Author response:

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

eLife assessment

In their valuable study, Chen et al. aim to define the neuronal role of HMMR, a microtubule-associated protein typically associated with cell division. Their findings suggest that HMMR is necessary for proper neuronal morphology and the generation of polymerizing microtubules within neurites, potentially by promoting the function of TPX2. While the study is recognized as a first step in deciphering the influence of HMMR on microtubule organization in neurons, reviewers note the current work has important gaps and would benefit from further exploration of the mechanism of microtubule stability by HMMR, the link between HMMR-mediated microtubule generation and morphogenesis, and the physiological implications of disrupting HMMR during neuronal morphogenesis.

Public Reviews:

Reviewer #1 (Public Review):

The microtubule cytoskeleton is essential for basic cell functions, enabling intracellular transport, and establishment of cell polarity and motility. Microtubule-associated proteins (MAPs) contribute to the regulation of microtubule dynamics and stability - mechanisms that are specifically important for the development and physiological function of neurons. Here, the authors aimed to elucidate the neuronal function of the MAP Hmmr, which they had previously identified in a quantitative study of the proteome associated with neuronal microtubules.

The authors conduct well-controlled experiments to demonstrate the localization of endogenous as well as exogenous Hmmr on microtubules within the soma as well as all neurites of hippocampal neurons. Functional analysis using gain- and loss-of-function approaches demonstrates that Hmmr levels are crucial for neuronal morphogenesis, as the length of both dendrites and axons decreases upon loss of Hmmr and increases upon Hmmr overexpression. In addition to length alterations, the branching pattern of neurites changes with Hmmr levels. To uncover the mechanism of how Hmmr influences neuronal morphology, the authors follow the lead that Hmmr overexpression induces looped microtubules in the soma, indicative of an increase in microtubule stability. Microtubule acetylation indeed decreases and increases with Hmmr LOF and GOF, respectively. Together with a rescue of nocodazole-induced microtubule destabilization by Hmmr GOF, these results argue that Hmmr regulates microtubule stability. Highlighted by the altered movement of a plus-end-associated protein, Hmmr also has an effect on the dynamic nature of microtubules. The authors present evidence suggesting that the nucleation frequency of neuronal microtubules depends on Hmmr's ability to recruit the microtubule nucleator Tpx2. Together, these data add novel insight into MAP-mediated regulation of microtubules as a prerequisite for neuronal morphogenesis. While the data shown support the author's conclusions, the study also has several weaknesses:

• The study appears incomplete as the initial proteomics analysis which is referenced as an entry into the study is not presented. This surely is the authors' choice, however, without presenting this data set, it would make more sense if the authors first showed the localization of Hmmr on neuronal microtubules and then started with the functional analysis.

The reviewer suggests moving the Hmmr localization data in front of the loss- and gain-of-function data because we did not present the proteomics data. However, we still believe placing the loss- and gain-of-function data in the beginning is the better arrangement. This is because it allows the audience to see the drastic changes on neuronal morphology when HMMR is depleted or overly abundant. It also provides a better linkage between HMMR’s localization on microtubules and its effect on the stability and dynamics of microtubules.

• Neurite branching is quantified, but the methods used are not consistent (normalized branch density vs. Sholl analysis) and there is no distinction between alterations of branching in dendrites vs. axons. This information should be added as it could prove informative with respect to the physiological function of Hmmr in neurite branching.

Sholl analysis is considered the gold standard in neurite branching analyses. However, in the knockdown experiment (Figure 1A~1E), HMMR-depleted neurons exhibited extremely short axons (<100 μm) and dendrites (<40 μm). Using Sholl analysis to assess the branching of these Hmmrdepleted neurons became unsuitable. That is why we used normalized branch density (Figure 1E) in the knockdown experiment and Sholl analysis (Figure 1J) in the overexpression experiment.

Regarding the branching difference between axons and dendrites, only axons exhibit branches at 4 DIV. Therefore, the branching analysis focuses on axons rather than on dendrites. We have revised the manuscript to clarify this.

• The authors show that altered Hmmr levels affect neurite branching and identify an effect on microtubule stability and dynamics as a molecular mechanism. However, how branching correlates with or is regulated by Hmmr-mediated microtubule dynamics is neither addressed experimentally nor discussed by the authors. The physiological significance of altered neuronal morphogenesis also lacks discussion.
• To discuss how branching correlates with or is regulated by HMMR-mediated microtubule dynamics, we have added the following paragraph into the Discussion section:

“It has been shown that compromising microtubule nucleation in neurons by SSNA1 mutant overexpression prevents proper axon branching (Basnet et al., 2018). Additionally, dendritic branching in Drosophila sensory neurons depends on the orientation of microtubule nucleation. Nucleation that results in an anterograde microtubule growth leads to increased branching, while nucleation that results in a retrograde microtubule growth leads to decreased branching (Yalgin et al., 2015). These results demonstrate the importance of microtubule nucleation on neurite branching. It is conceivable that overexpressing a microtubule nucleation promoting protein such as HMMR results in an increase of branching complexity.”

• In terms of discussing the physiological significance of altered neuronal morphogenesis. We have added the following paragraph to the Discussion section:

“Neurons are the communication units of the nervous system. The formation of their intricate shape is therefore crucial for the physiological function. Alterations in neuronal morphogenesis have a profound impact on how nerve cells communicate, leading to a variety of physiological consequences. These consequences include impaired neural circuit formation and function, compromised signal transmission between neurons, as well as altered anatomical structure of the CNS. Depending on the specific type and location of the morphogenetically altered neurons, the physiological consequences can include neurological disorders such as autism spectrum disorder (Berkel et al., 2012) and schizophrenia (Goo et al., 2023), as well as learning and memory deficits (Winkle et al., 2016). However, due to the involvement of HMMR on mitosis, most HMMR mutations are associated with familial cancers (based on ClinVar data).”

• Multiple times, the manuscript lacks a rationale for an experimental approach, choice of cell type, time points, regions of interest, etc. Also, a meaningful description of the methods and for how data were analyzed is missing, making the paper hard to read for someone not directly from the field.

We understand the reviewer’s comments regarding the lack of rationale for choosing the experimental approach, choice of cell type, time points, regions of interest, etc. As a result, we have added the rationales where appropriate to help readers from other fields to better understand the choice of cell type, time points, regions of interest, etc. A brief explanation is shown below:

• Approach and timing: We employed both electroporation (immediate but milder expression) and lipofectamine transfection (delayed but stronger expression). We prioritized knocking down HMMR early in development, so electroporation was used. For overexpression experiments, we chose lipofectamine which allows high protein expression level to be achieved.

• Cell selection: Hippocampal neurons were chosen in experiments that involve morphological quantification due to their homogeneous morphology. On the other hand, cortical neurons were selected in experiments that require large amounts of neurons and/or experiments where we want to demonstrate the universality of a proposed hypothesis.

• Regions of interest (ROIs): In our previous publication (Chen et al., 2017), it was discovered that a significant reduction of EB3 emanation frequency can be detected at the tip and the base of the neurite but not in the middle of the neurite in TPX2-depleted neurons. The reason for this difference is due to the presence of GTP-bound Ran GTPase (RanGTP) at the tip and the base of the neurite. Since RanGTP has also been shown to regulate the interaction between HMMR and TPX2 in the cell-free system (Scrofani et al., 2015), it is possible that the same phenomenon can be observed in HMMR-depleted neurons. This is why we examined those 3 ROIs in Figure 4.

Reviewer #2 (Public Review):

The mechanism of microtubule formation, stabilization, and organization in neurites is important for neuronal function. In this manuscript, the authors examine the phenotype of neurons following alteration in the level of the protein HMMR, a microtubule-associated protein with established roles in mitosis. Neurite morphology is measured as well as microtubule stability and dynamic parameters using standard assays. A binding partner of HMMR, TPX2, is localized. The results support a role for HMMR in neurons.

The work presented in this manuscript seeks to determine if a MAP called HMMR contributes to microtubule dynamics in neurons. Several steps, including validation of the RNAi, additional statistical analysis, use of cells at the same age in culture, and better documentation in figures, would increase the impact of the work.

In many places, the data can be improved which might make the story more convincing. As presented, the results show that HMMR is distributed as puncta on neurons with data coming from a single HMMR antibody, and some background staining that was not discussed. In the discussion the authors state that HMMR impacts microtubule stability, which was evaluated by the presence of post-translational modification and resistance to nocodazole; the data are suggestive but not entirely convincing. The discussion also states that HMMR increases the “amount” of growing microtubules which was measured as the frequency of comet appearance. The authors did not comment on how the number of growing microtubules results in the observed morphological changes.

We actually tested several HMMR antibodies, including E-19 (Santa Cruz, sc-16170), EPR4054 (Abcam, ab124729), and a variety of antibodies provided by Prof. Eva Turley. E-19 performed the best in immunofluorescence (IF) staining and knockdown validation. The other antibodies either failed to detect HMMR in IF staining or generate excessive background signal. We understand that the final images are produced using a single antibody. But since we meticulous validated this antibody and that the localization of overexpressed HMMR is consistent with the endogenous HMMR, we are very confident about our data generated using this single antibody.

We have added the following paragraph in the Discussion section to elucidate how the number of growing microtubules result in the observed morphological changes such as an increase of axon branches:

“It has been shown that compromising microtubule nucleation in neurons by SSNA1 mutant overexpression prevents proper axon branching (Basnet et al., 2018). Additionally, dendritic branching in Drosophila sensory neurons depends on the orientation of microtubule nucleation. Nucleation that results in an anterograde microtubule growth leads to increased branching, while nucleation that results in a retrograde microtubule growth leads to decreased branching (Yalgin et al., 2015). These results demonstrate the importance of microtubule nucleation on neurite branching. It is conceivable that overexpressing a microtubule nucleation promoting protein such as HMMR results in an increase of branching complexity.

Reviewer #1 (Recommendations for The Authors):

(1) The manuscript jumps extensively between main figures and supplementary figures. Please check whether parts of the supplement could be moved to the main figures.

We understand the frustration of moving back and forth between the main figures and supplementary figures. After examining the manuscript, we decided to combine Figure 2A with Figure S3.

(2) In Figure 1, total neurite length between days 3 and 4 DIV does not appear to change - can this be true?

Please check or else explain.

We carefully re-examined our raw data and found out the total neurite length of 4 DIV hippocampal neurons expressing non-targeting shRNA (Figure 1B) and that of 3 DIV hippocampal neurons expressing AcGFP (Figure 1G) are indeed very similar. The explanation is that the 3 DIV hippocampal neurons used for Figure 1G was cultured in low-density and in the presence of cortical neuron-conditioned neurobasal medium (as written in Methods, Neuron culture and transfection section). The low-density culture with minimal overlapping neurites allowed us to better quantify total neurite length, because neurons expressing AcGFP-mHMMR sprouted long and highly branched axons. However, the addition of cortical neuron-conditioned neurobasal medium promoted neurite elongation. This is the reason why the total neurite length of 4 DIV hippocampal neurons expressing non-targeting shRNA (Figure 1B) and that of 3 DIV hippocampal neurons expressing AcGFP (Figure 1G) is similar.

(3) Groen et al. have shown that Hmmr also bundles microtubules, a mechanism that surely is important for neuronal microtubules. Please discuss.

We thank the reviewer for pointing out that HMMR also bundles microtubules and have added this to our revised Discussion section:

“It has been shown that the Xenopus HMMR homolog XRHAMM bundles microtubules in vitro (Groen et al., 2004). In addition, deleting proteins which promote microtubule bundling (e.g., doublecortin knockout, MAP1B/MAP2 double knockout) leads to impaired neurite outgrowth (Bielas et al., 2007; Teng et al., 2001). These observations are consistent with our data that overexpressing HMMR leads to the increased axon and dendrite outgrowth, while depleting it results in the opposite phenotype (Figure 1).”

(4) Please explain why in Figure 4, cortical neurons were chosen for analysis and why and how the three different ROIs were picked.

To answer the question why we chose cortical neurons for the analyses in Figure 4, it will be important to explain why we used hippocampal neurons for other figures. Primary hippocampal neurons have a high homogeneity in terms of their morphology. This uniform morphology allows more consistent morphological quantification. Figure 4, however, does not involve morphological quantification. We are more confident to conclude that HMMR regulates microtubule dynamics if this effect can be detected in the relatively heterogeneous cortical neurons. These are the reasons why we chose to analyze cortical neurons in Figure 4.

In our previous publication (Chen et al., 2017), it was discovered that a significant reduction of EB3 emanation frequency can be detected at the tip and the base of the neurite but not in the middle of the neurite in TPX2-depleted neurons. The reason for this difference is due to the presence of GTP-bound Ran GTPase (RanGTP) at the tip of the neurite and in the soma. Since RanGTP has also been shown to regulate the interaction between HMMR and TPX2 in the cell-free system (Scrofani et al., 2015), it is possible that the same phenomenon can be observed in HMMR-depleted neurons. This was why we examined those 3 ROIs in Figure 4.

(5) Microtubule looping has been shown to occur in regions prior to branch formation (e.g. Dent et al. 2004). As the authors identify increased looping upon Hmmr GOF, this should be discussed.

We thank the reviewer for pointing out that microtubule looping occurs in regions of branch formation and have added this to our revised discussion:

“It is worth noting that the elevated level of HMMR increases the branching density of axons (Figure 1J) and promotes the formation of looped microtubules (Figure 3A). This is consistent with the observations that looped microtubules are often detected in regions of axon branch formation (Dent et al., 1999; Dent and Kalil, 2001; Purro et al., 2008).”

Reviewer #2 (Recommendations for The Authors):

(1) The work seeks to gain insight into microtubule behavior in neurons, an important issue.

(2) Several steps, including validation of the RNAi, additional statistical analysis, use of cells at the same age in culture, and better documentation in figures, would increase the impact of the work.

(3) Figure 1 documents the results of experiments in which the HMMR protein was depleted using shRNA. A western blot of cell extracts from control and depleted cells is needed to verify that the protein level is reduced; alternatively, documentation of the reduction in RNA levels in treated cells could be provided. Neurite, axon, and dendrite length and branch density are measured. The neurite length is in microns, and the axon length is normalized to 100% of the non-treated cells. Please use the same for measures for easier comparison. Looking at the images in Figure 1, the length of the dendrites does not look different in the examples shown, whereas the axon appears shorter. This impression is not supported by the quantification. Are representative images shown? Additionally, the authors should report the values for each replicate of the experiment and compare the three averages rather than comparison of lengths from all measurements. A related issue is that the dendrites do not look longer in panel F, following overexpression of HMMR. For examples of using averages of replicates see: https://pubmed.ncbi.nlm.nih.gov/32346721/

The reviewer mentioned that Western blot of cell extracts or RNA quantification from control and depleted cells are needed to verify that the protein level is reduced.

Unfortunately, these assays are extremely difficult to perform in primary neurons due to the low transfection efficiency. We believe that the consistent knockdown phenotype from 3 different shRNA sequences (Figure 1A-D) and the immunofluorescence staining in depleted primary neurons (Figure S2) are sufficient to confirm that HMMR level is reduced.

We revised Figure 1C, 1D, 1H, 1I so that axon and dendrite lengths are all in micron.

We selected another image for the non-targeting control in Figure 1A to better demonstrate the reduction of dendrite length when HMMR is knocked down.

We thank the reviewer for the suggestion of comparing the three average values rather than comparing all measurements. We have performed statistical analyses for all our data using the average values and revised the graphs accordingly. While the P-values changed, our conclusions remain the same.

We thank the reviewer for pointing out this discrepancy and have selected another image of the AcGFP control for Figure 1F to better demonstrate the increase of dendrite length when HMMR is overexpressed.

(4) Given the changes in neurite morphology, the authors examine the localization of endogenous and overexpressed. The supplemental figures (see S2 and S3) show evidence that HMMR is present in a punctate pattern by conventional immunofluorescence. This is reasonable evidence that the protein is in a linear pattern along cytoskeletal microtubules and that the signal is present in puncta. Please move this to the main text, perhaps replacing Figure 2A, which is low magnification and very hard to see the HMMR staining. Additionally, the level of overexpression of HMMR is not mentioned. Please address this; were cells with similar levels of overexpression selected? Did the result depend on the overexpression? A related issue is the DIV for the cells - some are examined earlier and some at later times; does this impact the results? Please provide information or perform experiments with consistent timing. For the immunofluorescence, were multiple antibodies tried to see if the result was the same with each? Were different fixations, in addition to methanol, utilized?

We have replaced Figure 2A with Figure S3 based on the reviewer’s suggestion.

In the HMMR overexpression experiments, we used HMMR antibody and immunofluorescence staining to confirm that the overexpression is achieved. However, we did not quantify to what extend HMMR was overexpressed.

We performed all the depletion experiments on 4 DIV to maximize knockdown efficiency and performed all the overexpression experiments on 3 DIV to prevent excessive axon fasciculation. Nonetheless, we examined the effect of HMMR depletion on neuronal morphology on 3 DIV. The trend of reduced total neurite length, axon length, and dendrite length can be observed, but no statistical significance can be detected. We also examined the effect of HMMR overexpression on neuronal morphology on 4 DIV and did observe an increase of total neurite length, axon length, and dendrite length. But the overlapping and bundled axons made reliable quantification extremely difficult.

We actually tested multiple HMMR antibodies, such as E-19 (Santa Cruz, sc-16170), EPR4054 (Abcam, ab124729), and a variety of antibodies provided by Prof. Eva Turley. E19 performed the best in immunofluorescence (IF) staining and knockdown validation. The other antibodies either failed to detect HMMR in IF staining or generate excessive background signal. We also tested various fixation methods, including 37°C formaldehyde fixation, -20°C methanol fixation, 37°C formaldehyde followed by -20°C methanol fixation. All fixation methods generated similar IF staining pattern using the E-19 antibody, but 3.7% formaldehyde fixation produced the highest signal.

(5) In Figure 2 C it is hard to see DAPI fluorescence. Are the white areas in the merge with bright cell nuclei? Is Figure 2C control or overexpressing cells? If this is endogenous, is there less signal in PLA compared with S4, which was in culture longer and is overexpressed prior to using PLA for detection?

The white areas in Figure 2C the reviewer mentioned are not cell nuclei, they are actually bubbles formed within the mounting medium.

HMMR detected in Figure 2C is endogenous. We did not quantitatively compare the PLA signals in Figure 2C and those in Figure S4. This is because the PLA signals in Figure 2C are generated using anti-HMMR (to detect endogenous HMMR) and anti-β-III-tubulin antibodies while those in Figure S4 are generated using anti-AcGFP (to detect overexpressed AcGFP-mHMMR) and anti-β-III-tubulin antibodies. Since the affinity of the two antibodies (i.e., anti-HMMR and anti-AcGFP) toward their antigens is different, comparing the PLA signals is not informative.

(6) The images of the endogenous HMMR (Fig S3) and the PLA with tubulin and HMMR antibodies are not the same (2C). The "dots" in PLA are widely separated; gauging from the marker bar length of 50 μm, the small clusters of dots are about 10 μm apart. In Figure S3, the puncta are much more closely spaced, appearing almost in a linear fashion along the microtubules. Enlarging the PLA image shows that each dot is very small - just a few pixels - please provide additional explanation including the minimal detection limit for the method, and why the images differ. If the standard immunofluorescence signal was enhanced, for example with the use of two secondaries, what is observed? Is the distribution of HMMR similar for both dendrites and axons? Microtubule polarity differs in these locations, so greater attention to this point seems of interest. There is a significant amount of punctate HMMR in the cytoplasm (or outside the cytoplasm?) in Figure S5; this is concerning. Please outline the cell edge for ease of visualization. What is the distribution of HMMR in a cell that has been treated with cold and/or nocodazole to disassemble the microtubules? is the signal lost?

The reasons images of the endogenous HMMR (Figure S3) and the PLA with tubulin and HMMR antibodies (Figure 2C) differ are due to the following reasons. o PLA utilizes two primary antibodies to target two different epitopes on HMMR and βIII-tubulin. It is conceivable that not every anti-HMMR antibody has the correct orientation and/or proximity (<40 nm) toward the anti-β-III-tubulin antibody to enable DNA amplification. This results in the shortage of PLA puncta compared to immunofluorescence signals.

• The creator of PLA has pointed out that in situ PLA is a method based upon equilibrium reactions and several enzymatic steps. Therefore, only a fraction of the inter-acting molecules is detected (Weibrecht et al., 2010).

We have not used signal enhancing immunofluorescence staining methods [e.g., using tertiary antibodies or tyramide signal amplification (TSA)] to detect HMMR. This is mainly because HMMR signal is strong enough to be detected using standard immunofluorescence staining.

Regarding the question “Is the distribution of HMMR similar for both dendrites and axons?” The reviewer raised a very important issue about the polarity difference of microtubules in axons (uniform) and dendrites (mixed). We were aware of such issue and very carefully examined the distribution and signal intensity of HMMR in axons vs dendrites. However, no differences were detected.

The reviewer mentioned that “there is a significant amount of punctate HMMR in the cytoplasm (or outside the cytoplasm?) in Figure S5; this is concerning. Please outline the cell edge for ease of visualization.” Instead of outlining the cell edge, we have selected another image to facilitate the visualization of HMMR signals. There are indeed HMMR signals outside the cell. However, these outside signals are usually weaker and smaller in size compared to those inside the cell.

