolar ZapD, each ZapD dimer should bridge two FtsZ's, likely forming crosslinks between filaments. At high ZapD, each FtsZ should have it's own ZapD dimer. However, this seems contradicted by later statements in Discussion and Results. (1) "At lower concentrations of ZapD, .. toroids are the most prominent structures, containing one ZapD dimer for every four to six FtsZ molecules." Shouldn't it be one ZapD dimer for every two FtsZ? (2) "at the high ZapD concentration...a ZapD dimer binds two FtsZ molecules connecting two filaments." Doesn't Fig. S5 show that each FtsZ subunit has its own ZapD dimer? And wouldn't this saturate the CTD sites with dimers and thus minimize crosslinking?

We thank the reviewer for these insightful comments. The affinity of ZapD for FtsZ is relatively low and a higher concentration of ZapD is required in solution to effectively saturate the binding sites of all FtsZ molecules forming macrostructures. It is important to clarify that the concentrations mentioned in the text refer to the amounts and ratios of protein added to the total volume of the sample, rather than the proteins actively interacting and forming bundles or macrostructures.

To differentiate, two aspects can be considered: the ratio of added protein (as mentioned in the text) and the fraction of proteins that contribute to the formation of the macrostructures. Under polymerization conditions, FtsZ-GTP recruits additional monomers to form polymers. Therefore, more FtsZ than ZapD would be involved in forming filaments and bundles. Our results support this hypothesis and show that a higher amount of ZapD is required in the sample to pellet with FtsZ bundles.

We propose that starting with the same initial concentration of FtsZ and ZapD in solution, only a small fraction of ZapD will bind to the structures, favoring the formation of toroidal structures despite the initial 1:1 ratio of proteins added to the sample. When considering a higher FtsZ:ZapD ratio (1:6), the increased amount of ZapD in solution would facilitate the saturation of all FtsZ binding sites, consistent with the observation of straight bundles. Analytical sedimentation velocity data further supported this finding, indicating a binding ratio of approximately 0.3-0.4, suggesting that one ZapD dimer binds for every 4-6 FtsZ monomers. The binding ratio indicates that two FtsZ monomers will bind to a single dimer of ZapD, but this only occurs when there is a significant excess of ZapD over FtsZ in the solution mixture. 

These findings align qualitatively with the relative intensities of the electrophoretic bands observed for FtsZ and ZapD in the pelleting assay with different FtsZ-ZapD mixtures, as shown in Suppl. Fig. 5 as % of FtsZ in the fractions. Without prior staining calibration of the gels, there is no simple quantitative relationship between gel band intensities after Coomassie staining and the amount of protein in a band (Darawshe et al. 1993 Anal Biochem - DOI: 10.1006/abio.1993.1581). This last point precludes a quantitative comparison between pelleting/SDS-PAGE data and analytical sedimentation measurements. For this reason, we have decided to present pelleting results as % of FtsZ in supernatant and pellet to avoid overestimations. 

A major weakness is the interpretation of the cryoEM tomograms, specifically distinguishing ZapD from FtsZ. The distinction of crosslinks seems based primarily on structure: long continuous filaments (which often appear as sheets) are FtsZ, and small masses between filaments are ZapD. The density of crosslinks seems to vary substantially over different parts of the figures. More important, the density of ZapD's identified and colored red seem much lower than the stoichiometry detailed above. Since the mass of the ZapD monomer is half that of FtsZ, the 1:1 stoichiometry in toroids means that 1/3 of the mass should be ZapD and 2/3 FtsZ. However, the connections identified as ZapD seem much fewer than the expected 1/3 of the mass. The authors conclude that connections run horizontally, diagonally and vertically, which implies no regularity. This seems likely, but as I would suggest that readers need to consider for themselves what they would identify as a crosslink.

The amount of ZapD in the toroids will be significantly less than one third. Although the theoretical addition of protein to the samples is at a 1:1 ratio, the actual amount of protein in the macrostructures containing ZapD is much lower, as shown by sedimentation velocity pelleting assays.

In contrast to the toroids formed at equimolar FtsZ and ZapD, thin bundles of straight filaments are assembled in excess ZapD. Here the stoichiometry is 2:1, which would mean that every FtsZ should have a bound ZapD DIMER. The segmentation of a single filament in Fig. 5e seems to agree with this, showing an FtsZ filament with spikes emanating like a picket fence, with a 4.5 nm periodicity. This is consistent with each spike being a ZapD dimer, and every FtsZ subunit along the filament having a bound ZapD dimer. But if each FtsZ has its own dimer, this would seem to eliminate crosslinking. The interpretative diagram in Fig. 6, far right, which shows almost all ZapD dimers bridging two FtsZs on opposite filaments, would be inconsistent with this 2:1 stoichiometry.