After the examination of neurons expressing AcGFP-mHMMR with or without 100 nM nocodazole treatment, we did not notice any difference of AcGFP-mHMMR in distribution. We did not examine the distribution and signal intensity of the endogenous HMMR.

(7) To determine if HMMR alters microtubule stability, the authors examine the distribution of acetylated tubulin and resistance to nocodazole-induced microtubule disassembly. In Figure 3 please show immunofluorescence images of the acetylated tubulin staining, not just the ratio images; the color is not obviously different in the various panels shown. For statistical analysis, see the comment above for Figure 1. For the nocodazole experiment, a similar change in neurite length following drug treatment was observed (Figure 3H), for the experimental and control, even though the starting length was greater in the overexpressing cells. Please consider the possibility that in both cases the microtubules are only partially resistant to nocodazole and that HMMR is not changing the fraction of microtubules that are sensitive to the drug. The cells were treated at 3 DIV; the authors note that more stable microtubules accumulate with time; how does time in culture impact stability? Often, acute treatment with a high concentration of nocodazole is used to assay microtubule stability; here the authors used a low (nM) concentration for 2 days (chronic). Why not use a higher concentration (1-10 μM) for a shorter incubation? The data show that overexpression of HMMR results in curved, buckled microtubules are these microtubules more acetylated and/or retained after nocodazole treatment?

The reviewer suggested that we show immunofluorescence images of the acetylated tubulin staining, not just the ratio images. But we still believe showing the ratio images is the better approach. This is because the microtubules density can be different from neuron to neuron. Showing acetylated tubulin may provide a false impression when the overall microtubule density is higher or lower in a particular neuron. We realized that “16 colors” pseudo-color scheme has the cyan color at the lower intensity which can sometimes be confused with the white color at the higher intensity. Therefore, we changed the pseudocolor from “16 colors” to “fire” for Figure 3B and 3E to better visualize these images so that they appear more consistent with the quantitative data.

The reviewer raised a very good question regarding the possibility that HMMR is not changing the fraction of microtubules that are sensitive to nocodazole. We re-conducted the same experiment and used a series of different nocodazole concentrations. While the addition of nocodazole causes a concentration-dependent reduction of total neurite length in both AcGFP and AcGFP-mHMMR expressing neurons, there are subtle differences in the susceptibility of neurite length to the concentration of nocodazole. 1) 10 nM nocodazole treatment causes a significant reduction of neurite length in AcGFP expressing neurons, but not in AcGFP-mHMMR expressing neurons. This result indicates that AcGFP-mHMMR expression increases the tolerance of neurite elongation toward 10 nM nocodazole treatment. 2) 50 nM and 100 nM nocodazole treatment exhibits no statistical significance in AcGFP expressing neurons, suggesting that 50 nM nocodazole has reached maximal effectiveness. In AcGFP-mHMMR expressing neurons, 100 nM nocodazole further reduces the neurite length compared to the 50 nM group. These results argue against the possibility that HMMR does not change the fraction of microtubules that are sensitive to nocodazole. We have revised Figure 3H accordingly.

The reviewer asked why we did not use the acute nocodazole treatment (μM concentration) to assess the effect of Hmmr on microtubule stability. This is because we used the neurite length as an indicator for microtubule stability. That is why the chronic treatment was chosen to produce a more detectable effect on neurite length.

The reviewer asked whether the looped microtubules caused by HMMR overexpression are more acetylated and/or nocodazole resistant. While we do not have direct evidence to answer the reviewer’s question, we can deduce the answer from our observations. We noticed that looped microtubules are only present when HMMR is highly expressed (i.e., using lipofection to introduce HMMR-expressing plasmid) but not when HMMR is mildly expressed (i.e., using electroporation to introduce HMMR-expressing plasmid). From these observations, we can conclude that HMMR is more abundantly present on looped microtubules. Since HMMR overexpression leads to higher microtubule acetylation (Figure 3E), looped microtubules which contains more HMMR are most likely to be more acetylated.

(8) An additional measure of microtubule dynamics is to measure the growth of microtubules using a live cell marker for microtubule plus ends. Such experiments were performed, using tagged EB3. The images are rather fuzzy. Parameters of microtubule dynamics were measured at three locations - is there data that the authors can cite about any differences in dynamics in control cells at these locations? They look very similar, so it is not clear why the different locations were used. It is not possible to learn much from the kymographs which look similar for all panels; I would remove these unless they can be changed or labeled to help the reader. Data is presented for three shRNA reagents. No data are presented to document the extent to which the protein is depleted with these reagents. This should be fixed. Alternatively, an RNAi pool could be utilized. Is there a control for off-target effects? For the analysis were all the comets used to generate the average values? What about a comparison of the average of each trial - not each comet?

In our previous publication (Chen et al., 2017), it was discovered that a significant reduction of EB3 emanation frequency can be detected at the tip and the base of the neurite but not in the middle of the neurite in TPX2-depleted neurons. The reason for this difference is due to the presence of RanGTP at the tip and the base of the neurite. Since RanGTP has also been shown to regulate the interaction between HMMR and TPX2 in the cell-free system (Scrofani et al., 2015), it is possible that the same phenomenon can be observed in HMMR-depleted neurons. This is why we examined those 3 ROIs in Figure 4.

We notice that photobleaching causes the EB3-mCherry signal to diminish at later time points, which made it difficult to observe the differences amongst kymographs. In the revised Figure 4B and 4D, we removed the second half of all the kymographs to make the differences more obvious.

The reviewer mentioned that there are no data documenting the extent to which the protein is depleted with the shRNAs. These data are shown in Figure S2, in which we quantified the HMMR protein level in the soma and along the neurite in neurons expressing different shRNA molecules.

The reviewer asked whether there is a control for off-target effects. The answer is yes. We performed the rescue experiment to control for off-target effects, which is shown in Figure S1.

We revised Figure 4 so that the dynamic properties of EB3 are quantified using the average of each experimental repetition.

(9) In a final experiment, the authors examine the distribution of TPX2, a binding partner of HMMR. Include a standard immunofluorescence in addition to PLA to illustrate the distribution of TPX2. The quantification used was the inter puncta distance; please quantify the signal in control and treated cells.

The reviewer asked us to include a standard immunofluorescence staining to illustrate the distribution of TPX2. We have done that in our previous publication (Chen et al., 2017) and TPX2 localizes primarily to the centrosome (https://www.nature.com/articles/srep42297/figures/2). In order to enhance the weak signal of TPX2 along the neurite, we actually needed to use PLA in that publication (https://www.nature.com/articles/srep42297/figures/3).

Proximity ligation assay (PLA) generates fluorescent signals based on a local enzymatic reaction which catalyzes the amplification of a specific DNA sequence that can then be detected using a red fluorescent probe. Because this enzymatic reaction is not linear, the amount of amplified DNA nor the intensity of the fluorescence does not correlate with the strength of the interaction (Soderberg et al., 2006). As a result, quantification of PLA is typically done by counting the number of fluorescent puncta per unit area or by calculating the area containing fluorescent signal (not signal intensity) per unit area in the case that PLA signals are too strong and coalesced. That is why our quantification is based on the distance between PLA fluorescent puncta, not the fluorescent signal intensity.

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Teng, J., Y. Takei, A. Harada, T. Nakata, J. Chen, and N. Hirokawa. 2001. Synergistic effects of MAP2 and MAP1B knockout in neuronal migration, dendritic outgrowth, and microtubule organization. J. Cell Biol. 155:65-76.

Weibrecht, I., K.J. Leuchowius, C.M. Clausson, T. Conze, M. Jarvius, W.M. Howell, M. Kamali-Moghaddam, and O. Soderberg. 2010. Proximity ligation assays: a recent addition to the proteomics toolbox. Expert Rev Proteomics. 7:401-409.

Winkle, C.C., R.H. Olsen, H. Kim, S.S. Moy, J. Song, and S.L. Gupton. 2016. Trim9 Deletion Alters the Morphogenesis of Developing and Adult-Born Hippocampal Neurons and Impairs Spatial Learning and Memory. J. Neurosci. 36:49404958.

Yalgin, C., S. Ebrahimi, C. Delandre, L.F. Yoong, S. Akimoto, H. Tran, R. Amikura, R. Spokony, B. Torben-Nielsen, K.P. White, and A.W. Moore. 2015. Centrosomin represses dendrite branching by orienting microtubule nucleation. Nat. Neurosci. 18:1437-1445.

Reviewer #1 (Public Review):

The microtubule cytoskeleton is essential for basic cell functions, enabling intracellular transport, and establishment of cell polarity and motility. Microtubule-associated proteins (MAPs) contribute to the regulation of microtubule dynamics and stability - mechanisms that are specifically important for the development and physiological function of neurons. Here, the authors aimed to elucidate the neuronal function of the MAP Hmmr, which they had previously identified in a (yet unpublished) quantitative study of the proteome associated with neuronal microtubules. The authors conduct well-controlled experiments to demonstrate the localization of endogenous as well as exogenous Hmmr on microtubules within the soma as well as all neurites of hippocampal neurons. Functional analysis using gain- and loss-of-function approaches demonstrates that Hmmr levels are crucial for neuronal morphogenesis, as the length of both dendrites and axons decreases upon loss of Hmmr and increases upon Hmmr overexpression. In addition to length alterations, the branching pattern of neurites changes with Hmmr levels. To uncover the mechanism of how Hmmr influences neuronal morphology, the authors follow the lead that Hmmr overexpression induces looped microtubules in the soma, indicative of an increase in microtubule stability. Microtubule acetylation indeed decreases and increases with Hmmr LOF and GOF, respectively. Together with a rescue of nocodazole-induced microtubule destabilization by Hmmr GOF, these results argue that Hmmr regulates microtubule stability. Highlighted by the altered movement of a plus-end-associated protein, Hmmr also has an effect on the dynamic nature of microtubules. The authors present evidence suggesting that the nucleation frequency of neuronal microtubules depends on Hmmr's ability to recruit the microtubule nucleator Tpx2. The authors discuss how branching may be regulated by Hmmr-mediated microtubule dynamics and speculate about the physiological significance of altered neuronal morphogenesis. Together, their work adds novel insight into MAP-mediated regulation of microtubules as a prerequisite for neuronal morphogenesis.

eLife assessment

In their valuable study, Chen et al. investigate the neuronal role of HMMR, a microtubule-associated protein typically associated with cell division. Their findings indicate that HMMR is necessary for proper neuronal morphology and the generation of polymerizing microtubules within neurites, potentially by promoting the function of TPX2. This solid body of work is the first step in deciphering the influence of a mitotic microtubule-associated protein in organizing microtubules in neurons and will be of interest to the neurobiology and cytoskeleton fields.

Reviewer #2 (Public Review):

The mechanism of microtubule formation, stabilization, and organization in neurites is important for neuronal function. In this manuscript, the authors examine the phenotype of neurons following alteration in the level of the protein HMMR, a microtubule-associated protein with established roles in mitosis. Neurite morphology is measured as well as microtubule stability and dynamic parameters using standard assays. A binding partner of HMMR, TPX2, is localized. The results support a role for HMMR in microtubule stabilization in neurons.

The results show that HMMR is distributed as puncta on neurons using standard immunofluorescence and PLA. Depletion of HMMR reduced neurite length and extent of branching; reduced post-translational acetylation of neurite microtubules. Conversely, overexpression of HMMR increased resistance to nocodazole. The parameters of microtubule dynamics were also impacted by reduction or overexpression of HMMR. The authors discuss the possibility HMMR regulates neurite morphological changes via regulation of microtubule nucleation and dynamics.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The authors set up a pipeline for automated high-throughput single-molecule fluorescence imaging (htSMT) in living cells and analysis of molecular dynamics

Strengths:

htSMT reveals information on the diffusion and bound fraction of molecules, dose-response curves, relative estimates of binding rates, and temporal changes of parameters. It enables the screening of thousands of compounds in a reasonable time and proves to be more sensitive and faster than classical cell-growth assays. If the function of a compound is coupled to the mobility of the protein of interest, or affects an interaction partner, which modulates the mobility of the protein of interest, htSMT allows identifying the modulator and getting the first indication of the mechanism of action or interaction networks, which can be a starting point for more in-depth analysis.

Weaknesses:

While elegantly showcasing the power of high-throughput measurements, the authors disclose little information on their microscope setup and analysis procedures. Thus, reproduction by other scientists is limited. Moreover, a critical discussion about the limits of the approach in determining dynamic parameters, the mechanism of action of compounds, and network reconstruction for the protein of interest is missing. In addition, automated imaging and analysis procedures require implementing sensitive measures to assure data and analysis quality, but a description of such measures is missing.

The reviewer rightly highlights both the power and complexity in high throughput assay systems, and as such the authors have spent significant effort in first developing quality control checks to support screening. We discuss some of these as part of the description and characterization of the platform. We added additional details into the manuscript to help clarify. The implementation of our workflow for image acquisition, processing and analysis relies heavily on the specifics of our lab hardware and software infrastructure. We have added additional details to the text, particularly in the Methods section, and believe we have added enough information that our results can be reproduced using the suite of tools that already exist for single molecule tracking.

The reviewer also points out that all assays have limitations, and these have not been clearly identified as part of our discussion of the htSMT platform. We have also added some comments on the limitations of the current system and our approach.

Reviewer #2 (Public Review):

Summary:

McSwiggen et al present a high throughput platform for SPT that allows them to identify pharmaceutics interactions with the diffusional behavior of receptors and in turn to identify potent new ligands and cellular mechanisms. The manuscript is well written, it provides a solid new mentor and a proper experimental foundation

Strengths:

The method capitalizes and extends to existing high throughput toolboxes and is directly applied to multiple receptors and ligands. The outcomes are important and relevant for society. 10^6 cells and >400 ligands per is a significant achievement.

The method can detect functionally relevant changes in transcription factor dynamics and accurately differentiate the ligand/target specificity directly within the cellular environment. This will be instrumental in screening libraries of compounds to identify starting points for the development of new therapeutics. Identifying hitherto unknown networks of biochemical signaling pathways will propel the field of single-particle live cell and quantitative microscopy in the area of diagnostics. The manuscript is well-written and clearly conveys its message.

Weaknesses:

There are a few elements, that if rectified would improve the claims of the manuscript.

The authors claim that they measure receptor dynamics. In essence, their readout is a variation in diffusional behavior that correlates to ligand binding. While ligand binding can result in altered dynamics or /and shift in conformational equilibrium, SPT is not recording directly protein structural dynamics, but their effect on diffusion. They should correct and elaborate on this.

This is an excellent clarifying question, and we have tried to make it more explicit in the text. The reviewer is absolutely correct; we’re not using SPT to directly measure protein structural dynamics, but rather the interactions a given protein makes with other macromolecules within the cell. So when an SHR binds to ligand it adopts conformations that promote association with DNA and other protein-protein interactions relevant to transcription. This is distinct from assays that directly measure conformational changes of the protein.

L 148 What do the authors mean 'No correlation between diffusion and monomeric protein size was observed, highlighting the differences between cellular protein dynamics versus purified systems'. This is not justified by data here or literature reference. How do the authors know these are individual molecules? Intensity distributions or single bleaching steps should be presented.

The point we were trying to make is that the relative molecular weights for the monomer protein (138 kDa for Halo-AR, 102 kDa for ER-Halo, 122 kDa for Halo-GR, and 135 kDa for Halo-PR) is uncorrelated with its apparent free diffusion coefficient. Were we to make this measurement on purified protein in buffer, where diffusion is well described by the Stokes Einstein equation, one would expect to see monomer size and diffusion related. We’ve clarified this point in the manuscript.

Along the same lines, the data in Figs 2 and 4 show that not only the immobile fraction is increased but also that the diffusion coefficient of the fast-moving (attributed to free) is reduced. The authors mention this and show an extended Fig 5 but do not provide an explanation.

This is an area where there is still more work to do in understanding the estrogen receptor and other SHRs. As the reviewer says, we see not only an increase in chromatin binding but also a decrease in the diffusion coefficient of the “free” population. A potential explanation is that this is a greater prevalence of freely-diffusing homodimers of the receptor, or other protein-protein interactions (14-3-3, P300, CBP, etc) that can occur after ligand binding. Nothing in our bioactive compound screen shed light on this in particular, and so we can only speculate and have refrained from drawing further conclusions in the text.

How do potential transient ligand binding and the time-dependent heterogeneity in motion (see comment above) contribute to this? Also, in line 216 the authors write "with no evidence" of transient diffusive states. How do they define transient diffusive states? While there are toolboxes to directly extract the existence and abundance of these either by HMM analysis or temporal segmentation, the authors do not discuss or use them.

Throughout the analysis in this work, we consider all of tracks with a 2-second FOV as representative of a single underlying population and have not looked at changes in dynamics within a single movie. As we show in the supplemental figures we added (see Figure 3, figure supplement 1), this appears to be a reasonable assumption, at least in the cases we’ve encountered in this manuscript. For experiments involving changes in dynamics over time, these are experiments where we’ve added compound simultaneous with imaging and collect many 2-second FOVs in sequence to monitor changes in ER dynamics. In this case when we refer to “transient states,” we are pointing out that we don’t observe any new states in the State Array diagram that exist in early time points but disappear at later time point.

The reviewer suggests track-level analysis methods like hidden Markov models or variational Bayesian approaches which have been used previously in the single molecule community. These are very powerful techniques, provided the trajectories are long (typically 100s of frames). In the case of molecules that diffuse quickly and can diffuse out of the focal plane, we don’t have the luxury of such long trajectories. This was demonstrated previously (Hansen et al 2017, Heckert el al 2022) and so we’ve adopted the State Array approach to inferring state occupations from short trajectories. As the reviewer rightly points out, this approach potentially loses information about state transitions or changes over time, but as of now we are not aware of any robust methods that work on short trajectories.

The authors discuss the methods for extracting kinetic information of ligand binding by diffusion. They should consider the temporal segmentation of heterogenous diffusion. There are numerous methods published in journals or BioRxiv based on analytical or deep learning tools to perform temporal segmentation. This could elevate their analysis of Kon and Koff.

We’re aware of a number of approaches for analyzing both high framerate SMT as well as long exposure residence time imaging. As we say above, we’re not aware of any methods that have been demonstrated to work robustly on short trajectories aside from the approaches we’ve taken. Similarly, for residence time imaging there are published approaches, but we’re not aware of any that would offer new insight into the experiments in this study. If the reviewer has specific suggestions for analytical approaches that we’re not aware of we would happily consider them.

Reviewer #3 (Public Review):

Summary:

The authors aim to demonstrate the effectiveness of their developed methodology, which utilizes super-resolution microscopy and single-molecule tracking in live cells on a high-throughput scale. Their study focuses on measuring the diffusion state of a molecule target, the estrogen receptor, in both ligand-bound and unbound forms in live cells. By showcasing the ability to screen 5067 compounds and measure the diffusive state of the estrogen receptor for each compound in live cells, they illustrate the capability and power of their methodology.

Strengths:

Readers are well introduced to the principles in the initial stages of the manuscript with highly convincing video examples. The methods and metrics used (fbound) are robust. The authors demonstrate high reproducibility of their screening method (R2=0.92). They also showcase the great sensitivity of their method in predicting the proliferation/viability state of cells (R2=0.84). The outcome of the screen is sound, with multiple compounds clustering identified in line with known estrogen receptor biology.

Weaknesses:

• Potential overstatement on the relationship of low diffusion state of ER bound to compound and chromatin state without any work on chromatin level.

We appreciate the reviewers caution in over-interpreting the relationship between an increase in the slowest diffusing states that we observe by SMT and bona fide engagement with chromatin. In the case of the estrogen receptor there is strong precedent in the literature showing increases in chromatin binding and chromatin accessibility (as measured by ChIP-seq and ATAC-seq) upon treatment with either estradiol or SERM/Ds. Taken together with the RNA-seq, we felt it reasonable to assume all the trajectories with a diffusion coefficient less that 0.1 µm2/sec were chromatin bound.

• Could the authors clarify if the identified lead compound effects are novel at any level?

Most of the compounds we characterize in the manuscript have not previously been tested in an SMT assay, but many are known to functionally impact the ER or other SHRs based on other biochemical and functional assays. We have not described here any completely novel ER-interacting compounds, but to our knowledge this is the first systematic investigation of a protein showing that both direct and indirect perturbation can be inferred by observing the protein’s motion. Especially for the HSP90 inhibitors, the observation that inhibiting this complex would so dramatically increase ER chromatin-binding as opposed to increasing the speed of the free population is counterintuitive and novel.

• More video example cases on the final lead compounds identified would be a good addition to the current data package.

Reviewer #1 (Recommendations For The Authors):

General:

• More information on the microscope setup and analysis procedures should be given. Since custom code is used for automated image registration, spot detection, tracking, and analysis of dynamics, this code should be made publicly available.

Results:

• line 97: more details about the robotic system and automatic imaging, imaging modalities, and data analysis procedures should be given directly in the text.

Additional information added to text and methods

• line 100: we generated three U2OS cell lines --> how?

Additional information added to text and methods

• line 101: ectopically expressing HaloTag fused proteins --> how much overexpression did cells show?

The L30 promoter tends to produce fairly low expression levels. The same approach was used for all ectopic expression plasmids, and for the SHRs the expression levels were all comparable to endogenous levels. We have not checked this for H2B, Caax and free Halo but given that the necessary dye concentration to achieve similar spot densities is within a 10-fold range for all constructs, its reasonable to say that those clonal cell lines will also have modest Halotag expression.

• line 107: Single-molecule trajectories measured in these cell lines yielded the expected diffusion coefficients --> how was data analysis performed?

Additional information added to text and methods

• line 109: how was the localization error determined?

Additional information added to text and methods

• line 155: define occupation-weighted average diffusion coefficient.

Additional information added to text and methods

• line 157: with 34% bound in basal conditions and 87% bound after estradiol treatment  contradicts figure 2b, where the bound fraction is up to 50% after estradiol treatment.

Line 157 is the absolute fraction bound, figure 2b is change in fbound

• line 205: Figure 2c is missing.

Fixed

• line 215: within minutes --> how was this data set obtained? which time bins were taken?

Additional information added to text and methods

• line 216: with no evidence of transient diffusive states  What is meant by transient diffusive state? It seems all time points have a diffusive component, which decreases over time.

Additional information added to text and methods

The diffusive peak decreases, the bound peak increases but no other peaks emerge during that time (e.g. neither super fast nor super slow)

• line 225: it seems that fbound of GDC-0810 and GDC-0927 are rather similar in FRAP experiments, please comment, how was FRAP done?

FRAP is in the methods section. The curves and recovery times are quite distinct, is the reviewer looking at

• line 285: reproducibly: how often was this repeated?

Information added to the manuscript

• line 285: it would be necessary to name all of the compounds that were tested, e.g. with an ID number in the graph and a table. This also refers to extended data 7 and 8.

Additional supplemental file with the list of bioactive compounds tested will be included.

• line 290/1: what is meant by vendor-provided annotation was poorly defined?

Additional information added to text and methods. Specifically, the “other” category is the most common category, and it includes both compounds with unknown targets/functions as well as compound where the target and pathway are reasonably well documented. Hence, we applied our own analysis to better understand the list of active compounds.

Figures:

• fig. 2-6: detailed statistics are missing (number of measured cells, repetitions, etc.).

We have added clarifying information, including an “experiment design and sample size” section in the Methods.

• fig. 3: the authors need to give a list with details about the 5067 compounds tested,

Additional supplemental file with the list of bioactive compounds tested will be included.

• extended data 1c: time axis does not correspond to the 1.5s of imaging in the text, results line 127.

Axes fixed

• extended data 3: panel c and d are mislabeled.

Panel labels fixed

Methods:

• line 746: HILO microscope: the authors need to explain how they can get such large fields of view using HILO

Additional details added to the materials and methods. The combination of the power of the lasers, the size of the incident beam out of the fiber optic coupling device and the sCMOS camera are the biggest components that enable detection over a larger field of view.

• line 761: it is common practice to publish the analysis code. Since the authors wrote their own code, they should publish it

Our software contains proprietary information that we cannot yet release publicly. Comparable results can be achieved with HILO data using publicly-available tools like utrack. State Arrays code is distributed and the parameters used are listed in the M&M.

Reviewer #2 (Recommendations For The Authors):

The writing and presentation are coherent, concise, and easy to follow.

The authors should consider justifying the following:

Why is 1.5s imaging time selected? Topological and ligand variations may last significantly longer than this. The authors should present at least for one condition the same effect images for longer.

Related to the similar comment above, we added a figure examining the jump length distribution as a function of frame. Over the 6 seconds of data collection the jump length distribution is unchanged, suggesting it is reasonable to consider all the trajectories within an FOV as representative of the same underlying dynamical states.

The authors miss the k test or T test in their graphs.

We chose to apply the Kurskal-Wallis test in the context of the bioactive screen to assess whether a grouping of compounds based on their presumed cellular target was significantly different from the control even when individual compounds might not by themselves raise to significance. In this case many of the pathway inhibitors are subtle and not necessarily obvious in their difference. In the other cases throughout the manuscript, whether two conditions are statistically distinguishable is rarely in question and of far less importance to the conclusions in the manuscript than the magnitude of the difference. We’ve added statistical tests where appropriate.

The overall integrated area of Fig 4a appears to reduce upon ligand addition. Data appear normalized but the authors should also add N (number of molecules) on top of the graphs.

While the integrated area may appear to decrease, all State Array analysis is performed by first randomly sampling 10,000 trajectories from the assay well and inferring state distribution on those 10,000. This has been clarified in the figure legend and in the Methods.

Minor

Extended Figure 3 legend c, d appear swapped and incorrectly named in the text.

Panel labels fixed

L 197 but this appears not to BE a general feature of SHRs (maybe missing Be).

Error fixed

L205 authors refer to Figure 2c, which does not exist.

Panel reference fixed

Reviewer #3 (Recommendations For The Authors):

Among minor issues:

In Figure 1B, if the authors could specify how they discriminate the specific cell lines from the mixed context, it would enhance clarity. Could they perform additional immunofluorescence to understand how the assignment is determined? Alternatively, could they also show the case with isolated cell lines in an unmixed context?

Immunofluorescence would be a challenge given that there is not a good epitope to distinguish the three ectopically-expressed genes from each other or from endogenous proteins in the case of H2B and CaaX. We are really reliant on the single cell dynamics to determine the likely cell identity. That said, we’ve added graphs of a number of individual cell State Arrays from the same data graphed in 1A which support the notion that it’s reasonable to assume a cells identity given the observed dynamics.

In Extended Figure 2F: possibly a CHip-Seq experiment would be more directly qualified to state the effect of ER ligand on ER ability to bind chromatin.

This is true. Presumably ER that is competent at activating transcription of ER-responsive genes is also capable of binding DNA. ChIP would be the more direct measure, but would not address whether the protein was functional. We chose to balance these measuring these two aspects of ER biology by pairing dynamics with the end-point transcription readout.

In Figure 3: A representation with plate-by-plate orientation along the x-axis, with controls included in each plate, would be more appropriate to reflect the consistency of the controls used in the assay across different plates. Currently, all controls are pooled in one location, and we cannot appreciate how the controls vary from plate to plate.

Figure added to the supplement

Also in this figure, a general workflow of the screen down to segmentation/analysis would be a great add-on.

New figure added to the supplement and reflected in the textual description of the platform

In Extended Figures 3B and C an add-on of the positive and negative control would make the figure more convincing.

Addressed as part of figure added to the supplement

Is there any description of compound leads identified that is novel in nature in relation to impact on ER, and if so could it be stated more clearly in the text as novel finding?

To our knowledge, the impact of HSP inhibition in increasing ER-chromatin association has never been described, neither has the link between inhibition post-translation modifying enzymes like the CDKs or mTOR and ER dynamics ever been described. We added clarifying text to the manuscript

eLife assessment

This work presents an important technological advance, in the form of a high throughput platform for Single Particle Tracking allowing us to measure millions of cells and thousands of compounds per day. Analysis of the diffusional behaviour of fluorescently-tagged targets permits the identification of, and differentiation between, small molecules that bind directly or affect the target indirectly. The methodology and metrics employed are compelling, leading to the identification of multiple compounds that effectively change the diffusive state of the estrogen receptor, the POC target of the study.

Reviewer #1 (Public Review):

Summary:

The authors set up a pipeline for automated high-through single-molecule fluorescence imaging (htSMT) in living cells and analysis of molecular dynamics.

Strengths:

htSMT reveals information on the diffusion and bound fraction of molecules, dose-response curves, relative estimates on binding rates, and temporal changes of parameters. It enables the screening of thousands of compounds in a reasonable time and proves to be more sensitive and faster than classical cell-growth assays. If the function of a compound is coupled to the mobility of the protein of interest or affects an interaction partner, which modulates the mobility of the protein of interest, htSMT allows identifying the modulator and getting the first indication on the mechanism of action or interaction networks, which can be a starting point for more in-depth analysis. The authors describe their automated imaging and analysis procedures as well as the measures taken to assure data and analysis quality.

Weaknesses:

While elegantly showcasing the power of high-throughput measurements, htSMT relies on a sophisticated robot-based workflow and several microscopes for parallel imaging, thus limiting wide-spread application of htSMT by other scientists.

Reviewer #3 (Public Review):

Summary:

The authors aim to demonstrate the effectiveness of their developed methodology, which utilizes super-resolution microscopy and single-molecule tracking in live cells on a high-throughput scale. Their study focuses on measuring the diffusion state of a molecule target, the estrogen receptor, in both ligand-bound and unbound forms in live cells. By showcasing the ability to screen 5067 compounds and measure the diffusive state of the estrogen receptor for each compound in live cells, they illustrate the capability and power of their methodology.

Readers are well introduced to the principles in the initial stages of the manuscript with highly convincing video examples. The methods and metrics used (fbound) are robust. The authors demonstrate high reproducibility of their screening method (R2=0.92). They also showcase the great sensitivity of their method in predicting the proliferation/viability state of cells (R2=0.84). The outcome of the screen is sound, with multiple compounds clustering identified in line with known estrogen receptor biology.

Author response:

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

Reviewer #1:

Detection of early-stage colorectal cancer is of great importance. Recently, both laboratory scientists and clinicians have reported different exosomal biomarkers to identify colorectal cancer patients.

Here, the authors exhibited a full RNA landscape for plasma exosomes of 60 individuals, including 31 colorectal cancer (CRC) patients, 19 advanced adenoma (AA) patients, and 10 noncancerous controls. RNAs with high fold change, high absolute abundance, and various module attribution were used to construct RT-qPCR-based RNA models for CRC and AA detection.

Overall, this is a well-performed proof-of-concept study to highlight exosomal RNAs as potential biomarkers of early-stage colorectal cancer and its precancerous lesions.

Thank you for your careful evaluation and valuable suggestions, which have provided valuable guidance for the improvement of our paper. In response to your feedback, we have implemented the following improvements.

(1) Depicting the full RNA landscape of circulating exosomes is still quite challenging. The authors annotated 58,333 RNA species in exosomes, most of which were lncRNAs, but the authors do not explain how they characterized those RNAs.

Author response and action taken: Thanks for your comments. In the Supplementary Methods section titled "Identification of mRNAs and lncRNAs", we have provided a comprehensive explanation on the characterization of mRNAs and lncRNAs to address the concerns you raised. Characterization of long-chain RNAs is a great challenge. For lncRNA analysis, the transcriptome was assembled using the Cufflinks and Scripture based on the reads mapped to the reference genome. The assembled transcripts were annotated using the Cuffcompare program from the Cufflinks package. The unknown transcripts were used to screen for putative lncRNAs.

(2) The authors tested their models in a medium size population of 124 individuals, which is not enough to obtain an accurate evaluation of the specificity and sensitivity of the biomarkers proposed here. External validation would be required.

Author response and action taken: Thanks for your comments. We fully acknowledge the significance of external validations in the evaluation of diagnostic model performance. Unfortunately, as a pilot study, we currently do not have the conditions for a multicenter investigation. To mitigate result bias and overfitting effects, we implemented a rigorous variable selection strategy and enhanced model stability through 10-fold cross-validation. In the meantime, we will persist in our efforts to elevate the quality of our research and seek additional resources for external validation in future studies.

Reviewer #2:

The authors present an important study on the potential of small extracellular vesicle (sEV)-derived RNAs as biomarkers for the early detection of colorectal cancer (CRC) and precancerous adenoma (AA). The authors provide a detailed analysis of the RNA landscape of sEVs isolated from participants, identifying differentially expressed sEV-RNAs associated with T1a stage CRC and AA compared to normal controls. The paper further categorises these sEV-RNAs into modules and constructs a 60-gene model that successfully distinguishes CRC/AA from NC samples. The authors also validate their findings using RT-qPCR and propose an optimised classifier with high specificity and sensitivity. Additionally, the authors discuss the potential of sEV-RNAs in understanding CRC carcinogenesis and suggest that a comprehensive biomarker panel combining sEV-RNAs and proteins could be promising for identifying both early and advanced CRC patients. Overall, the study provides valuable insights into the potential clinical application of sEV-RNAs in liquid biopsy for the early detection of CRC and AA.

Major strengths:

(1) Comprehensive sEV RNA profiling: The study provides a valuable dataset of the whole-transcriptomic profile of circulating sEVs, including miRNA, mRNA, and lncRNA. This approach adds to the understanding of sEV-RNAs' role in CRC carcinogenesis and facilitates the discovery of potential biomarkers.

(2) Detection of early-stage CRC and AA: The developed 60-gene t-SNE model successfully differentiated T1a stage CRC/AA from normal controls with high specificity and sensitivity, indicating the potential of sEV-RNAs as diagnostic markers for early-stage colorectal lesions.

(3) Independent validation cohort: The study combines RNA-seq, RT-qPCR, and modelling algorithms to select and validate candidate sEV-RNAs, maximising the performance of the developed RNA signature. The comparison of different algorithms and consideration of other factors enhance the robustness of the findings.

Thank you for your careful evaluation and valuable suggestions. These comments have been highly valuable for the performance evaluation and clinical applications of our work. In response to your feedback, we have implemented the following improvements.

(1). Lack of analysis on T1-only patients in the validation cohort: While the study identifies key sEV-RNAs associated with T1a stage CRC and AA, the validation cohort is only half of the patients in T1(25 out of 49). It would be better to do an analysis using only the T1 patients in the validation cohort, so the conclusion is not affected by the T2-T3 patients.

Author response and action taken: Thanks for your comments. This feedback is essential for ensuring consistency in the results with our previous findings. In this context, we revalidated various diagnostic panels using exclusively Stage I patients (Figure 7—figure supplement 2). To minimize the potential overfitting effect due to the reduction in sample size after partitioning, we implemented a 10-fold cross-validation for each panel and these panels exhibit promising performance in Stage I colorectal cancer (CRC) patients.

Author response image 1.

The ROC analysis of different sEV-RNA signatures in the prediction of Stage I CRC patients by different algorithms (a: 6-gene panel; b: 7-gene panel; c: 8-gene panel; d: 9-gene panel).

(2). Lack of performance analysis across different demographic and tumor pathology factors listed in Supplementary Table 12. It's important to know if the sEV-RNAs identified in the study work better/worse in different age/sex/tumor size/Yamada subtypes etc.

Author response and action taken: Thanks for your comments. This feedback will be immensely beneficial for clinical diagnosis. Similarly, cross-validation was performed in this section. We assessed the discriminative effects of CRC on NC, taking into account different age groups, genders, tumor sizes, and anatomical locations (Figure 7—figure supplement 3). Overall, these sEV RNA panels perform better in individuals under the age of 55 and in female patients. There is no significant difference in discriminative effects across different tumor sizes. Compared to rectal cancer, the discriminative effects are better in colon cancer.

Author response image 2.

The ROC analysis of different sEV-RNA signatures for predicting CRC patients using the Lasso regression algorithm in different clinical parameters (ab: age; cd: gender; ef: tumor size; gh: anatomical position).

eLife assessment

This study presents a useful description of RNA in extracellular vesicles (EV-RNAs) and highlights the potential to develop biomarkers for the early detection of colorectal cancer (CRC) and precancerous adenoma (AA). The data were analysed using overall solid methodology and would benefit from further validation of predicted lncRNAs and biomarker validation at each stage of CRC/AA to evaluate the potential application to early detection of CRC and AA.

Joint Public Review:

Detection of early-stage colorectal cancer is of great importance. Laboratory scientists and clinicians have reported different exosomal biomarkers to identify colorectal cancer patients. This is a proof-of-principle study of whether exosomal RNAs, and particularly predicted lncRNAs, potential biomarkers of early-stage colorectal cancer and its precancerous lesions.

Strengths:

The study provides a valuable dataset of the whole-transcriptomic profile of circulating sEVs, including miRNA, mRNA, and lncRNA. This approach adds to the understanding of sEV-RNAs' role in CRC carcinogenesis and facilitates the discovery of potential biomarkers.

The developed 60-gene t-SNE model successfully differentiated T1a stage CRC/AA from normal controls with high specificity and sensitivity, indicating the potential of sEV-RNAs as diagnostic markers for early-stage colorectal lesions.

The study combines RNA-seq, RT-qPCR, and modelling algorithms to select and validate candidate sEV-RNAs, maximising the performance of the developed RNA signature. The comparison of different algorithms and consideration of other factors enhance the robustness of the findings.

Weaknesses:

Validation in larger cohorts would be required to establish as biomarkers, and to demonstrate whether the predicted lncRNAs implicated in these biomarkers are indeed present, and whether they are robustly predictive/prognostic.

Author response:

Following our first submission last August, we have received positive feedback on the relevance and interesting aspect of our work. However, a functional validation was requested to strengthen our findings. Specifically, the rejection was motivated as such:

“Although the authors presented certain pieces of evidence from hMSC cell line experiments and mouse subcutaneous implantation studies, indicating the involvement of elements from eECM in endogenous repair, the study is not of sufficient depth. Additional validation of the findings within a context such as bone repair/regeneration is lacking.”

We have addressed the raised concern by implementing the following major changes:

(1) An ex vivo Chorioallantoic Membrane (CAM) assay was performed, to functionally assess the angiogenic potential of VEGF-edited ECMs. We confirmed the capacity of engineered ECMs to promote vessel formation, in line with ectopic in vivo assessment in mouse. Findings are implemented as Figure 2A, 2B and 2C, and as Supplementary figure 2A.

(2) The regenerative potential of RUNX2-edited ECMs was evaluated in a rat osteochondral defect model. The model was selected in order to assess both the potential of our engineered ECMs to participate in cartilage and/or bone regeneration. In short, our findings demonstrate that RUNX2edited eECMs significantly enhanced cartilage regeneration. In contrast, the non-edited ECMs exhibiting clear sign of cartilage hypertrophy- could not promote joint repair in the model. Findings are implemented in an entirely new figure panel (Figure 5), with Supplementary Figure 5, Table 1 and supplementary Table 1.

In addition, beyond the suggested functional validation of our eECMs we have also compiled new data reinforcing our previous claim. This is now implemented as:

• Figure 1G: Immunofluorescence stainings of engineered cartilage ECMs generated by the MSOD-B and MSOD-BΔV1 lines, respectively. These stainings confirmed strong content in collagen type I and collagen type X in the tissues, while vascular endothelial growth factor (VEGF) is poorly detectable in the edited MSOD-BΔV1 ECMs.

• Figure 3I: A 2D osteogenic differentiation assessment of the MSOD-B and MSOD-BΔR1 cells was performed in vitro. We could confirm the functional impact of RUNX2 knock-down on the osteogenic potential of MSOD-BΔR1 cells, as no mineralized matrix was deposited by the cells.

• Figure 3J: We implemented a gene expression profile analysis of MSOD-B and MSOD-BΔR1, stimulated or not with pro-osteogenic medium for three weeks. In line, with the results presented in Figure 3I, we could confirm an impairment in the expression of key osteoblastic-associated genes (RUNX2, COLX, ALPL) in MSOD-BΔR1 cells.

Altogether, we have compiled additional in vitro and in vivo evidence on the impact of CRISPR/Cas9 knock-out leading to eECMS customized in composition and function. Our findings significantly consolidate and strengthen our previous observations.

eLife assessment

The study presents a potentially useful approach to genetically modify cells to produce extracellular matrices with altered compositions. The evidence supporting the authors' conclusions regarding the chondrogenicity of lyophilized constructs is considered incomplete, as the study does not adequately demonstrate the formation of a histologically identifiable cartilaginous matrix. The study also lacks several significant details and does not have sufficient power to support the conclusions.

Reviewer #1 (Public Review):

Summary:

The authors aimed to modify the characteristics of the extracellular matrix (ECM) produced by immortalized mesenchymal stem cells (MSCs) by employing the CRISPR/Cas9 system to knock out specific genes. Initially, they established VEGF-KO cell lines, demonstrating that these cells retained chondrogenic and angiogenic properties. Additionally, lyophilized carriage tissues produced by these cells exhibited retained osteogenic properties.

Subsequently, the authors established RUNX2-KO cell lines, which exhibited reduced COLX expression during chondrogenic differentiation and notably diminished osteogenic properties in vitro. Transplantation of lyophilized carriage tissues produced by RUNX2-KO cell lines into osteochondral defects in rat knee joints resulted in the regeneration of articular cartilage tissues as well as bone tissues, a phenomenon not observed with tissues derived from parental cells. This suggests that gene-edited MSCs represent a valuable cell source for producing ECM with enhanced quality.

Strengths:

The enhanced cartilage regeneration observed with ECM derived from RUNX2-KO cells supports the authors' strategy of creating gene-edited MSCs capable of producing ECM with superior quality. Immortalized cell lines offer a limitless source of off-the-shelf material for tissue regeneration.

Weaknesses:

Most data align with anticipated outcomes, offering limited novelty to advance scientific understanding. Methodologically, the chondrogenic differentiation properties of immortalized MSCs appeared deficient, evidenced by Safranin-O staining of 3D tissues and histological findings lacking robust evidence for endochondral differentiation. This presents a critical limitation, particularly as authors propose the implantation of cartilage tissues for in vivo experiments. Instead, the bulk of data stemmed from type I collagen scaffold with factors produced by MSCs stimulated by TGFβ.

The rationale behind establishing VEGF-KO cell lines remains unclear. What specific outcomes did the authors anticipate from this modification?

Insufficient depth was given to elucidate the disparity in osteogenic properties between those observed in ectopic bone formation and those observed in transplantation into osteochondral defects. While the regeneration of articular cartilage in RUNX2-KO ECM presents intriguing results, the study lacked an exploration into underlying mechanisms, such as histological analyses at earlier time points.