Assessing the precise stoichiometry of FtsZ and ZapD within the macrostructures is challenging. We interpret the spikes as ZapD dimers bridging two FtsZ filaments, implying a theoretical 1:1 stoichiometry in the straight bundle. However, ZapD may be enriched in certain areas, indicating that a single FtsZ monomer is binding to one side of the dimer. In contrast, the other side remains available for additional connections, resulting in a potential 2:1 stoichiometry. A combination of both scenarios is likely, although our resolution does not allow further characterization. Considering these complexities, we assume these connections represent a dimer of ZapD binding to two FtsZ monomers.

Figure 6 shows a simplified scheme illustrating how the bundles could be assembled based on the Cryo-ET data. We acknowledge the limitations of this diagram; its purpose is to depict the mesh formed by the stabilization of ZapD. We have not included interactions that do not lead to filament crosslinking, such as dimers binding to only one FtsZ filament. This focus enhances the interpretation of the scheme and the FtsZ-ZapD interaction. A sentence has been added to the caption to highlight the possibility of other interactions not considered in the scheme.

In the original review I suggested a control that might help identify the structures of ZapD in the toroids. Popp et al (Biopolymers 2009) generated FtsZ toroids that were identical in size and shape to those here, but lacking ZapD. These toroids of pure FtsZ were generated by adding 8% polyvinyl chloride, a crowding agent. The filamentous substructure of these toroids in negative stain seemed very similar to that of the ZapD toroids here. CryoET of these toroids lacking ZapD might have been helpful in confirming the identification of ZapD crosslinks in the present toroids. However, the authors declined to explore this control.

The mechanisms by which methylcellulose (MC) promotes the assembly of FtsZ macrostructures reported by Popp et al. involve more than simple excluded volume effects, as the low concentration of MC (less than 1 mg/ml) falls below the typical crowding regime. The latter suggests the existence of poorly characterized additional interactions between MC and FtsZ. These complexities preclude the use of FtsZ polymers formed in the presence of MC as a true control for the FtsZ toroidal structures reported here.

Finally, it should be noted that the CTD binding sites for ZapD should be on the outside of curved filaments, the side facing the membrane in the cell. All bound ZapD should project radially outward, and if it contacted the back side of the next filament, it should not bind (because the CTD is on the front side). The diagram second to right in Fig. 6 seems to incorporate this abortive contact.

The role of the flexible linker and its biological implications are still under debate in the field. The flexible linker allows ZapD-driven connections to be made in different directions. While these implications are not the primary focus of our manuscript, the flexible linker could allow connections between filaments in different orientations.

Reviewer #1 (Recommendations for the authors):

Most of the concerns which I had raised in the earlier version have been taken care of, as detailed in the response.

A few minor points, mostly related to re-phrasing are listed below:

Page 2: line 21: The use of the term 'C-terminal domain' for the C-terminal unstructured region of FtsZ is confusing. The term C-terminal domain or CTD for FtsZ is commonly used to describe part of the globular domain, while C-terminal tail or CCTP will be a more apt usage for all the instances in this manuscript.

We refer to the C-terminal domain as the carboxy-terminal region of the protein. This domain includes the C-terminal linker (CTL), which varies in length between species, followed by a conserved 11-residue sequence (CTC) and shorter, variable C-terminal sequences (CTV). We used the term "C-terminal domain" primarily to improve the readability of the manuscript, but we appreciate the reviewer's feedback. We have now adopted the term "CCTP" instead of "C-terminal domain" to improve the clarity of our manuscript.

On a related note, the schematic in Fig 1 shows the interaction with CCTP rather than the C-terminal domain of the globular FtsZ. Please provide an explanation.

We refer to the unstructured C-terminal domain of FtsZ as the C-terminal tail. To avoid confusion, we have introduced the term CCTP in this manuscript.

Supple Fig 2: "The FCS analysis demonstrated an increasing diffusion time of ZapD along with the FtsZ concentration as result of higher proportion of ZapD bound to FtsZ.