Reviewer #2 (Public Review):

The manuscript submitted by Sujeethkumar et al. describes an alternative approach to skeletal tissue repair using extracellular matrix (ECM) deposited by genetically modified mesenchymal stromal/stem cells. Here, they generate a loss of function mutations in VEGF or RUNX2 in a BMP2-overexpressing MSC line and define the differences in the resulting tissue-engineered constructs following seeding onto a type I collagen matrix in vitro, and following lyophilization and subcutaneous and orthotopic implantation into mice and rats. Some strengths of this manuscript are the establishment of a platform by which modifications in cell-derived ECM can be evaluated both in vitro and in vivo, the demonstration that genetic modification of cells results in complexity of in vitro cell-derived ECM that elicits quantifiable results, and the admirable goal to improve endogenous cartilage repair. However, I recommend the authors clarify their conclusions and add more information regarding reproducibility, which was one limitation of primary-cell-derived ECMs.

Overcoming the limitations of native/autologous/allogeneic ECMs such as complete decellularization and reduction of batch-to-batch variability was not specifically addressed in the data provided herein. For the maintenance of ECM organization and complexity following lyophilization, evidence of complete decellularization was not addressed, but could be easily evaluated using polarized light microscopy and quantification of human DNA for example in constructs pre and post-lyophilization. It would be ideal to see minimization of batch-to-batch variability using this approach, as mitigation of using a sole cell line is likely not sufficient (considering that the sole cell line-derived Matrigel does exhibit batch-to-batch and manufacturer-to-manufacturer variability).

I recommend adding details regarding experimental design and outcomes not initially considered. Inter- and intra-experimental reproducibility was not adequately addressed. The size of in vitro-derived cartilage pellets was not quantified, and it is not clear that more than one independent 'differentiation' was performed from each gene-edited MSC line to generate in vitro replicates and constructs that were implanted in vivo.

The use of descriptive language in describing conclusions may mislead the reader and should be modified accordingly throughout the manuscript. For example, although this reviewer agrees with the comparative statements made by the authors regarding parental and gene-edited MSC lines, non-quantifiable terms such as 'frank' 'superior' (example, line 242) are inappropriate and should rather be discussed in terms of significance. Another example is 'rich-collagenous matrix,' which was not substantiated by uniform immunostaining for type II collagen (line 189).

I have similar recommendations regarding conclusive statements from the rat implantation model, which was appropriately used for the purpose of evaluating the response of native skeletal cells to the different cell-derived ECMs. Interpretations of these results should be described with more accuracy. For example, increased TRAP staining does not indicate reduced active bone formation (line 237). Many would not conclude that GAGs were retained in the RUNX2-KO line graft subchondral region based on the histology. Quantification of % chondral regeneration using histology is not accurate as it is greatly influenced by the location in the defect from which the section was taken. Chondral regeneration is usually semi-quantified from gross observations of the cartilage surface immediately following excision. The statements regarding integration (example line 290) are not founded by histological evidence, which should show high magnification of the periphery of the graft adjacent to the native tissue.

Reviewer #3 (Public Review):

Summary:

In this study, the authors have started off using an immortalized human cell line and then gene-edited it to decrease the levels of VEGF1 (in order to influence vascularization), and the levels of Runx2 (to decrease chondro/osteogenesis). They first transplanted these cells with a collagen scaffold. The modified cells showed a decrease in vascularization when VEGF1 was decreased, and suggested an increase in cartilage formation.

In another study, the matrix generated by these cells was subsequently remodeled into a bone marrow organ. When RUNX2 was decreased, the cells did not mineralize in vitro, and their matrices expressed types I and II collagen but not type X collagen in vitro, in comparison with unedited cells. In vivo, the author claims that remodeling of the matrices into bone was somewhat inhibited. Lastly, they utilized matrices generated by RUNX2 edited cells to regenerate chondro-osteal defects. They suggest that the edited cells regenerated cartilage in comparison with unedited cells.

Strengths:

-The notion that inducing changes in the ECM by genetically editing the cells is a novel one, as it has long been thought that ECM composition influences cell activity.

-If successful, it may be possible to make off-the-shelf ECMS to carry out different types of tissue repair.

Weaknesses:

-The authors have not generated histologically identifiable cartilage or bone in their transplants of the cells with a type I scaffold.

-In many cases, they did not generate histologically identifiable cartilage with their cell-free-edited scaffold. They did generate small amounts of bone but this is most likely due to BMPs that were synthesized by the cells and trapped in the matrix.

-There is a great deal of missing detail in the manuscript.

-The in vivo study is underpowered, the results are not well documented pictorially, and are not convincing.

-Given the fact that they have genetically modified cells, they could have done analyses of ECM components to determine what was different between the lines, both at the transcriptome and the protein level. Consequently, the study is purely descriptive and does not provide any mechanistic understanding of what mixture of matrix components and growth factors works best for cartilage or bone. But this presupposes that they actually induced the formation of bona fide cartilage, at least.

eLife assessment

This important study, which presents novel data on variation in sperm whale communication, contributes to a richer understanding of the social transmission of vocal styles across neighbouring clans. The evidence is solid but could be further improved with some clarification of the specialized measurements and terms used, particularly for comparisons to other taxa. This research will be of interest for bioacoustics and animal communication specialists, particularly those working on social learning and culture.

Reviewer #1 (Public Review):

Summary:

This manuscript presents evidence of 'vocal style' in sperm whale vocal clans. Vocal style was defined as specific patterns in the way that rhythmic codas were produced, providing a fine-scale means of comparing coda variations. Vocal style effectively distinguished clans similar to the way in which vocal repertoires are typically employed. For non-identity codas, vocal style was found to be more similar among clans with more geographic overlap. This suggests the presence of social transmission across sympatric clans while maintaining clan vocal identity.

Strengths:

This is a well-executed study that contributes exciting new insights into cultural vocal learning in sperm whales. The methodology is sound and appropriate for the research question, building on previous work and ground-truthing much of their theories. The use of the Dominica dataset to validate their method lends strength to the concept of vocal style and its application more broadly to the Pacific dataset. The results are framed well in the context of previous works and clearly explain what novel insights the results provide to the current understanding of sperm whale vocal clans. The discussion does an overall great job of outlining why horizontal social learning is the best explanation for the results found.

Weaknesses:

The primary issues with the manuscript are in the technical nature of the writing and a lack of clarity at times with certain terminology. For example, several tree figures are presented and 'distance' between trees is key to the results, yet 'distance' is not clearly defined in a way for someone unfamiliar with Markov chains to understand. However, these are issues that can easily be dealt with through minor revisions with a view towards making the manuscript more accessible to a general audience.

I also feel that the discussion could focus a bit more on the broader implications - specifically what the developed methods and results might imply about cultural transmission in other species. This is specifically mentioned in the abstract but not really delved into in detail during the discussion.

Reviewer #2 (Public Review):

Summary:

The current article presents a new type of analytical approach to the sequential organisation of whale coda units.

Strengths:

The detailed description of the internal temporal structure of whale codas is something that has been thus far lacking.

Weaknesses:

It is unclear how the insight gained from these analyses differs or adds to the voluminous available literature on how codas varies between whale groups and populations. It provides new details, but what new aspects have been learned, or what features of variation seem to be only revealed by this new approach?<br /> The theoretical basis and concepts of the paper are problematical and indeed, hamper potentially the insights into whale communication that the methods could offer. Some aspects of the results are also overstated.

Reviewer #3 (Public Review):

Summary:

The study presented by Leitao et al., represents an important advancement in comprehending the social learning processes of sperm whales across various communicative and socio-cultural contexts. The authors introduce the concept of "vocal style" as an addition to the previously established notion of "vocal repertoire," thereby enhancing our understanding of sperm whale vocal identity.

Strengths:

A key finding of this research is the correlation between the similarity of clan vocal styles for non-ID codas and spatial overlap (while no change occurs for ID codas), suggesting that social learning plays a crucial role in shaping symbolic cultural boundaries among sperm whale populations. This work holds great appeal for researchers interested in animal cultures and communication. It is poised to attract a broad audience, including scholars studying animal communication and social learning processes across diverse species, particularly cetaceans.

Weaknesses:

In terms of terminology, while the authors use the term "saying" to describe whale vocalizations, it may be more conservative to employ terms like "vocalize" or "whale speech" throughout the manuscript. This approach aligns with the distinction between human speech and other forms of animal communication, as outlined in prior research (Hockett, 1960; Cheney & Seyfarth, 1998; Hauser et al., 2002; Pinker & Jackendoff, 2005; Tomasello, 2010).

Author response:

We thank the reviewers for their positive assessments and constructive feedback.

In light of their comments, we will aim to improve the explanation of the methods and interpretation of results, as well as their relation to well-established literature in this research area.

The major contributions of our work are threefold:

• First, we introduce a novel way of analyzing codas that specifically targets subcoda structures by considering inter-click intervals within codas in terms of transition probabilities. By describing codas’ click patterns via Variable Length Markov Chains, we do not need to consider codas in their entirety, but we can detect coda subunits.This enables a new dimension for quantitatively comparing differences among various individuals, social units, and clans; which we term ‘vocal style’.

• Using this approach, we reinforce findings from past research, including the idea that identity codas function as symbolic markers of vocal clan identity (Hersh et al., 2022; Sharma et al., 2024). More importantly, we offer new insights into the function of non-identity codas, which comprise the majority of coda types produced by sperm whales but have been largely uncharacterized. 

• Our work reveals that non-identity coda vocal styles are more similar for spatially overlapped clans, and suggests that this similarity in style may be maintained by social learning across clan boundaries. This opens up a paradigm shift in our understanding of between-clan acoustic interactions.

From a broader perspective, our work builds on two well-established research areas: the form and function of sperm whale codas, and statistical generative models, specifically Variable Length Markov Chains on finite data spaces. Our methods, results, and interpretations are grounded in theories and concepts from these fields.

For clarity, we will ensure that our terminology aligns with field standards and existing research. We will clearly introduce each key theory or concept at first mention and justify its relevance. In particular, we will clarify the definition and meaning of the distance between subcoda trees for a general audience. We agree with the reviewers’ comments on the broader implications and will refine our work accordingly.

eLife assessment

This important study highlights the role of SLAM-SAP signaling in shaping innate-like γδ T cell subsets, providing compelling evidence for the importance of SLAM-SAP in immune system regulation, and the potential implications of the findings for tumor surveillance and infectious disease management. The work will be of broad interest to immunologists.

Reviewer #1 (Public Review):

Summary:

In this study, the authors advance their previous findings on the role of the SLAM-SAP signaling pathway in the development and function of multiple innate-like gamma-delta T-cell subsets. Using a high throughput single-cell proteogenomics approach, the authors uncover SAP-dependent developmental checkpoints, and the role of SAP signaling in regulating the diversion of γδ T cells into the αβ T cell developmental pathway. Finally, the authors define TRGV4/TRAV13-4(DV7)-expressing T cells as a novel, SAP-dependent Vγ4 γδT1 subset.

Strengths:

This study furthers our understanding of the importance and complexity of the SLAM-SAP signaling pathway not only in the development of innate-like γδ T cells but also in how it potentially balances the γδ/αβ T cell lineage commitment. Additionally, this study reveals the role of SAP-dependent events in the generation of γδ TCR repertoire.

The conclusions of the study are supported by well-thought-out experiments and compelling data.

Weaknesses:

No major weaknesses in the study were identified.

Reviewer #2 (Public Review):

Summary:

Mistri et al explore the role of SLAM-SAP signaling in the developmental programming of innate-like gd T cell subsets. Using proteo-genomics, they determined that abrogation of SLAM-SAP signaling altered that programming, reducing some IL-17-producing subsets, including a novel Vγ4 γδT1 subset, and diverting gdTCR-expressing precursors to the ab fate. Altogether, this is a very thorough, thoughtfully interpreted study that adds significantly to our understanding of the contribution of the SLAM-SAP pathway to lineage specification. A particularly interesting element is the role of SLAM-SAP in preventing gd17 progenitors from switching fates and adopting the ab fate.

One thing to keep in mind in assessing the ultimate fate of the "ab wannabe cells" is that mechanisms exist to silence the gd TCR as cells differentiate to the DP stage and so their presence as diverted DP cells may not be evident by staining for gdTCR expression - and will only be evident transcriptomically.

Strengths:

This is an exceedingly well-designed and thorough study that significantly enriches our understanding of gd T cell development.

Weaknesses:

There are no major weaknesses identified by this reviewer.

Author response:

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

eLife assessment

Both reviewers positively received the manuscript, in general. The agreement was that the manuscript presented valuable findings, using solid techniques and approaches, that shed additional light into how the canine distemper virus hemagglutinin might engage cellular receptors and how that engagement impacts host tropism. While both reviewers appreciated the X-ray crystallographic data, they also felt that the AFM experiments could have been performed at a higher standard and that the interpretation of the results ensuing from those AFM experiments could have been explained more thoroughly and in simpler terms. An additional missed opportunity of the current manuscript is the lack of comparison of the crystal structure to that of the already published cryo-EM structure, for context.

Thank you very much for constructive comments of the editor and reviewers. Following your comments, we have changed the text related to the AFM experiments with simpler terms as follows.

“When CDV-H was loaded onto a mica substrate and scanned with a cantilever to acquire images of attached molecules, the CDV-H dimer was observed as two globules clustered together in most cases, but sometimes, each domain moved independently (Fig. 7B and Supplementary Movie). Time-course analysis of the dynamics of the representative CDV-H dimer showed that CDV-H could adopt both associated and dissociated forms (Fig. 7C). The distances between the domains were calculated by measuring those between the centers of mass of each domain. Finally, the distribution of distances between each head domain in the CDV-H dimers showed approximately 15 nm as a major peak (Fig. 7D). This is a reasonable length for the linker between the head domain dimers.” in Page 11, Lines 8-17.

With regards to the structural comparison between cryo-EM structure published in Proc. Natl. Acad. Sci. U. S. A. (2023) 120, e2208866120 and our crystal structure, we have compared these structures for Cα on page 6 and added the following text. “A recent cryo-EM structure of the wild-type CDV-H ectodomain revealed that the head dimer is located on one side of the stalk region in solution (Proc. Natl. Acad. Sci. U. S. A. (2023) 120, e2208866120)” in Page 14, Lines 22-24.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Fukuhara, Maenaka, and colleagues report a crystal structure of the canine distemper virus (CDV) attachment hemagglutinin protein globular domain. The structure shows a dimeric organization of the viral protein and describes the detailed amino-acid side chain interactions between the two protomers. The authors also use their best judgement to comment on predicted sites for the two cellular receptors - Nectin-4 and SLAM - and thus speculate on the CDV host tropism. A complementary AFM study suggests a breathing movement at the hemagglutinin dimer interface.

Strengths:

The study of CDV and related Paramyxoviruses is significant for human/animal health and is very timely. The crystallographic data seem to be of good quality.

Thank you very much for the constructive comment of the reviewer.

Weaknesses:

While the recent CDV hemagglutinin cryo-EM structure is mentioned, it is not compared to the present crystal structure, and thus the context of the present study is poorly justified. Additionally, the results of the AFM experiment are not unexpected. Indeed, other paramyxoviral RBP/G proteins also show movement at the protomer interface.

Thank you very much for constructive comments of the reviewer. When we submitted our manuscript to e-life, cryo-EM structure just published in Proc. Natl. Acad. Sci. U. S. A. (2023) 120, e2208866120 a week ago was not able to be available. Following the comment of the reviewer, we have added the text about the structural comparison between the cryo-EM structure and our crystal structure. We also have changed the text related to the AFM experiments to tone down the movement of the protomer interfaceas follows.

“This observation raises the possibility that each head domain of CDV-H also dissociates and moves flexibly, as shown in the structure of Nipah virus (NiV)-G protein, previously (Science (2022) 375, 1373–1378).” in Page 11, Lines 4-6.

Reviewer #2 (Public Review):

Summary:

The authors solved the crystal structure of CDV H-protein head domain at 3,2 A resolution to better understand the detailed mechanism of membrane fusion triggering. The structure clearly showed that the orientation of the H monomers in the homodimer was similar to that of measles virus H and different from other paramyxoviruses. The authors used the available co-crystal strictures of the closely related measles virus H structures with the SLAM and Nectin4 receptors to map the receptor binding site on CDV H. The authors also confirmed which N-linked sites were glycosylated in the CDV H protein and showed that both wildtype and vaccine strains of CDV H have the same glycosylation pattern. The authors documented that the glycans cover a vast majority of the H surface while leaving the receptor binding site exposed, which may in part explain the long-term success of measles virus and CDV vaccines. Finally, the authors used HS-AFM to visualize the real-time dynamic characteristics of CDV-H under physiological conditions. This analysis indicated that homodimers may dissociate into monomers, which has implications for the model of fusion triggering.

The structural data and analysis were thorough and well-presented. However, the HS-AFM data, while very exciting, was not presented in a manner that could be easily grasped by readers of this manuscript. I have some suggestions for improvement.

(1) The authors claim their structure is very similar to the recently published croy-EM structure of CDV H. Can the authors provide us with a quantitative assessment of this statement?

Thank you very much for constructive comments of the reviewer. When we submitted our manuscript to e-life, cryo-EM structure just published in Proc. Natl. Acad. Sci. U. S. A. (2023) 120, e2208866120 a week ago was not able to be available. Following the comment of the reviewer, we have added the text about the structural comparison between the cryo-EM structure and our crystal structure. We also have changed the text related to the AFM experiments to tone down the movement of the protomer interface as follows.

“This observation raises the possibility that each head domain of CDV-H also dissociates and moves flexibly, as shown in the structure of Nipah virus (NiV)-G protein, previously (Science (2022) 375, 1373–1378).” in Page 11, Lines 4-6.

(2) The results for the HS-AFM are difficult to follow and it is not clear how the authors came to their conclusions. Can the authors better explain this data and justify their conclusions based on it?

Thank you very much for constructive comments of the reviewer. Following your comments, we have changed the text related to the AFM experiments with simpler terms as follows.

“When CDV-H was loaded onto a mica substrate and scanned with a cantilever to acquire images of attached molecules, the CDV-H dimer was observed as two globules clustered together in most cases, but sometimes, each domain moved independently (Fig. 7B and Supplementary Movie). Time-course analysis of the dynamics of the representative CDV-H dimer showed that CDV-H could adopt both associated and dissociated forms (Fig. 7C). The distances between the domains were calculated by measuring those between the centers of mass of each domain. Finally, the distribution of distances between each head domain in the CDV-H dimers showed approximately 15 nm as a major peak (Fig. 7D). This is a reasonable length for the linker between the head domain dimers.” in Page 11, Lines 8-17.

(3) The fusion triggering model in Figure 8 is ambiguous as to when H-F interactions are occurring and when they may be disrupted. The authors should clarify this point in their model.

Thank you very much for constructive comments of the reviewer. Following your comments, we have changed the Figure 8 and its legend.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) AFM experiments with SLAM or Nectin-4 immobilized on the cantilever would be much more informative.

Thank you very much for the constructive comment of the reviewer. We will try this experiment in the next paper.

(2) The authors should compare their crystal structure to that of the reported cryo-EM structure.

With regards to the structural comparison between cryo-EM structure published in Proc. Natl. Acad. Sci. U. S. A. (2023) 120, e2208866120 and our crystal structure, we have added the text.

(3) Figure 1D - why does the beta2 MG negative control have such a high SPR signal?

Thank you very much for the constructive comment of the reviewer. The immobilization levels for b 2-microglobulin (beta2 MG), CDV-OP-H and CDV-5VD-H were similar, 1204.7 RU, 1235.7 RU, and 1504.5 RU, respectively. We applied relatively high concentrations (5 mM) of dNectin4 and hNectin4 onto the chip to determine low-affinity dissociation constants. Then, the signals for beta2 MG (negative control) were high. In other SPR experiments for cell surface receptors, such high signals for beta2 MG were often observed in our previous paper, Kuroki et al., J. Immunol. 2019 Dec 15;203(12):3386-3394. doi: 10.4049/jimmunol.1900562. Therefore, we think that these SPR signals are not unusual.

(4) Figure 1C - please indicate the Ve volume for the peak and add in Ve for standard.

Thank you very much for the constructive comment of the reviewer. We have indicated the Ve volume for the peak and added in Ve for standard in Figure 1C.

(5) The authors mention that one of the chains in the asymmetric unit was better resolved than the other. Please show regions of the atomic model fit regions of the electron density to convince the reader of the quality of your data.

Thank you very much for the constructive comment of the reviewer. We have added new Supplementary figure 2 for comparison of electron density maps of chains A and B.

(6) Table 2 indicates that the difference between Rw and Rf values is larger than 5% which indicates slight overfitting during refinement. Please provide details of your refinement strategy and attempt simulated annealing as a strategy to reduce this delta.

Thank you very much for the constructive comment of the reviewer. We further introduced TLS and NCS parameters for the refinement. Consequently, the R/Rfree factors became 0.2645/0.3092. Simulated annealing had been already carried out. All the refinement statistics in the table 2 are updated.

Reviewer #2 (Recommendations For The Authors):

(1) The authors' fusion triggering model was difficult to follow. For example, this sentence was difficult to understand: "The other possible models may include the monomer-dimer-tetramer transition facilitated by receptor binding for the fusion."

Thank you very much for the constructive comment of the reviewer. Following your comments, we have removed the above sentences and have added the detail mechanism of the proposed model in Discussion. Furthermore, we have changed the Figure 8 and its legend for readers to understand more clearly.

(2) Figure 5A is not called out in the main text.

Thank you very much for the constructive comment of the reviewer. Following your comments, we have added the text as follows.

“the crystal structure of MeV-H in complex with hNectin-4 showed that the H-SLAM interaction consists of three main sites (Fig. 5A) (Nat. Struct. Mol. Biol. (2013) 20, 67–72).” in Page 11, Lines 4-6.

(3) Page 9, Line 4: interspaces? Perhaps interphases.

Thank you very much for the constructive comment of the reviewer. We have changed the term “interspaces” to “internal spaces”.

(4) Page 12, penultimate line: The authors mention "epitopes for anti-MeV-H Abs." Do they mean anti-CDV-H Abs?

Thank you very much for the constructive comment of the reviewer. Following your comments, we have changed the “anti-MeV-H Abs” to “anti-morbillivirus H neutralizing antibodies”.

(5) The paper will benefit from an English language editor to help clarify what the authors are trying to convey.

Thank you very much for the constructive comment of the reviewer.

We have asked a English proof reading company to check.

eLife assessment

The manuscript presents valuable findings, using solid techniques and approaches, that shed additional light into how the canine distemper virus (CDV) hemagglutinin might engage cellular receptors and how that engagement impacts host tropism. The structural data and their analysis were thorough and well-presented. The HS-AFM data, which indicate that homodimers may dissociate into monomers - and thus have significant implications for the model of fusion triggering - are very exciting, but require further validation, perhaps by alternate approaches, to bolster the current molecular model of the CDV fusion triggering.

Reviewer #2 (Public Review):

The authors solved the crystal structure of CDV H-protein head domain at 3,2 A resolution to better understand the detailed mechanism of membrane fusion triggering. The structure clearly showed that the orientation of the H monomers in the homodimer was similar to that of measles virus H and different from other paramyxoviruses. The authors used the available co-crystal strictures of the closely related measles virus H structures with the SLAM and Nectin4 receptors to map the receptor binding site on CDV H. The authors also confirmed which N-linked sites were glycosylated in the CDV H protein and showed that both wildtype and vaccine strains of CDV H have the same glycosylation pattern. The authors documented that the glycans cover a vast majority of the H surface while leaving the receptor binding site exposed, which may in part explain the long-term success of measles virus and CDV vaccines. Finally, the authors used HS-AFM to visualize the real-time dynamic characteristics of CDV-H under physiological conditions. This analysis indicated that homodimers may dissociate into monomers, which has implications for the model of fusion triggering.

The structural data and analysis were thorough and well-presented. The HS-AFM data, while very exciting, needs to be further validated, perhaps by alternate approaches to further support the authors' model describing the molecular dynamics of fusion triggering.

Reviewer #2 (Public Review):

Summary:

The manuscript by Djebar et al investigated the role and the underlying mechanism of the ciliary transition zone protein Rpgrip1l in zebrafish spinal alignment. They showed that rpgrip1l mutant zebrafish develop a nearly full penetrance of body curvature at juvenile stages. The mutant fish have cilia defects associated with ventricular dilations and loss of the Reissner fibers. Scoliosis onset and progression are also strongly associated with astrogliosis and neuroinflammation, and anti-inflammatory drug treatment prevents scoliosis in mutant zebrafish, suggesting a novel pathogenic mechanism for human idiopathic scoliosis. This study is quite comprehensive with high-quality data, and the manuscript is well written, providing important information on how the ciliary transition zone protein functions in maintaining the zebrafish body axis straightness.

Strengths:

Very clear and comprehensive analysis of the mutant zebrafish.

Weaknesses:

(1) In Figures 1D-G, magnified high-resolution pictures are required to show there are indeed no vertebral malformations.

(2) Are the transcriptome data and proteomic data consistent? Consistent targets in both analyses should be highlighted.

(3) What is the role of Anxa2 in neuroinflammation? Is increased Anxa2 expression in rpgrip1l mutant zebrafish reduced after anti-inflammatory drug treatment? What is the expression level of anxa2 in cep290 mutant zebrafish?

(4) More background about Rpgrip1l should be provided in the introduction, particularly the past studies of the mammalian homolog of Rpgrip11, if there are any.

(5) Is there any human disease associated with Rpgrip1l? Do these patients have scoliosis phenotype?

(6) A summary diagram at the end would be helpful for understanding the main findings.

eLife assessment

This valuable study analyzes the role of the ciliary transition zone protein rpgrip1l in the development of the scoliotic phenotype in zebrafish. Through convincing proteomic and experimental validation in vivo, the authors demonstrated increased Annexin A2 expression in the brain and increased LCP1+ immune cell infiltration in scoliosis fish. These findings provide additional evidence for the previously proposed role of neuroinflammation in the development of idiopathic scoliosis in zebrafish.

Reviewer #1 (Public Review):

Summary:

In this study, Djebar et al. perform a comprehensive analysis of mutant phenotypes associated with the onset and progression of scoliosis in zebrafish ciliary transition zone mutants rpgrip1l and cep290. They determine that rpgrip1l is required in foxj1a-expressing cells for normal spine development, and that scoliosis is associated with brain ventricle dilations, loss of Reissner fiber polymerization, and the loss of 'tufts' of multi-cilia surrounding the subcommissural organ (the source of Reissner substance). Informed by transcriptomic and proteomic analyses, they identify a neuroinflammatory response in rpgrip1l and cep290 mutants that is associated with astrogliosis and CNS macrophage/microglia recruitment. Furthermore, anti-inflammatory drug treatment reduced scoliosis penetrance and severity in rpgrip1l mutants. Based on their data, the authors propose a feed-forward loop between astrogliosis, induced by perturbed ventricular homeostasis, and immune cell recruitment as a novel pathogenic mechanism of scoliosis in zebrafish ciliary transition zone mutants.

Strengths:

(1) Comprehensive characterization of the causes of scoliosis in ciliary transition zone mutants rpgrip1l and cep290.

(2) Comparison of rpgrip1l mutants pre- and post-scoliosis onset allowed authors to identify specific phenotypes as being correlated with spine curvature, including brain ventricle dilations, loss of Reissner fiber, and loss of cilia in proximity to the sub-commissural organ.

(3) Elegant genetic demonstration that increased urotensin peptide levels do not account for spinal curvature in rpgrip1l mutants.

(4) The identification of astrogliosis and Annexin over-expression in glial cells surrounding diencephalic and rhombencephalic ventricles as being correlated with scoliosis onset and severe curve progression is a very interesting finding, which may ultimately inform pathogenic mechanisms driving spine curvature

Weaknesses:

(1) The fact that cilia loss/dysfunction and Reissner fiber defects cause scoliosis in zebrafish is already well established in the literature, as is the requirement for cilia in foxj1a-expressing cells.

(2) Neuroinflammation has already been identified as the underlying pathogenic mechanism in at least 2 previously published scoliosis models (zebrafish ptk7a and sspo mutants).

(3) Anti-inflammatory drugs like aspirin, NAC, and NACET have also previously been demonstrated to suppress scoliosis onset and severe curve progression in these models.

Therefore, although similar observations in rpgrip1l and cep290 mutants (as reported here) add to a growing body of literature that supports a common biological mechanism underlying spine curvature in zebrafish, the novelty of reported findings is diminished.

(4) Although authors demonstrate that astrogliosis and/or macrophage or microglia cell recruitment are correlated with scoliosis, they do not formally demonstrate that these events are sufficient to drive spine curvature. Thus, the functional consequences of astrogliosis and microglia infiltration remain uncertain.

(5) The authors do not investigate the effect of anti-inflammatory treatments on other phenotypes they have correlated with spinal curve onset (like ventricle dilation, Reissner fiber loss, and multi-cilia loss around the subcommissural organ). This would help to identify causal events in scoliosis.

Reviewer #3 (Public Review):

Summary:

This paper describes a new mechanism of clearance of protein aggregates occurring during mitosis.

The authors have observed that animal cells can clear misfolded aggregated proteins at the end of mitosis. The images and data gathered are solid, convincing, and statistically significant. However, there is a lack of insight into the underlying mechanism. They show the involvement of the ER, ATPase-dependent, BiP chaperone, and the requirement of Cdk1 inactivation (a hallmark of mitotic exit) in the process. They also show that the mechanism seems to be independent of the APC/C complex (anaphase-promoting complex). Several points need to be clarified regarding the mechanism that clears the aggregates during mitosis:

• What happens in the cell substructure during mitosis to explain the recruitment of BiP towards the aggregates, which seem to be relocated to the cytoplasm surrounded by the ER membrane.

• How the changes in the cell substructure during mitosis explain the relocation of protein aggregates during mitosis.

• Why BiP seems to be the main player of this mechanism and not the cyto Hsp70 first described to be involved in protein disaggregation.

Strengths:

Experimental data showing clearance of protein aggregates during mitosis is solid, statistically significant, and very interesting.

Weaknesses:

Weak mechanistic insight to explain the process of protein disaggregation, particularly the interconnection between what happens in the cell substructure during mitosis to trigger and drive clearance of protein aggregates.

eLife assessment

How misfolded proteins are segregated and cleared is a significant question in mechanistic cell biology, since clearance of these aggregates can protect against pathologies that may otherwise arise. The authors discover a cell cycle stage-dependent clearing mechanism that involves the ER chaperone BiP, the proteosome, and CDK inactivation, but is curiously independent of the APC. These are valuable and interesting new observations, but the evidence supporting these claims is incomplete, and needs to be strengthened and further validated.

Reviewer #1 (Public Review):

Strengths:

The manuscript utilizes a previously reported misfolding-prone reporter to assess its behaviour in ER in different cell line models. They make two interesting observations:

(1) Upon prolonged incubation, the reporter accumulates in nuclear aggregates.

(2) The aggregates are cleared during mitosis. They further provide some insight into the role of chaperones and ER stressors in aggregate clearance. These observations provide a starting point for addressing the role of mitosis in aggregate clearance. Needless to say, going ahead understanding the impact of aggregate clearance on cell division will be equally important.

Weaknesses:

The study almost entirely relies on an imaging approach to address the issue of aggregate clearance. A complementary biochemical approach would be more insightful. The intriguing observations pertaining to aggregates in the nucleus and their clearance during mitosis lack mechanistic understanding. The issue pertaining to the functional relevance of aggregation clearance or its lack thereof has not been addressed. Experiments addressing these issues would be a terrific addition to this manuscript.

Reviewer #2 (Public Review):

Summary:

The authors provide an interesting observation that ER-targeted excess misfolded proteins localize to the nucleus within membrane-entrapped vesicles for further quality control during cell division. This is useful information indicating transient nuclear compartmentalization as a quality control strategy for misfolded ER proteins in mitotic cells, although endogenous substrates of this pathway are yet to be identified.

Strengths:

This microscopy-based study reports unique membrane-based compartments of ER-targeted misfolded proteins within the nucleus. Quarantining aggregating proteins in membrane-less compartments is a widely accepted protein quality control mechanism. This work highlights the importance of membrane-bound quarantining strategies for aggregating proteins. These observations open up multiple questions on proteostasis biology. How do these membrane-bound bodies enter the nucleus? How are the single-layer membranes formed? How exactly are these membrane-bound aggregates degraded? Are similar membrane-bound nuclear deposits present in post-mitotic cells that are relevant in age-related proteostasis diseases? Etc. Thus, the observations reported here are potentially interesting.

Weaknesses:

This study, like many other studies, used a set of model misfolding-prone proteins to uncover the interesting nuclear-compartment-based quality control of ER proteins. The endogenous ER-proteins that reach a similar stage of overdose of misfolding during ER stress remain unknown.

The mechanism of disaggregation of membrane-trapped misfolded proteins is unclear. Do these come out of the membrane traps? The authors report a few vesicles in living cells. This may suggest that membrane-untrapped proteins are disaggregated while trapped proteins remain aggregates within membranes.

The authors figure out the involvement of proteasome and Hsp70 during the disaggregation process. However, the detailed mechanisms including the ubiquitin ligases are not identified. Also, is the protein ubiquitinated at this stage?

This paper suffers from a lack of cellular biochemistry. Western blots confirming the solubility and insolubility of the misfolded proteins are required. This will also help to calculate the specific activity of luciferase more accurately than estimating the fluorescence intensities of soluble and aggregated/compartmentalized proteins. Microscopy suggested the dissolution of the membrane-based compartments and probably disaggregation of the protein. This data should be substantiated using Western blots. Degradation can only be confirmed by Western blots. The authors should try time course experiments to correlate with microscopy data. Cycloheximide chase experiments will be useful.

The cell models express the ER-targeted misfolded proteins constitutively that may already reprogram the proteostasis. The authors may try one experiment with inducible overexpression.

It is clear that a saturating dose of ER-targeted misfolded proteins activates the pathway. The authors performed a few RT-PCR experiments to indicate the proteostasis-sensitivity. Proteome-based experiments will be better to substantiate proteostasis saturation.

The authors should immunostain the nuclear compartments for other ER-membrane resident proteins that span either the bilayer or a single layer. The data may be discussed.

All microscopy figures should include control cells with similarly aggregating proteins or without aggregates as appropriate. For example, is the nuclear-targeted FlucDM-EGFP similarly entrapped? A control experiment will be interesting. Expression of control proteins should be estimated by western blots.

There are few more points that may be out of the scope of the manuscript. For example, how do these compartments enter the nucleus? Whether similar entry mechanisms/events are ever reported? What do the authors speculate? Also, the bilayer membrane becomes a single layer. This is potentially interesting and should be discussed with probable mechanisms. Also, do these nuclear compartments interfere with transcription and thereby deregulate cell division? What about post-mitotic cells? Similar deposits may be potentially toxic in the absence of cell division. All these may be discussed.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Boudjerna and Balagé et al. aim to elucidate the spatial origin of centriole amplification and the mechanisms behind the formation of an apical-basal body patch in multiciliated cells (MCCs). To this end, they focused on the role of microtubules and developed new tools for spatiotemporal and high-resolution analysis of different stages of centriole amplification, including the centrosome stages, A-stage, G-stage, and MCC-stage. Among these tools, the MEF-MCC cells grown on micropatterns stands out for its versatility as it is not tissue-specific and does not require epithelial cell-to-cell contact for differentiation. Additionally, the Cen2-GFP; mRuby-Deup1 knock-in mouse model was used to study different stages of centriole amplification in physiological brain MCCs. This model offers an advantage over the previously described Cen2-GFP model by enabling the resolution of early events in centriole amplification through the visualization of Deup1-positive structures and their dynamics. Finally, the authors leveraged powerful imaging techniques, including super-resolution microscopy, the U-ExM, and high-resolution live cell imaging in order to detect and track centriole amplification, elongation, disengagement, and migration.

By combining the MEF-MCC and knock-in mouse model with spatiotemporal imaging in control and nocodazole-treated cells(treated acutely or chronically), the authors define the sequence of events during centriole amplification, revealing the critical roles of microtubules for the first time. Initially, the centrosome-mediated microtubule network forms, organizing a pericentrosomal nest from which procentrioles and deuterosomes emerge. Their findings indicate the importance of microtubules in recruiting and maintaining pericentriolar material clouds that contain DEUP1, PCNT, SAS6, PLK1, PLK4, and tubulins. Following the amplification stage, the procentrioles mature, leading to cells displaying numerous MTOCs, as demonstrated by regrowth experiments. Mature centrioles then disengage from deuterosomes, attach to the nuclear envelope, and migrate to the apical surface facilitated by microtubules.

Strengths:

The manuscript provides new insights into the regulatory function of microtubules in centriole amplification. Addressing the role of microtubules during different stages of centriole amplification required the development of new tools to study brain MCCs, which will be useful in future studies of MCCs. A notable strength of this manuscript is the authors' thorough and quantitative analysis of highly dynamic processes in MCCs. The precision and detail in describing these dynamic events are impressive. This comprehensive analysis advances our understanding of MCC biology.

Weaknesses:

The role of microtubules and other molecular players during different stages of centriole amplification in brain MCCs can be further studied and strengthened using the tools developed in the manuscript. A more quantitative description of some of the analysis performed in the manuscript is required to strengthen the conclusions.

eLife assessment

In this important study, Boudjema et al. use cell culture models and advanced microscopic imaging to provide detailed analyses of the cellular events underlying centriole amplification, apical migration, and assembly of hundreds of motile cilia in multi-ciliated cells. This largely descriptive work provides a better understanding of this process that is of interest to cell biologists studying centrioles and cilia. Most of the claims are supported by the data, but the study would benefit from additional analyses regarding the roles of microtubules, which are currently incomplete, and from text editing to improve accessibility and readability, especially for a wider audience.

Reviewer #1 (Public Review):

The manuscript by Boudjema et al. describes the cellular events underlying centriole amplification and apical migration to allow the assembly of hundreds of motile cilia in multi-ciliated cells. For this, they use cell culture models in combination with fixed and live cell imaging using antibody staining and fluorescence from endogenously tagged centriole and deuterostome markers, respectively. The work is largely descriptive and functional analyses are restricted to treatment with the microtubule depolymerizing drug nocodazole. The imaging is state-of-the-art including confocal microscopy, live imaging with optical sectioning and high optical and temporal resolution, as well as super-resolution imaging by ultra-expansion microscopy.

The study does a good job of providing a very detailed description of the dynamics of centrioles and deuterostomes that lead to centriole amplification and apical migration in multiciliated cells. This detailed view was missing in previous work. It also reveals the involvement of microtubules at multiple steps: the formation of a cloud of deuterostome precursors, the nuclear envelope tethering of newly formed centrioles, their separation, and their migration to the apical surface.

It would have been useful to expand the analysis of the role of microtubules by including analyses of the requirement for specific microtubule motors, for a better understanding and additional evidence that microtubule-based transport is involved. A weak point is that there is no visualization of microtubules together with deuterosomes and centrioles at the different steps of centriole amplification and migration, to directly address how these structures may interact with and move along microtubules.

Overall, apart from experimental aspects and since this is largely a descriptive study, the manuscript would benefit from more precise language and a better description of the complex events underlying centriole amplification and movements.

Reviewer #2 (Public Review):

This important work will be of interest to centriole and cilia cell biologists. It describes in detail how microtubules control multiple aspects of centriole amplification in brain multiciliated cells. This study provides a greater time-resolved and molecular proteomic mapping of the different steps involved, with or without microtubule disruption. Boudjema et al. show that microtubules are important throughout the centriole amplification process, from the early stages, where the procentrioles emerge from a pericentriolar "nest", through the growth stage where microtubules maintain the perinuclear localisation, to the detachment stage, where microtubules assist in perinuclear disengagement and apical migration. The results are generally well supported by the evidence, but the manuscript would benefit significantly from some heavy editing to introduce more niche terms, standardize abbreviations in text, and labels on figures to help bring the readers, especially non-specialists, along with them - increasing the accessibility of their work.

Reviewer #3 (Public Review):

Summary:

The authors want to prove that there is a redox potential between germline stem cells (GSCs) and somatic cyst stem cells (CySCs) in the Drosophila testis, with ROS being higher in the former compared to the latter. They also want to prove that ROS travels from CySCs to GSCs. Finally, they begin to characterize the phenotypes caused by loss of SOD (which normally lowers ROS levels) in the tj- lineage and how this impacts the germline.

Strengths:

The role of SOD in somatic support cells is an under-explored area.

Weaknesses:

The authors fall short of accomplishing their goals. There are issues with the concept of the paper (ROS gradient between cells that causes a transfer of ROS across membranes for homeostasis), the data, the figures, and the scholarship of the testis. I have discussed each of the points in detail below. These weaknesses negatively impact the conclusions put forward by the authors. In short, their data is not compelling: there is no evidence provided by the authors that ROS diffuses from CySCs to GSCs as most of the claims about stem cells are founded on data about differentiating germ and somatic cells. The somatic SOD depletion phenotype is incompletely characterized and several pathways appear to change in these cells, including reduced Egfr signaling, increased Tor signaling, and increased Hh signaling. None of these results are sufficiently followed up on. And none of them are considered relative to their known roles in the testis. For example, high Hh signaling in CySCs increases their competitiveness with GSCs. Increased Tor signaling in all CySCs does not affect the CySC lineage. Reduced Egfr signaling in CySCs reduces the number of CySCs and reduces/inhibits abscission between GSCs-gonialblasts.