The increased diffusion time need not be interpreted as increased ZapD bound, it could also mean that FtsZ could polymerise in the presence of increasing ZapD, was this possibility ruled out? Including a comment on this aspect will be useful.

In these experiments, we monitored fluorescently labeled ZapD. Due to their interaction, we found that its diffusion time increased at high FtsZ concentrations. The data presented in Supplementary Figure 2 shows ZapD in the presence of FtsZ-GDP (i.e. under non-polymerization conditions).

Was it possible to get a molecular weight estimate based on the diffusion time?

It is possible to estimate hydrodynamic volumes using the Stokes-Einstein equation if the diffusion coefficient of the diffusing particles is known, assuming that the particles are small and spherical. A molecular weight can then be estimated using a standard density of 1.35 g/cm3 (Fisher et all. Protein science 2009 DOI: 10.1110/ps.04688204). This estimate is heavily dependent on the shape of the diffusing particle, as we assume that our protein of interest here is far from a spherical shape due to the interaction through the flexible linker, the hydrodynamic volumes are overestimated. This overestimation then leads to a further overestimation of the molecular weight. In addition, for a more accurate estimation of the sizes and thus molecular weights for proteins, a modified model of the Stokes-Einstein equation is required (Tyn and Gusek Biotechnology and Bioengineering DOI: 10/1002/bit.260350402), where additional information about the shape of the diffusing particle is estimated by measuring the radius of gyration of the particle. These calculations are complex and beyond the scope of our manuscript.

Supple Fig 4:

Does FtsZ GTPase activity (without ZapD) also vary with KCl concentrations? It will be useful to comment on this in Supplementary Figure 4.

Yes, it has been previously reported that moderate concentration of KCl is optimal for FtsZ GTPase activity. We added a comment to the caption.

Page 6, line 42: short filament segments arranged nearly 'parallel' to each other Since FtsZ filaments are polar, it is better to rephrase as 'parallel or antiparallel'.

Corrected.

Page 7, line 41: cross linking of short 'FtsZ' filaments and not ZapD?

It was a typo. Corrected

Page 8: delete 'from above' in the title?

Corrected

The use of the phrases such as 'cross linking from the top'; 'binds to FtsZ from above' is vague. (Figure 5b legend; discussion page 10, line 18; page 8, line 26; page 12, line 27). Similarly labelling on a schematic figure on the use of vertical, diagonal/lateral will be useful for the readers.

We thank the reviewer for the suggestions to improve the understanding of our data. We have simplified them by renaming these interactions as vertical.

Page 13, lines 6 -10

Rather than an orientation of top or from the side, just the presence of multiple crosslinks along coaxial filaments suffices for a straight bundle. The average spacing will be more uniform in such a straight bundle compared to a toroid where there might be regions without ZapD. I do not find the data on an upward orientation convincing. ZapD binding need not be above to have the C-terminal ends of FtsZ pointing towards the membrane. On the other hand, having ZapD bind above is likely to occlude membrane binding of FtsZ?

The flexibility of the FtsZ linker suggests that ZapD can bind filaments oriented in different directions. In a cellular environment, FtsZ molecules interact with other division proteins that compete with ZapD for binding sites. This competition could prevent the membrane from occluding and instead create binding sites between the filaments, stabilizing them.

Page 11, lines 32 - 34: Please rephrase the sentence, with focus on the main point to be conveyed. Do the authors want to say that the 'Same molecule contributes to variability in spacing based on the number of connections formed.'

Thank you for your comment. We have rephrased the sentence for clarity.

Page 11: paragraphs 1,2, and 3 appears to convey similar, related ideas and are redundant. Could these be shortened further into one paragraph highlighting how the ratio leads to differences in higher order FtsZ organisation?

These paragraphs discuss different ideas, and it is better to keep them separate.

In the response to reviewers, page 19, point 5 (iii), it is given that 5000 FtsZ molecules correspond to 2/3rd of the total, while in the manuscript text, it is given as one-third. Please correct the response text/manuscript text accordingly. The numbers in the cited reference appears to suggest 1/3rd.

Yes, it was 1/3rd. Thanks for pointing that out. 

Fig 1b. Y-axis: Absorbance spelling has a typo.

Page 14, line 11: Healthcare ('h' missing)

Page 14, line 15: HCl, KCl (L should be in small letter)

Page15, line 18: 43 - 48K rpm (not Krpm)

Supple Fig 1 legend: line 5: 's' missing for species

Corrected.