Major issues:

(1) Data<br /> a. Problems proving which mitochondria are associated with which lineage.<br /> b. There is no evidence that ROS diffuses from CySCs into GSCs.<br /> c. The changes in gst-GFP (redox readout) are possibly seen in differentiating germ cells (i.e., spermatogonia) but not in GSCs. This weakens their model that ROS in CySC is transferred to GSCs.<br /> d. Most of the paper examines the effect of SOD depletion (which should increase ROS) on the CySC lineage and GSC lineage. One big caveat is that tj-Gal4 is expressed in hub cells (Fairchild, 2016) so the loss of SOD from hub cells may also contribute to the phenotype. In fact, the niche in Figure 2D looks larger than the niche in the control in Figure 2C, arguing that the expression of Tj in niche cells may be contributing to the phenotype. The authors need to better characterize the niche in tj>SOD-RNAi testes.<br /> e. The tj>SOD-RNAi phenotype is an expansion of the Zfh1+ CySC pool, expansion of the Tj+ Zfh1- cyst cells (both due to increased somatic proliferation) and a non-autonomous disruption of the germline.<br /> f. I am not convinced that MAPK signaling is decreased in tj>SOD-i testes. Not only is this antibody finicky, but the authors don't have any follow-up experiments to see if they can restore SOD-depleted CySCs by expressing an Egfr gain of function. Additionally, reduced Egfr activity causes fewer somatic cells (not more) (Amoyel, 2016) and also inhibits abscission between GSCs and gonialblasts (Lenhart 2015), which causes interconnected cysts of 8- to 16 germ cells with one GSC emanating from the hub.<br /> g. The increase in Hh signaling in SOD-depleted CySCs would increase their competitiveness against GSCs and GSCs would be lost (Amoyel 2014). The authors need to validate that Hh protein expression is indeed increased in SOD-depleted CySCs/cyst cells and which cells are producing this Hh. Normally, only hub cells produce Hh (Michel, 2012; Amoyel 2013) to promote self-renewal in CySCs.<br /> h. The increase in p4E-BP is an indication that Tor signaling is increased, but an increase in Tor in the CySC lineage does not significantly affect the number of CySCs or cyst cells (Chen, 2021). So again I am not sure how increased Tor factors into their phenotype.<br /> i. The over-expression of SOD in CySCs part is incomplete. The authors would need to monitor ROS in these testes. They would also need to examine with tj>SOD affects the size of the hub.

(2) Concept<br /> Why would it be important to have a redox gradient across adjacent cells? The authors mention that ROS can be passed between cells, but it would be helpful for them to provide more details about where this has been documented to occur and what biological functions ROS transfer regulates.

(3) Issues with scholarship of the testis<br /> a. Line 82 - There is no mention of BMPs, which are the only GSC-self-renewal signal. Upd/Jak/STAT is required for adhesion of GSCs to the niche but not self-renewal (Leatherman and Dinardo, 2008, 2010). The author should read a review about the testis. I suggest Greenspan et al 2015. The scholarship of the testis should be improved.<br /> b. Line 82-84 - BMPs are produced by both hub cells and CySCs. BMP signaling in GSCs represses bam. So it is not technically correct to say the CySCs repress bam expression in GSCs.<br /> c. Throughout the figures the authors score Vasa+ cells for GSCs. This is technically not correct. What they are counting is single, Vasa+ cells in contact with the niche. All graphs should be updated with the label "GSCs" on the Y-axis.

(4) Issues with the text<br /> a. Line 1: multi-lineage is not correct. Multi-lineage refers to stem cells that produce multiple types of daughter cells. GSCs produce only one type of offspring and CySCs produce only one type of offspring. So both are uni-lineage. Please change accordingly.<br /> b. Lines 62-75 - Intestinal stem cells have constitutively high ROS (Jaspar lab paper) so low ROS in stem cell cells is not an absolute.<br /> c. Line 79: The term cystic is not used in the Drosophila testis. There are cyst stem cells (CySCs) that produce cyst cells. Please revise.<br /> d. Line 90 - perfectly balanced is an overstatement and should be toned down.<br /> e. Line 98 - division of labour is not supported by the data and should be rephrased.<br /> f. Line 200 - the authors provide no data on BMPs - the GSC self-renewal cue - so they should avoid discussing an absence of self-renewal cues.

(5) Issues with the figures<br /> a. The images are too small to appreciate the location of mitochrondria in GSCs and CySCs.<br /> b. Figure 1<br /> i. cell membranes are not marked, reducing the precision of assigning mitochondria to GSC or CySCs. It would be very helpful if the authors depleted ATP5A from GSCs and showed that the puncta are reduced in these cells and did a similar set of experiments for the tj-Gal4 lineage. It would also be very helpful if the authors expressed membrane markers (like myr-GFP) in the GSC and then in the CySC lineage and then stained with ATP5A. This would pinpoint in which cells ATP5A immunoreactivity is occurring.<br /> ii. The presumed changes in gst-GFP (redox readout) are possibly seen in differentiating germ cells (i.e., spermatogonia) but not in GSC.<br /> iii. Panels F, Q, and S are not explained and currently are irrelevant.<br /> c. Figure 3K - The evidence to support less Ecad in GSCs in tj>SOD-i testes is not compelling as the figure is too small and the insets show changes in Ecad in somatic cells, not GSC.<br /> d. Figure 4:<br /> i. Panel A, B The apparent decline (not quantified) may not contribute to the phenotype.<br /> ii. dpERK is a finicky antibody and the authors are showing a single example of each genotype. This is an important experiment because the authors are going to use it to conclude that MAPK is decreased in the tj>SOD-i samples. However, the authors don't have any positive (dominant-active Egfr) or negative (tj>mapk-i). As is standing the data are not compelling. The graph in F does not convey any useful information.<br /> e. Figure S1D - cannot discern green on black. It is critical for the authors to show monochromes (gray scale) for the readouts that they want to emphasize. I cannot see the green on black in Figure S1D.<br /> f. Figure S4 - there is no quantification of the number of Tj cells in K-N.

(6) Issues with Methods<br /> a. Materials and Methods are not described in sufficient depth - please revise.<br /> b. Note that tj-Gal4 has real-time expression in hub cells and this is not considered by the authors. The ideal genotype for targeting CySCs is tjGal4, Gal80TS, hh-Gal80. Additionally, the authors do not mention whether they are depleting throughout development into adulthood or only in adults. If the latter, then they must have used a temperature shift like growing the flies at 18C and then upshifting to 25C or 29C during adult stages.<br /> c. The authors need to show data points in all of the graphs. Some graphs do this but others do not.<br /> d. The authors state that all data points are from three biological replicates. This is not sufficient for GSC and CySC counts. Most labs count GSCs and CySCs from at least 10 testes of the correct genotype.

eLife assessment

This work focuses on the role of Reactive Oxygen Species (ROS) signaling in cyst stem cells of the Drosophila testis. In particular, the authors suggest that ROS can act as signaling molecules between somatic and germ stem cells of the testis. The work is potentially useful, although the evidence that supports the authors' claims is incomplete.

Reviewer #1 (Public Review):

The manuscript by Majhi and colleagues describes the effects of manipulating ROS levels in somatic stem cells of the testis on overall testis architecture, signaling, and function. The conclusions made by the authors are somewhat difficult to judge as the changes to the testis cell types are mostly not apparent in the representative images shown. This is true in examining gstD1-GFP expression and in the analysis of cell types and behaviours (e.g. cell cycle) and cell signaling pathway activity. Thus, the reader is left to try and interpret the quantification of the data to justify the authors' conclusions, but it is often not clear how the quantification was accomplished. For example, it is not clear how CySC vs. GSC quantification is done when the molecular markers used do not define the surface of these cells (plasma membrane) and mark different cellular compartments (Tj is nuclear while Vasa is perinuclear or cytoplasmic). Why the changes reported in quantification are not apparent in the specific example images chosen for the figures is worrisome. I'm much more used to being able to clearly see what the authors are reporting in the images, and then using the quantification to illustrate the range of data observed and demonstrate statistical significance. For this reason, I'm very concerned about the strength and validity of the conclusions. In addition, while many different characteristics of the testis somatic and germline cells are analyzed, a general and consistent view of how ROS affects these cells is not presented. In particular, one of the principle conclusions, that ROS signaling in the CySCs affects ROS signaling in the GSCs, is not well-supported by the data presented.

Specific Comments:

In Figure 1, it is very difficult to identify where CySCs end and GSCs begin without using a cell surface marker for these different cell types. In addition, the methods for quantifying the mitochondrial distribution in GSCs vs. CySCs are very much unclear, and appear to rely on colocalization with molecular markers that are not in the same cellular compartment (Tj-nuclear vs Vasa-perinuclear and cytoplasmic), the reader has no way to determine the validity of the mitochondrial distribution. Similarly, the labeling with gstD1-GFP is also very much unclear - I see little to no GFP signal in either GSCs or CySCs in panels 1G-K. Lastly, while the expression of SOD in CySCs does increase the gstD1-GFP signal in CySCs, the effects on GSCs claimed by the authors are not apparent.

In Figure 2, while the cell composition of the niche region does appear to be different from controls when SOD1 is knocked down in the CySCs, at least in the example images shown in Figures 2A and B, how cell type is quantified in Figures 2E-G is very much unclear in the figure and methods. Are these counts of cells contacting the niche? If so, how was that defined? Or were additional regions away from the niche also counted and, if so, how were these regions defined?

In Figure 3, it is quite interesting that there is an increase in Eya+, differentiating cyst cells in SOD1 knockdown animals, and that these Eya+ cells appear closer to the niche than in controls. However, this seems at odds with the proliferation data presented in Figure 2, since Eya+ somatic cells do not normally divide at all. Are they suggesting that now differentiating cyst cells are proliferative? In addition, it is important for them to show example images of the changes in Socs36E and ptp61F expression.

Overall, the various changes in signaling are quite puzzling-while Jak/Stat signaling from the niche is reduced, hh signaling appears to be increased. Similarly, while the authors conclude that premature differentiation occurs close to the niche, EGF signaling, which occurs from germ cells to cyst cells during differentiation, is decreased. Many times these changes are contradictory, and the authors do not provide a suitable explanation to resolve these contradictions.

Reviewer #2 (Public Review):

Summary:

In this work, the authors investigate the role of the Superoxide disumutase 1 (Sod1) enzyme, which acts to reduce the reactive oxygen species load, in the Drosophila testis. They show that the knockdown of Sod1 in somatic cells impacts stem cell numbers both autonomously in the soma and non-autonomously in the germline. Somatic stem cell numbers are increased, while germline stem cells are decreased and differentiate prematurely. The authors then show that in somatic Sod1 knockdowns, several signalling pathways are disrupted and that these may be responsible at least in part for the phenotypes observed. Finally, over-expression of Sod1 in the soma results in opposite phenotypes, suggesting that ROS levels do play a role in maintaining the balance between both stem cell populations in the testis.

Strengths:

The main strength of this work is to show a previously unappreciated role for Sod1 (and presumably by extension of ROS) in the Drosophila testis and in the regulation of stem cell self-renewal and differentiation. The authors use multiple readouts to show that the knockdown of Sod1 in the soma increases the number of somatic cells and also drives a non-autonomous, premature differentiation of germ cells. They also quantify the early differentiation of the germline using two different methods. Importantly, overexpression of Sod1 produces opposite phenotypes to knockdown, strengthening the conclusions.

Weaknesses:

Although the data presented are interesting, an important weakness of the manuscript as it currently stands is that many statements are not fully supported by the data. In particular, the authors do not provide any evidence of "cell redox-pairs" as indicated in the manuscript title, nor of intercellular redox gradients, as stated in several places throughout. While the data are consistent with non-autonomous regulation of ROS levels, this would not constitute a gradient. However, and crucially, there is no evidence provided to show that Sod1 manipulation in the soma is affecting ROS levels in the germline and that any of the phenotypes observed are a consequence of elevated ROS in the germline, rather than indirect effects caused by dysregulation of somatic self-renewal and differentiation, which is known to impact the germline. Indeed, there are many published reports of autonomous manipulations in the soma that influence either germline stem cell number (eg PMID: 19797664 among others) or differentiation (eg PMID: 17629483). The latter example is particularly relevant as the authors show altered somatic ERK levels, and the role of somatic ERK in promoting germ cell development is well established (PMID: 11048722, 11048723,...). Thus, whether Sod1 plays any non-autonomous role in controlling germ cell fate through ROS in the germline directly, or whether the phenotypes observed can all be explained by autonomous effects on somatic cell behaviour is debatable, but the experiments presented here do not distinguish between these two hypotheses. The only evidence presented by the authors for a non-autonomous role of Sod1 is the expression of a GFP reporter for gstD1. The quantifications and images are not clear and do not show unambiguously that this reporter is expressed in germ cells. Indeed, the quantifications show overlap between somatic and germline markers, suggesting that either the images themselves or the way they are quantified does not allow the authors to distinguish between the two cell types. Similarly, the claim that somatic mitochondria are enriched at the CySC-GSC interface and that this distribution maintains the redox balance in the niche is not supported by any experimental data. CySCs are extremely thin cells and much of the space is occupied by the nucleus (PMID: 114676), therefore it is likely that mitochondria would be enriched at the periphery. A careful analysis would be necessary to show that this enrichment is specific to the interface with GSCs. Moreover, no experiments are conducted to test whether mitochondrial distribution in CySCs has any impact on GSCs. Finally, no experiments are conducted to show definitively that the phenotypes observed upon Sod1 knockdown are indeed due to increased ROS, while this claim is made several times in the text. At present, the data presented here can support a role for Sod1 in somatic CySCs, but much more caution is required in attributing this to either ROS or intercellular ROS signaling. Therefore, several claims made in the title and throughout the text are not supported by evidence.

Besides this central point, there are other areas that should be improved. In particular, the data using the Fucci reporter to show accelerated proliferation do not appear convincing. It would seem that the proportions of cells in each phase are roughly similar, just that there are more cycling cells. A careful analysis of these results would distinguish between these two and determine whether Sod1 knockdown simply impairs differentiation (and therefore results in more somatic cells proliferating) or whether it speeds up the cell cycle (resulting in an increased mitotic index as suggested, but this requires a ratio to be shown). Similarly, several quantifications are not clearly explained, making it hard to understand what is being measured. As an example, while the decrease in pERK in CySCs is clear from the image and matched in the quantification, the increase in cyst cells is not apparent from the fire LUT used. The change in fluorescence intensity therefore may be that more cells have active ERK, rather than an increase per cell (similar arguments apply to the quantifications for p4E-BP or Ptc). Therefore, it is hard to know whether Sod1 knockdown results in increased or decreased signaling in individual cells.

Impact of study:

Demonstrating intercellular communication through ROS and its importance in maintaining the balance between two stem cell populations would be a finding of interest to a broad field. However, it remains to be demonstrated that this is the case, and given this, this study will have a limited impact.

Reviewer #3 (Public Review):

The authors tested a dietary intervention focused on improving meal regularity in this interesting paper. The study, a two-group, single-center, randomized, controlled, single-blind trial, utilized a smartphone application to track participants' meal frequencies and instructed the experimental group to confine their eating to these times for six weeks. The authors concluded that improving meal regularity reduced excess body weight despite food intake not being altered and contributed to overall improvements in well-being.

The concept is interesting, but the need for more rigor is of concern.

A notable limitation is the reliance on self-reported food intake, with the primary outcome being self-reported body weight/BMI, indicating an average weight loss of 2.62 kg. Despite no observed change in caloric intake, the authors assert weight loss among participants.

The trial's reliance on self-reported caloric intake is problematic, as participants tend to underreport intake; for example, in the NEJM paper (DOI: 10.1056/NEJM199212313272701), some participants underreported caloric intake by approximately 50%, rendering such data unreliable and hence misleading. More rigorous methods for assessing food intake are available and should have been utilized. Merely acknowledging the unreliability of self-reported caloric intake is insufficient as it would still leave the reader with the impression that there is no change in food intake when we actually have no idea if food intake was altered. A more robust approach to assessing food intake is imperative. Even if a decrease in caloric intake is observed through rigorous measurement, as I am convinced a more rigorous study would unveil testing this paradigm, this intervention may merely represent another short-term diet among countless others that show that one may lose weight by going on a diet, principally due to heightened dietary awareness.

Furthermore, the assessment of circadian rhythm using the MCTQ, a self-reported measure of chronotype, may not be as reliable as more objective methods like actigraphy.

Given the potential limitations associated with self-reported data in both dietary intake and circadian rhythm assessment, the overall impact of this manuscript is low. Increasing rigor by incorporating more objective and reliable measurement techniques in future studies could strengthen the validity and impact of the findings.

eLife assessment

This study investigates a dietary intervention that employs a smartphone app to promote meal regularity, which may be useful. Despite no observed changes in caloric intake, the authors report significant weight loss. While the concept is very interesting and deserves to be studied due to its potential clinical relevance, the study's rigor needs to be revised, notably for its reliance on self-reported food intake, a highly unreliable way to assess food intake. Additionally, the study theorizes that the intervention resets the circadian clock, but the study needs more reliable methods for assessing circadian rhythms, such as actigraphy.

Reviewer #1 (Public Review):

The authors Wilming and colleagues set out to determine the impact of regularity of feeding per se on the efficiency of weight loss. The idea was to determine if individuals who consume 2-3 meals within individualized time frames, as opposed to those who exhibit stochastic feeding patterns throughout the circadian period, will cause weight loss.

The methods are rigorous, and the research is conducted using a two-group, single-center, randomized-controlled, single-blinded study design. The participants were aged between 18 and 65 years old, and a smartphone application was used to determine preferred feeding times, which were then used as defined feeding times for the experimental group. This adds strength to the study since restricting feeding within preferred/personalized feeding windows will improve compliance and study completion. Following a 14-day exploration phase and a 6-week intervention period in a cohort of 100 participants (inclusive of both the controls and the experimental group that completed the study), the authors conclude that when meals are restricted to 45min or less durations (MTVS of 3 or less), this leads to efficient weight loss. Surprisingly, the study excludes the impact of self-reported meal composition on the efficiency of weight loss in the experimental group. In light of this, it is important to follow up on this observation and develop rigorous study designs that will comprehensively assess the impact of changes (sustained) in dietary composition on weight loss. The study also reports interesting effects of regularity of feeding on eating behavior, which appears to be independent of weight loss. Perhaps the most important observation is that personalized interventions that cater to individual circadian needs will likely result in more significant weight loss than when interventions are mismatched with personal circadian structures. One are of concern for the study is its two-group design; however, single-group cross-over designs are tedious to develop, and an adequate 'wash-out' period may be difficult to predict. A second weakness is not considering the different biological variables and racial and ethnic diversity and how that might impact outcomes. In sum, the authors have achieved the aims of the study, which will likely help move the field forward.

Reviewer #2 (Public Review):

Summary:

The authors investigated the effects of the timing of dietary occasions on weight loss and well-being with the aim of explaining if a consistent, timely alignment of dietary occasions throughout the days of the week could improve weight management and overall well-being. The authors attributed these outcomes to a timely alignment of dietary occasions with the body's own circadian rhythms. However, the only evidence the authors provided for this hypothesis is the assumption that the individual timing of dietary occasions of the study participants identified before the intervention reflects the body's own circadian rhythms. This concept is rooted in understanding of dietary cues as a zeitgeber for the circadian system, potentially leading to more efficient energy use and weight management. Furthermore, the primary outcome, body weight loss, was self-reported by the study participants.

Strengths:

The innovative focus of the study on the timing of dietary occasions rather than daily energy intake or diet composition presents a fresh perspective in dietary intervention research. The feasibility of the diet plan, developed based on individual profiles of the timing of dietary occasions identified before the intervention, marks a significant step towards personalised nutrition.

Weaknesses:

Several methodological issues detract from the study's credibility, including unclear definitions not widely recognized in nutrition or dietetics (e.g., "caloric event"), lack of comprehensive data on body composition, and potential confounders not accounted for (e.g., age range, menstrual cycle, shift work, unmatched cohorts, inclusion of individuals with normal weight, overweight, and obesity). The primary outcome's reliance on self-reported body weight and subsequent measurement biases further undermines the reliability of the findings. Additionally, the absence of registration in clinical trial registries, such as the EU Clinical Trials Register or clinicaltrials.gov, and the multiple testing of hypotheses which were not listed a priori in the research protocol published on the German Register of Clinical Trials impede the study's transparency and reproducibility.

Achievement of Objectives and Support for Conclusions:

The study's objectives were partially met; however, the interpretation of the effects of meal timing on weight loss is compromised by the weaknesses mentioned above. The evidence only partially supports some of the claims due to methodological flaws and unstructured data analysis.

Impact and Utility:

Despite its innovative approach, significant methodological and analytical shortcomings limit the study's utility. If these issues were addressed, the research could have meaningful implications for dietary interventions and metabolic research. The concept of timing of dietary occasions in sync with circadian rhythms holds promise but requires further rigorous investigation.

Reviewer #1 (Public Review):

In this work, the authors provide a valuable transcriptomic resource for the intermediate free-living transmission stage (miracidium larva) of the blood fluke. The single-cell transcriptome inventory is beautifully supplemented with in situ hybridization, providing spatial information and absolute cell numbers for many of the recovered transcriptomic states. The identification of sex-specific transcriptomic states within the populations of stem cells was particularly unexpected. The work comprises a rich resource to complement the biology of this complex system, however falls short in some technical aspects of the bioinformatic analyses of the generated sequence data.

(1) Four sequencing libraries were generated and then merged for analysis, however, the authors fail to document any parameters that would indicate that the clustering does not suffer from any batch effects.

(2) Additionally, the authors switch between analysis platforms without a clear motivation or explanation of what the fundamental differences between these platforms are. While in theory, any biologically robust observation should be recoverable from any permutation of analysis parameters, it has been recently documented that the two popular analysis platforms (Seurat - R and scanPy - python) indeed do things slightly differently and can give different results (https://www.biorxiv.org/content/10.1101/2024.04.04.588111v1). For this reason, I don't think that one can claim that Seurat fails to find clusters resolved by SAM without running a similar pipeline on the cluster alone as was done with SAM/scanPy here. The manuscript itself needs to be checked carefully for misleading statements in this regard.

(3) Similarly, the manuscript contains many statements regarding clusters being 'connected to', or forming a 'bridge' on the UMAP projection. One must be very careful about these types of statements, as the relative position of cells on a reduced-dimension cell map can be misleading (see Chari and Pachter 2023). To support these types of interpretations, the authors should provide evidence of gene expression transitions that support connectivity as well as stability estimates of such connections under different parameter conditions. Otherwise, these descriptors hold little value and should be dropped and the transcriptomic states simply defined as clusters with no reference to their positions on the UMAP.

(4) The underlying support for the clusters as transcriptomically unique identities is not well supported by the dot plots provided. The authors used very permissive parameters to generate marker lists, which hampers the identification of highly specific marker genes. This permissive approach can allow for extensive lists of upregulated genes for input into STRING/GO analyses, this is less useful for evaluating the robustness of the cluster states. Running the Seurat::FindAllMarkers with more stringent parameters would give a more selective set of genes to display and thereby increase the confidence in the reader as to the validity of profiles selected as being transcriptomically unique.

(5) Figure 5B shows a UMAP representation of cell positions with a statement that the clustering disappears. As a visual representation of this phenomenon, the UMAP is a very good tool, however, to make this statement you need to re-cluster your data after the removal of this gene set and demonstrate that the data no longer clusters into A/B and C/D. Also, as a reader, these data beg the question: which genes are removed here? Is there an over-representation of any specific 'types' of genes that could lead to any hypotheses of the function? Perhaps the STRING/GO analyses of this gene set could be informative.

(6) How do the proportions of cell types characterized via in situ here compare to the relative proportions of clusters obtained? It does not correspond to the percentages of the clusters captured (although this should be quantified in a similar manner in order to make this comparison direct: 10,686/20,478 = ~50% vs. 7%), how do you interpret this discrepancy? While this is mentioned in the discussion, there is no sufficient postulation as to why you have an overabundance of the stem cells compared to their presence in the tissue. While it is true that you could have a negative selection of some cell types, for example as stated the size of the penetration glands exceeds both that of the 10x capabilities (40uM), and the 30uM filters used in the protocol, this does not really address why over half of the captured cells represent 'stem cells'. A more realistic interpretation would be biological rather than merely technical. For example, while the composition of the muscle cells and the number of muscle transcriptomes captured are quite congruent at ~20%, the organism is composed of more than 50% of neurons, but only 15% of the transcriptomic states are assigned to neuronal. Could it be that a large fraction of the stem cells are actually neural progenitors? Are there other large inconsistencies between the cluster sizes and the fraction of expected cells? Could you look specifically at early transcription factors that are found in the neurons (or other cell types) within the various stem cell populations to help further refine the precursor/cell type relationships?

eLife assessment

This is a valuable study in which the authors provide an expression profile of the human blood fluke, Schistosoma mansoni. A strength of this solid study is in its inclusion of in situ hybridisation to validate the predictions of the transcript analysis.

Reviewer #2 (Public Review):

Summary:

In this manuscript the authors have generated a single-cell atlas of the miracidium, the first free-living stage of an important human parasite, Schistosoma mansoni. Miracidia develop from eggs produced in the mammalian (human) host and are released into freshwater, where they can infect the parasite's intermediate snail host to continue the life cycle. This study adds to the growing single-cell resources that have already been generated for other life-cycle stages and, thus, provides a useful resource for the field.

Strengths:

Beyond generating lists of genes that are differentially expressed in different cell types, the authors validated many of the cluster-defining genes using in situ hybridization chain reaction. In addition to providing the field with markers for many of the cell types in the parasite at this stage, the authors use these markers to count the total number of various cell types in the organism. Because the authors realized that their cell isolation protocols were biasing the cell types they were sequencing, they applied a second method to help them recover additional cell types.

Schistosomes have ZW sex chromosomes and the authors make the interesting observation that the stem cells at this stage are already expressing sex (i.e. W)-specific genes.

Weaknesses:

The sample sizes upon which the in situ hybridization results and cell counts are based are either not stated (in most cases) or are very small (n=3). This lack of clarity about biological replicates and sample sizes makes it difficult for the reader to assess the robustness of the results and the extremely small sample sizes (when provided) are a missed opportunity to explore the variability of the system, or lack thereof.

Although assigning transcripts to a given cell type is usually straightforward via in situ experiments, the authors fail to consider the potential difficulty of assigning the appropriate nuclei to cells with long cytoplasmic extensions, like neurons. In the absence of multiple markers and a better understanding of the nervous system, it seems likely that the authors have overestimated the number of neurons and misassigned other cell types based on their proximity to neural projections.

The conclusion that germline genes are expressed in the miracidia stem cells seems greatly overstated in the absence of any follow-up validation. The expression scales for genes like eled and boule are more than 3 orders of magnitude smaller than those used for any of the robustly expressed genes presented throughout the paper. These scales are undefined, so it isn't entirely clear what they represent, but neither of these genes is detected at levels remotely high (or statistically significant) enough to survive filters for cluster-defining genes. Given that germ cells often develop early in embryogenesis and arrest the cell cycle until later in development, and that these transcripts reveal no unspliced forms, it seems plausible that the authors are detecting some maternally supplied transcripts that have yet to be completely degraded.

Reviewer #1 (Public Review):

Summary:

The article explores the connection between immunogenic cell death (ICD)-related genes and bladder cancer prognosis, immune infiltration, and response to therapy. The study identifies a risk-scoring model involving four ICD-related genes (CALR, IL1R1, IFNB1, IFNG), showing a correlation between higher risk scores and weaker anti-tumor immune function.

Strengths:

The significance lies in the potential for personalized treatment guidance in bladder cancer. The establishment of a risk-scoring model to predict patient survival is noteworthy.

Weaknesses:

However, the identification of ICD-related genes is somewhat conventional, focusing on known genes regulating cancer immune response. To enhance the significance of the risk-scoring model, it would be better if the authors could validate the model across various cancer types. The strength of evidence appears moderate, but broader applicability would strengthen the findings.

eLife assessment

This study investigates the associations of four ICD-related genes in bladder cancer with increased immune cell infiltration and more prolonged survival. The study is valuable because it identifies a risk-scoring model, showing a correlation between high-risk scores based on four ICD-related genes and weak anti-tumour immune function. However, the evidence supporting the association of these genes and immunotherapy response is incomplete.

Reviewer #2 (Public Review):

Immunogenic cell death (ICD) can lead to the release of factors such as DAMPs which promote an adaptive immune response. In the context of cancer, there is clear evidence of anti-tumour benefits as a result of ICD, perhaps induced by chemotherapy.

Lilong et al used TCGA data to explore whether a previously published 34 gene 'ICD-related' signature could stratify bladder cancer patients by prognosis and ultimately predict patient survival. The gene signature contains many genes involved in inflammation and immunity (IFNg, IL6, TNF, IL17A, TLR4, CD8B, etc) and those related to ICD (such as CALR, HMGB1, HSP, NLRP3, etc). The authors divide patients into 'ICD-high' and '-low' based on the expression of this gene set and find that 'ICD-high' is associated with longer survival in TCGA bladder cancer data. The authors further argue that ICD-high group responds better to PD1 therapies. From this 34-gene signature, it appears that LASSO regularisation and Cox analysis identifies a four-gene 'risk' signature (CALR, IL1R1, IFNB1, IFNG) which is associated with shorter patient survival and lower immunotherapy response rates. This is the primary finding. Their methodology is very similar to a publication in 2021 in Frontiers in Immunology instead in the context of head and neck squamous cell carcinoma. This paper is not referenced.

In terms of the strengths of the work, it is certainly plausible that the author's four gene signature has an association with survival in bladder cancer, at least based on the two datasets studied. However, the relatedness of their findings to ICD is unconvincing, and glaring omissions from the manuscript in terms of methods limit confidence in the work. The authors show a potential association with bladder cancer patient survival and their four gene signatures, but substantial revisions are required for this to be appropriately evidenced.

Reviewer #2 (Public Review):

Summary:

The authors provide compelling evidence that stimulation of epidermal cells in Drosophila larvae results in the stimulation of sensory neurons that evoke a variety of behavioral responses. Further, the authors demonstrate that epidermal cells are inherently mechanoresponsive and implicate a role for store-operated calcium entry (mediated by Stim and Orai) in the communication to sensory neurons.

Strengths:

The study represents a significant advance in our understanding of mechanosensation. Multiple strengths are noted. First, the genetic analyses presented in the paper are thorough with appropriate consideration to potential confounds. Second, behavioral studies are complemented by sophisticated optogenetics and imaging studies. Third, identification of roles for store-operated calcium entry is intriguing. Lastly, conservation of these pathways in vertebrates raise the possibility that the described axis is also functional in vertebrates.

Weaknesses:

The study has a few conceptual weaknesses that are arguably minor. The involvement of store-operated calcium entry implicates ER calcium store release. Whether mechanical stimulation evokes ER calcium release in epidermal cells and how this might come about (e.g., which ER calcium channels, roles for calcium-induced calcium release etc.) remains unaddressed. On a related note, the kinetics of store-operated calcium entry is very distinct from that required for SV release. The link between SOC and epidermal cells-neuron transmission is not reconciled. Finally, it is not clear how optogenetic stimulation of epidermal cells results in the activation of SOC.

eLife assessment

This is an important work and provides a significant advance in our understanding of mechanosensation in the epidermis. The evidence presented is solid, however, additional work such as testing whether the activation time can be shorter, addressing the mechanism underlying endoplasmic reticulum calcium release, and improving the clarity of writing and rigor of analysis would strengthen the study. This work will be of broad interest to neurobiologists, epithelial cell biologists, and mechanobiologists.

Reviewer #1 (Public Review):

Summary:

In this meticulously conducted study, the authors show that Drosophila epidermal cells can modulate escape responses to noxious mechanical stimuli. First, they show that activation of epidermal cells evokes many types of behaviors including escape responses. Subsequently, they demonstrate that most somatosensory neurons are activated by activation of epidermal cells, and that this activation has a prolonged effect on escape behavior. In vivo analyses indicate that epidermal cells are mechanosensitive and require stored-operated calcium channel Orai. Altogether, the authors conclude that epidermal cells are essential for nociceptive sensitivity and sensitization, serving as primary sensory noxious stimuli.

Strengths:

The manuscript is clearly written. The experiments are logical and complementary. They support the authors' main claim that epidermal cells are mechanosensitive and that epidermal mechanically evoked calcium responses require the stored-operated calcium channel Orai. Epidermal cells activate nociceptive sensory neurons as well as other somatosensory neurons in Drosophila larvae, and thereby prolong escape rolling evoked by mechanical noxious stimulation.

Weaknesses:

Core details are missing in the protocols, including the level of LED intensity used, which are necessary for other researchers to reproduce the experiments. For most experiments, the epidermal cells are activated for 60 s, which is long when considering that nocifensive rolling occurs on a timescale of milliseconds. It would be informative to know the shortest duration of epidermal cell activation that is sufficient for observing the behavioral phenotype (prolongation of escape behavior) and activation of sensory neurons.

eLife assessment

The study presents important findings on the role of MSI2-HOXA9 translocation in chronic myeloid leukemia. The authors provide convincing evidence supporting the role of this translocation in leukemogenesis by using elegant mouse modeling and in vitro mechanistic studies. Consistent with the reviews, the studies can be strengthened with further murine and cell line experiments.

Reviewer #1 (Public Review):

This is a very interesting study by Kyle Spinler et al., demonstrating the novel role of MSI2-HOXA9 translocation in the development and pathogenesis of blast crisis CML. The authors employed appropriate in vitro and in vivo assays, including a sophisticated transplantation-based model of CML, which is well-established in the field of studying the pathogenesis of CML. Additionally, the authors successfully concluded that the MSI2 RNA binding domain RRM1 has a preferential impact on the growth of blast crisis CML.

The quality of this research article could be significantly enhanced by addressing the following points:

Major:

(1) Do mice with BCR-ABL/MSI2-HOXA9 leukemia have an increased pool of leukemic stem cells (LSC), or do they have an increased propensity to develop blast cells? Is it the number of LSCs that has increased, or is it the function of LSC to give rise to the disease that has increased? It is not clear if the detected differences in Lineage-negative cells (Figure S1D) were detected in vitro in retrovirally transduced cells or were detected in vivo in transplanted mice. If the differences were detected in vitro, could the author confirm the same findings in vivo? This will greatly enhance the understanding of in vivo disease pathogenesis and could directly link the aggressivity of the disease (shortened survival) with an increased stem cell-like population.

(2) The authors suggest that BCR-ABL/MSI2-HOXA9 leads to the development of blast crisis-CML. One of the main characteristics of blast crisis-CML is drug resistance. Is BCR-ABL/MSI2-HOXA9 leukemia resistant to classical CML treatment drugs?

(3) The authors have emphasized the heightened expression of Polrmt in delineating the mitochondrial phenotype of BCR-ABL/MSI2-HOXA9 leukemia cells. However, the regulatory mechanism governing the expression of Polrmt by MSI2-HOXA9 has not been clearly demonstrated by the authors. Unveiling this mechanism would constitute a novel finding and significantly elevate the quality of the research.

(4) Did the authors observe any survival differences between BCR-ABL/NUP98-HOXA9 and BCR-ABL/MSI2-HOXA9?

Reviewer #2 (Public Review):

The manuscript titled, "Identification of a Musashi2 translocation as a novel oncogene in myeloid leukemia" by Spinler et al. studies the functional role of the translocation t(7;17)(p15;q23), resulting in MSI2/HOXA9 fusion gene, as a secondary driver in bcCML. MSI2-HOXA9 forced expression along with BCR-ABL enhances colony formation and leads to a more aggressive disease in vivo. Depletion of the RNA binding domain RRM1 or RRM2 of MSI2 led to a significant reduction in colony formation, with RRM1 depletion specifically impacting differentiation and blast cell counts. Mechanistically, the authors find that MSI2-HOXA9 aberrantly localizes to the nucleus, elevating the expression of mitochondrial polymerase Polrmt, thereby leading to upregulation of mitochondrial components and enhancing mitochondrial function and basal respiration. Overall, this study examines how the rare MSI2-HOXA9 fusion gene can act as a novel cooperating oncogene and could serve as a secondary hit in the progression of CML to blast crisis.

Strengths:

(1) Demonstration that MSI2-HOXA9 contributes to oncogenesis in the BCR-ABL context.

(2) Development of a novel cooperativity model for BCR-ABL and provides additional supporting data for the role of MSI2 in leukemogenesis.

(3) Evidence that MSI2-HOXA9 acts uniquely compared to MSI2 alone through nuclear vs. cytoplasmic localization and activation of mitochondrial polymerase Polrmt.

Weaknesses:

(1) MSI2-HOXA9 fusion is extremely rare as it has been only found in a handful of patients and it is not clear whether other MSI2 fusions function in a similar manner.

(2) The mechanism needs to be strengthened since MSI2 alone or the HOXA9 mutant may not be linked to the mitochondrial mechanism.

(3) It is not clear that the mitochondrial pathway is sufficient for the MSI2-HOXA9 oncogenic mechanism.

Author response:

We are grateful to the reviewers for their interest and enthusiasm about the work, and deeply appreciate their constructive comments and suggestions. Our responses are below

(1) Do mice with BCR-ABL/MSI2-HOXA9 leukemia have an increased pool of leukemic stem cells (LSC), or do they have an increased propensity to develop blast cells? Is it the number of LSCs that has increased, or is it the function of LSC to give rise to the disease that has increased? It is not clear if the detected differences in Lineage-negative cells (Figure S1D) were detected in vitro in retrovirally transduced cells or were detected in vivo in transplanted mice. If the differences were detected in vitro, could the author confirm the same findings in vivo? This will greatly enhance the understanding of in vivo disease pathogenesis and could directly link the aggressivity of the disease (shortened survival) with an increased stem cell-like population.

We find that BCR-ABL/MSI2-HOXA9 leads to a marked increase in Lineage negative (Lin-) cells which contains the LSC fraction. Specifically, the LSC containing fraction represented 14.1% of the BCR-ABL driven disease and 56.7% of the BCR-ABL and MSI2-HOXA9 driven disease (p<.0001). This suggests that MSI2-HOXA9 triggers the expansion of the undifferentiated LSC containing pool. In addition, the blast frequency was also increased albeit to a lesser extent, with 63.8% blasts (SEM 1.1) for BCR-ABL and 83.3% (SEM 3.1) for BCR-ABL/MSI2-HOXA9 (p=.0001). This suggests that the resulting aggressive disease seen with MSI2-HOXA9 is a consequence of a large increase in undifferentiated  LSC containing cells, as well as the resulting increase in the blast count. The Lin- cells were analyzed from fully established leukemias in vivo (Fig. S1D)

(2) The authors suggest that BCR-ABL/MSI2-HOXA9 leads to the development of blast crisis-CML. One of the main characteristics of blast crisis-CML is drug resistance. Is BCR-ABL/MSI2-HOXA9 leukemia resistant to classical CML treatment drugs?

The sensitivity to Imatinib is a very interesting question. In general, while differentiated cells in CML are sensitive to Imatinib, the more undifferentiated cells (LSCs) are resistant1,2. Based on the fact that therapy resistance in blast crisis is largely driven by the undifferentiated fraction of leukemia cells, and given that BCR-ABL/MSI2-HOXA9 driven disease harbors a larger fraction of these undifferentiated cells, we would predict that BCR-ABL/MSI2-HOXA9 leukemia would also be more resistant to imatinib. However, this would need to be experimentally demonstrated and is an important question to address.

(3) The authors have emphasized the heightened expression of Polrmt in delineating the mitochondrial phenotype of BCR-ABL/MSI2-HOXA9 leukemia cells. However, the regulatory mechanism governing the expression of Polrmt by MSI2-HOXA9 has not been clearly demonstrated by the authors. Unveiling this mechanism would constitute a novel finding and significantly elevate the quality of the research.

Since Polrmt and mitochondrial genes are transcribed in the nucleus we explored whether MSI2-HOXA9 may control mitochondrial gene expression by triggering expression of Polrmt and other key transcription factors. Consistent with this possibility, MSI2-HOXA9 was preferentially found in the nucleus relative to MSI2. In addition, there were 10 occurrences of the minimal MSI2 RRM1 consensus binding sequence UAGU within the Polrmt transcript. While this is consistent with the possibility that Polrmt expression can be post-transcriptionally modulated by MSI2-HOXA9, this needs to be experimentally validated using Clip Seq analysis with wild type MSI2 as well as the MSI2-HOXA9 fusion protein in context of blast crisis CML.

(4) Did the authors observe any survival differences between BCR-ABL/NUP98-HOXA9 and BCR-ABL/MSI2-HOXA9?

In previous work from our lab we have found that the median survival for BCR-ABL/NUP98-HOXA9 was 17 days, and with BCR-ABL/ MSI2-HOXA9 was 18.5 days (p value of 0.22). This suggests that there is not a significant difference in survival times between the leukemias driven by the distinct alleles, and they may be equally aggressive.

(1) MSI2-HOXA9 fusion is extremely rare as it has been only found in a handful of patients and it is not clear whether other MSI2 fusions function in a similar manner.

We were very surprised and excited to see the large number of translocations in solid cancers that involve MSI2.  Interestingly, MSI2 translocations occurred both at the N and the C terminus.  Distinct translocations are likely to have unique roles in each disease context. For example, if MSI2’s 5 prime end is part of a translocation, it may functionally contribute via its promoter to drive expression in immature cells and could thus activate oncogenic signals (e.g. controlled by the partner gene) in immature cells which are inherently more susceptible to transformation (Eµ-myc is an example of such a translocation). If Msi2’s RRM domains are part of the fusion, they could bind and target RNAs aberrantly (such as in the wrong cell and the wrong time) and lead to activation of downstream oncogenic mediators. To fully understand the role of each of these translocations in each specific cancer, we would need to experimentally test their impact by ectopic expression in the appropriate cell of origin and domain mapping the basis of any impact in the relevant cancer models as we have done for MSI2-HOXA9 in blast crisis CML in the work we report here.   While this is an intensive undertaking, it is nonetheless important future work as it will undoubtedly lead to new insight about MSI2 linked translocations in diverse solid cancers such as breast cancer and lung cancer.

(2) The mechanism needs to be strengthened since MSI2 alone or the HOXA9 mutant may not be linked to the mitochondrial mechanism. (3) It is not clear that the mitochondrial pathway is sufficient for the MSI2-HOXA9 oncogenic mechanism.

Our observation that MSI2-HOXA9 triggered changes in mitochondrial function was of particular interest as it was (to our knowledge) uncharted in context of Msi2 signaling in cancer, thus leading us to explore this further.  However, multiple other signals are likely downstream regulators and these may well act cooperatively with, or independently of, the heightened­­ mitochondrial function we report here. Among these pathways, the most likely mediators included oncogenic programs related to the Wnt pathway including Wnt, Fzd 3 and Frat1, and those related to the Notch pathway including-Tribbles and Hey1 as well as other stem cell genes such as Aldh1. These programs have been previously implicated in the regulation of myeloid leukemia3-11 and could well mediate the impact of the MSI2-HOXA9 translocation. The relative contribution of mitochondrial metabolism and that of developmental and stem cell signals to the onset of MSI2-HOXA9 driven blast crisis CML is an important avenue of future work.

References

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(8) Riether, C., Schürch, C. M., Flury, C., Hinterbrandner, M., Drück, L., Huguenin, A. L., Baerlocher, G. M., Radpour, R. & Ochsenbein, A. F. 2015. Tyrosine kinase inhibitor-induced CD70 expression mediates drug resistance in leukemia stem cells by activating Wnt signaling. Sci Transl Med 7: 298ra119.

(9) Venton, G., Pérez-Alea, M., Baier, C., Fournet, G., Quash, G., Labiad, Y., Martin, G., Sanderson, F., Poullin, P., Suchon, P., Farnault, L., Nguyen, C., Brunet, C., Ceylan, I. & Costello, R. T. 2016. Aldehyde dehydrogenases inhibition eradicates leukemia stem cells while sparing normal progenitors. Blood Cancer J 6: e469. PMC5056970.

(10) Yin, D. D., Fan, F. Y., Hu, X. B., Hou, L. H., Zhang, X. P., Liu, L., Liang, Y. M. & Han, H. 2009. Notch signaling inhibits the growth of the human chronic myeloid leukemia cell line K562. Leuk Res 33: 109-114.

(11) Kang, Y. A., Pietras, E. M. & Passegué, E. 2020. Deregulated Notch and Wnt signaling activates early-stage myeloid regeneration pathways in leukemia. J Exp Med 217. PMC7062512.

eLife assessment

This study provides useful data substantiating a role of long noncoding RNAs in liver metabolism and organismal physiology. With murine knockout and knockin models, the authors invoke a previously unidentified role for the lncRNA Snhg3 in fatty liver. While certain findings are backed by solid evidence, other conclusions require more support and should be consolidated with existing paradigms in the field.

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors investigate the contributions of the long noncoding RNA snhg3 in liver metabolism and MAFLD. The authors conclude that liver-specific loss or overexpression of Snhg3 impacts hepatic lipid content and obesity through epigenetic mechanisms. More specifically, the authors invoke that the nuclear activity of Snhg3 aggravates hepatic steatosis by altering the balance of activating and repressive chromatin marks at the Pparg gene locus. This regulatory circuit is dependent on a transcriptional regulator SNG1.

Strengths:

The authors developed a tissue-specific lncRNA knockout and KI models. This effort is certainly appreciated as few lncRNA knockouts have been generated in the context of metabolism. Furthermore, lncRNA effects can be compensated in a whole organism or show subtle effects in acute versus chronic perturbation, rendering the focus on in vivo function important and highly relevant. In addition, Snhg3 was identified through a screening strategy and as a general rule the authors the authors attempt to follow unbiased approaches to decipher the mechanisms of Snhg3.

Weaknesses:

Despite efforts at generating a liver-specific knockout, the phenotypic characterization is not focused on the key readouts. Notably missing are rigorous lipid flux studies and targeted gene expression/protein measurement that would underpin why the loss of Snhg3 protects from lipid accumulation. Along those lines, claims linking the Snhg3 to MAFLD would be better supported with careful interrogation of markers of fibrosis and advanced liver disease. In other areas, significance is limited since the presented data is either not clear or rigorous enough. Finally, there is an important conceptual limitation to the work since PPARG is not established to play a major role in the liver.

Reviewer #2 (Public Review):

Through RNA analysis, Xie et al found LncRNA Snhg3 was one of the most down-regulated Snhgs by a high-fat diet (HFD) in mouse liver. Consequently, the authors sought to examine the mechanism through which Snhg3 is involved in the progression of metabolic dysfunction-associated fatty liver diseases (MASLD) in HFD-induced obese (DIO) mice. Interestingly, liver-specific Sngh3 knockout was reduced, while Sngh3 over-expression potentiated fatty liver in mice on an HFD. Using the RNA pull-down approach, the authors identified SND1 as a potential Sngh3 interacting protein. SND1 is a component of the RNA-induced silencing complex (RISC). The authors found that Sngh3 increased SND1 ubiquitination to enhance SND1 protein stability, which then reduced the level of repressive chromatin H3K27me3 on PPARg promoter. The upregulation of PPARg, a lipogenic transcription factor, thus contributed to hepatic fat accumulation.

The authors propose a signaling cascade that explains how LncRNA sngh3 may promote hepatic steatosis. Multiple molecular approaches have been employed to identify molecular targets of the proposed mechanism, which is a strength of the study. There are, however, several potential issues to consider before jumping to a conclusion.

(1) First of all, it's important to ensure the robustness and rigor of each study. The manuscript was not carefully put together. The image qualities for several figures were poor, making it difficult for the readers to evaluate the results with confidence. The biological replicates and numbers of experimental repeats for cell-based assays were not described. When possible, the entire immunoblot imaging used for quantification should be presented (rather than showing n=1 representative). There were multiple mislabels in figure panels or figure legends (e.g., Figure 2I, Figure 2K, and Figure 3K). The b-actin immunoblot image was reused in Figure 4J, Figure 5G, and Figure 7B with different exposure times. These might be from the same cohort of mice. If the immunoblots were run at different times, the loading control should be included on the same blot as well.

(2) The authors can do a better job in explaining the logic for how they came up with the potential function of each component of the signaling cascade. Sngh3 is down-regulated by HFD. However, the evidence presented indicates its involvement in promoting steatosis. In Figure 1C, one would expect PPARg expression to be up-regulated (when Sngh3 was down-regulated). If so, the physiological observation conflicts with the proposed mechanism. In addition, SND1 is known to regulate RNA/miRNA processing. How do the authors rule out this potential mechanism? How about the hosting snoRNA, Snord17? Does it involve the progression of NASLD?

(3) The role of PPARg in fatty liver diseases might be a rodent-specific phenomenon. PPARg agonist treatment in humans may actually reduce ectopic fat deposition by increasing fat storage in adipose tissues. The relevance of the findings to human diseases should be discussed.

eLife assessment

This is a mechanistic study showing the effect of combining inhibition of autophagy (through ULK1/2) and KRAS (using sotorasib) on KRAS mutant NSCLC making the study valuable to cancer biologists and more broadly in a clinical setting. The evidence generated by GEM mouse models and cell lines is solid but could be further strengthened by increasing the mouse cohort size. This study holds translational relevance beyond NSCLC to other indications that carry KRAS mutations.

Reviewer #1 (Public Review):

Summary:

Given that KRAS inhibition approaches are a relatively new innovation and that resistance is now being observed to such therapies in patients with NSCLC, investigation of combination therapies is valuable. The manuscript furthers our understanding of combination therapy for KRAS mutant non-small cell lung cancer by providing evidence that combined inhibition of ULK1/2 (and therefore autophagy) and KRAS can inhibit KRAS-mutant lung cancer growth. The manuscript will be of interest to the lung cancer community but also to researchers in other cancer types where KRAS inhibition is relevant.

Strengths:

The manuscript combines cell line, cell line-derived xenograft, and genetically-engineered mouse model data to provide solid evidence for the proposed combination therapy.

The manuscript is well written, and experiments are broadly well performed and presented.

Weaknesses:

With 3-4 mice per group in many experiments, experimental power is a concern and some comparisons (e.g. mono vs combination therapy) seem to be underpowered to detect a difference. Both male and female mice are used in experiments which may increase variability.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Ghazi et reported that inhibition of KRASG12C signaling increases autophagy in KRASG12C-expressing lung cancer cells. Moreover, the combination of DCC 3116, a selective ULK1/2 inhibitor, plus sotorasib displays cooperative/synergistic suppression of human KRASG12C-driven lung cancer cell proliferation in vitro and tumor growth in vivo. Additionally, in genetically engineered mouse models of KRASG12C-driven NSCLC, inhibition of either KRASG12C or ULK1/2 decreases tumor burden and increases mouse survival. Additionally, this study found that LKB1 deficiency diminishes the sensitivity of KRASG12C/LKB1Null-driven lung cancer to the combination treatment, perhaps through the emergence of mixed adeno/squamous cell carcinomas and mucinous adenocarcinomas.

Strengths:

Both human cancer cells and mouse models were employed in this study to illustrate that inhibiting ULK1/2 could enhance the responsiveness of KRASG12C lung cancer to sotorasib. This research holds translational importance.

Weaknesses:

Additional validation of certain data is necessary.

(1) mCherry-EGFP-LC3 reporter was used to assess autophagy flux in Figure 1A. Please explain how autophagy status (high, medium, and low) was defined. It's also suggested to show WB of LC3 processing in different treatments as in Figure 1A at 48 hours.

(2) For Figures 1J, K, and L, please provide immunohistochemistry (IHC) images demonstrating RAS downstream signaling blockade by sotorasib and autophagy blockade by DCC 3116 in tumors.

(3) Given that both DCC 3116 and ULK1K46N exhibit the ability to inhibit autophagy and synergize with sotorasib in inhibiting cell proliferation, in addition to demonstrating decreased levels of pATG13 via ELISA assay, please include Western blot analyses of LC3 or p62 to confirm the blockade of autophagy by DCC 3116 and ULK1K46N in Figure 1 & Figure 2.

(4) Since adenocarcinomas, adenosquamous carcinomas (ASC), and mucinous adenocarcinomas were detected in KL lung tumors, please conduct immunohistochemistry (IHC) to detect these tumors, including markers such as p63, SOX2, Katrine 5.

(5) Please provide the sample size (n) for each treatment group in the survival study (Figure 4E). It appears that all mice were sacrificed for tumor burden analysis in Figure 4F. However, there doesn't seem to be a significant difference among the treatment groups in Figure 4F, which contrasts with the survival analysis in Figure 4E. It is suggested to increase the sample size in each treatment group to reduce variation.

(6) In KP mice (Figure 5), it seems that a single treatment alone is sufficient to inhibit established KP lung tumor growth. Combination treatment does not further enhance anti-tumor efficacy. Therefore, this result doesn't support the conclusion generated from human cancer cell lines. Please discuss.

eLife assessment

This fundamental paper reports a new biosensor to study G protein-coupled receptor activation by the pituitary adenylyl cyclase-activating polypeptide (PACAP) in cell culture, ex vivo (mouse brain slices), and in vivo (zebrafish). Convincing data are presented that show the new sensor works, albeit at very high (non-physiological) concentrations of exogenous PACAP. The sensor has not yet been used to detect endogenously released PACAP, raising questions about whether the sensor can be used for its intended purpose. While further work must be pursued to achieve broad in vivo applications under physiological conditions, the new tool will be of interest to cell biologists, especially those studying the large GPCR family.

Reviewer #1 (Public Review):

Summary:

This study assumes but also demonstrates that auditory rhythm processing is produced by internal oscillating systems and evaluates the properties of internal oscillators across individuals. The authors designed an experiment and performed analyses that address individuals' preferred rate and flexibility, with a special focus on how much past rhythms influence subsequent trials. They find evidence for such historical dependence and show that we adapt less well to new rhythms as we age. Furthermore, the revised version of this manuscript includes evidence for detuning; i.e., a gradual reduction in accuracy as the difference between a participant's preferred rate and stimulus rate increases. Such detuning also correlates with modelled oscillator flexibility measures. Such outcomes increase our credence that an entrainment-based interpretation is indeed warranted. Regardless of mechanism though, this work contributes to our understanding of individual differences in rhythm processing.

Strengths:

The inclusion of two tasks -- a tapping and a listening task -- complement each other methodologically. By analysing both the production and tracking of rhythms, the authors emphasize the importance of the characteristics of the receiver, the external world, and their interplay. The relationship between the two tasks and components within tasks are explored using a range of analyses. The visual presentation of the results is very clear. The age-related changes in flexibility are useful and compelling. The paper includes a discussion of the study assumptions, and it contextualizes itself more explicitly as taking entrainment frameworks as a starting point. Finally, the revised versions show creative additional analyses that increase our credence in an entrainment-based interpretation versus an interpretation of timekeeper other models, increasing the theoretical relevance of this study as compared to previous work.

Weaknesses:

The authors have addressed many of the weaknesses of previous peer review rounds. One final point is that our credence in an entrainment-based interpretation of these results could further increase by not only carefully outlining what is expected under entrainment (as is now done), but to also specify more extensively what predictions emerge from a timekeeper or other model, and how these data do not bear out such predictions.

Author response:

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

We thank the reviewers for their thorough re-evaluation of our revised manuscript. Addressing final issues they raised has improved the manuscript further. We sincerely appreciate the detailed explanations that the reviewers provided in the "recommendations for authors" section. This comprehensive feedback helped us identify the sources of ambiguity within the analysis descriptions and in the discussion where we interpreted the results. Below, you will find our responses to the specific comments and recommendations.

Reviewer #1 (Recommendations):

(1) I find that the manuscript has improved significantly from the last version, especially in terms of making explicit the assumptions of this work and competing models. I think the response letter makes a good case that the existence of other research makes it more likely that oscillators are at play in the study at hand (though the authors might consider incorporating this argumentation a bit more into the paper too). Furthermore, the authors' response that the harmonic analysis is valid even when including x=y because standard correlation analysis were not significant is a helpful response. The key issue that remains for me is that I have confusions about the additional analyses prompted by my review to a point where I find it hard to evaluate how and whether they demonstrate entrainment or not. 

First, I don't fully understand Figure 2B and how it confirms the Arnold tongue slice prediction. In the response letter the authors write: "...indicating that accuracy increased towards the preferred rate at fast rates and decreased as the stimulus rate diverged from the preferred rate at slow rates". The figure shows that, but also more. The green line (IOI < preferred rate) indeed increases toward the preferred rate (which is IOI = 0 on the x-axis; as I get it), but then it continues to go up in accuracy even after the preferred rate. And for the blue line, performance also continues to go up beyond preferred rate. Wouldn't the Arnold tongue and thus entrainment prediction be that accuracy goes down again after the preferred rate has passed? That is to say, shouldn't the pattern look like this (https://i.imgur.com/GPlt38F.png) which with linear regression should turn to a line with a slope of 0?

This was my confusion at first, but then I thought longer about how e.g. the blue line is predicted only using trials with IOI larger than the preferred rate. If that is so, then shouldn't the plot look like this? (https://i.imgur.com/SmU6X73.png). But if those are the only data and the rest of the regression line is extrapolation, why does the regression error vary in the extrapolated region? It would be helpful if the authors could clarify this plot a bit better. Ideally, they might want to include the average datapoints so it becomes easier to understand what is being fitted. As a side note, colours blue/green have a different meaning in 2B than 2D and E, which might be confusing. 

We thank the reviewer for their recommendation to clarify the additional analyses we ran in the previous revision to assess whether accuracy systematically increased toward the preferred rate estimate. We realized that the description of the regression analysis led to misunderstandings. In particular, we think that the reviewer interpreted (1) our analysis as linear regression (based on the request to plot raw data rather than fits), whereas, in fact, we used logistic regression, and (2) the regression lines in Figure 2B as raw IOI values, while, in fact, they were the z-scored IOI values (from trials where stimulus IOI were faster than an individual’s preferred rate, IOI < preferred rate, in green; and from trials stimulus IOI were slower than an individual’s preferred rate, IOI > preferred rate, in blue), as the x axis label depicted. We are happy to have the opportunity to clarify these points in the manuscript. We have also revised Figure 2B, which was admittedly maybe a bit opaque, to more clearly show the “Arnold tongue slice”.  

The logic for using (1) logistic regression with (2) Z-scored IOI values as the predictor is as follows. Since the response variable in this analysis, accuracy, was binary (correct response = 1, incorrect response = 0), we used a logistic regression. The goal was to quantify an acrosssubjects effect (increase in accuracy toward preferred rate), so we aggregated datasets across all participants into the model. The crucial point here is that each participant had a different preferred rate estimate. Let’s say participant A had the estimate at IOI = 400 ms, and participant B had an estimate at IOI = 600 ms. The trials where IOI was faster than participant A’s estimate would then be those ranging from 200 ms to 398 ms, and those that were slower would range from 402 ms to 998 ms. For Participant B, the situation would be different:  trials where IOI was faster than their estimate would range from 200 ms to 598 ms, and slower trials would range between 602 ms to 998 ms. For a fair analysis that assesses the accuracy increase, regardless of a participant’s actual preferred rate, we normalized these IOI values (faster or slower than the preferred rate). Zscore normalization is a common method of normalizing predictors in regression models, and was especially important here since we were aggregating predictors across participants, and the predictors ranges varied across participants. Z-scoring ensured that the scale of the sample (that differs between participant A and B, in this example) was comparable across the datasets. This is also important for the interpretation of Figure 2B. Since Z-scoring involves mean subtraction, the zero point on the Z-scaled IOI axis corresponds to the mean of the sample prior to normalization (for Participant A: 299 ms, for Participant B: 399 ms) and not the preferred rate estimate. We have now revised Figure 2B in a way that we think makes this much clearer.  

The manuscript text includes clarification that the analyses included logistic regression and stimulus IOI was z-scored: 

“In addition to estimating the preferred rate as stimulus rates with peak performance, we investigated whether accuracy increased as a function of detuning, namely, the difference between stimulus rate and preferred rate, as predicted by the entrainment models (Large, 1994; McAuley, 1995; Jones, 2018). We tested this prediction by assessing the slopes of mixed-effects logistic regression models, where accuracy was regressed on the IOI condition, separately for stimulus rates that were faster or slower than an individual’s preferred rate estimate. To do so, we first z-scored IOIs that were faster and slower than the participant’s preferred rate estimates, separately to render IOI scales comparable across participants.” (p. 7)

While thinking through the reviewer’s comment, we realized we could improve this analysis by fitting mixed effects models separately to sessions’ data. In these models, fixed effects were z-scored IOI and ‘detuning direction’ (i.e., whether IOI was faster or slower than the participant’s preferred rate estimate). To control for variability across participants in the predicted interaction between z-scored IOI and direction, this interaction was added as a random effect. 

“Ideally, they might want to include the average datapoints so it becomes easier to understand what is being fitted.”

Although we agree with the reviewer that including average datapoints in a figure in addition to model predictions usually better illustrates what is being fitted than the fits alone, this doesn’t work super well for logistic regression, since the dependent variable is binary. To try to do a better job illustrating single-participant data though, we instead  fitted logistic models to each participant’s single session datasets, separately to conditions where z-scored IOI from fasterthan-preferred rate trials, and those from slower-than-preferred rate trials, predicted accuracy. From these single-participant models, we obtained slope values, we referred to as ‘relative detuning slope’, for each condition and session type. This analysis allowed us to illustrate the effect of relative detuning on accuracy for each participant. Figure 2B now shows each participant’s best-fit lines from each detuning direction condition and session.

Since we now had relative detuning slopes for each individual (which we did not before), we took advantage of this to assess the relationship between oscillator flexibility and the oscillator’s behavior in different detuning situations (how strongly leaving the preferred rate hurt accuracy, as a proxy for the width of the Arnold tongue slice). Theoretically, flexible oscillators should be able to synchronize to wide range of rates, not suffering in conditions where detuning is large (Pikovsky et al., 2003). Conversely, synchronization of inflexible oscillators should depend strongly on detuning. To test whether our flexibility measure predicted this dependence on detuning, which is a different angle on oscillator flexibility, we first averaged each participant’s detuning slopes across detuning directions (after sign-flipping one of them). Then, we assessed the correlation between the average detuning slopes and flexibility estimates, separately from conditions where |-𝚫IOI| or |+𝚫IOI| predicted accuracy. The results revealed significant negative correlations (Fig. 2F), suggesting that performance of individuals with less flexible oscillators suffered more as detuning increased. Note that flexibility estimates quantified how much accuracy decreased as a function of trial-to-trial changes in stimulus rate (±𝚫IOI). Thus, these results show that oscillators that were robust to changes in stimulus rate were also less dependent on detuning to be able to synchronize across a wide range of stimulus rates. We are excited to be able to provide this extra validation of predictions made by entrainment models. 

To revise the manuscript with the updated analysis on detuning:

• We added the descriptions of the analyses to the Experiment 1 Methods section.

Calculation of detuning slopes and their averaging procedure are in Preferred rate estimates:

“In addition to estimating the preferred rate as stimulus rates with peak performance, we investigated whether accuracy increased as a function of detuning, namely, the difference between stimulus rate and preferred rate, as predicted by the entrainment models (Large, 1994; McAuley, 1995; Jones, 2018). We tested this prediction by assessing the slopes of mixed-effects logistic regression models, where accuracy was regressed on the IOI condition, separately for stimulus rates that were faster or slower than an individual’s preferred rate estimate. To do so, we first z-scored IOIs that were faster and slower than the participant’s preferred rate estimates, separately to render IOI scales comparable across participants. The detuning direction (i.e., whether stimulus IOI was faster or slower than the preferred rate estimate) was coded categorically. Accuracy (binary) was predicted by these variables (zscored IOI, detuning direction), and their interaction. The model was fitted separately to datasets from random-order and linear-order sessions, using the fitglme function in MATLAB. Fixed effects were z-scored IOI and detuning direction and random effect was their interaction. We expected a systematic increase in performance toward the preferred rate, which would result in a significant interaction between stimulus rate and detuning direction. To decompose the significant interaction and to visualize the effects of detuning, we fitted separate models to each participant’s single-session datasets, and obtained slopes from each direction condition, hereafter denoted as the ‘relative-detuning slope’. We treated relative-detuning slope as an index of the magnitude of relative detuning effects on accuracy. We then evaluated these models, using the glmval function in MATLAB to obtain predicted accuracy values for each participant and session. To visualize the relative-detuning curves, we averaged the predicted accuracies across participants within each session, separately for each direction condition (faster or slower than the preferred rate). To obtain a single value of relative-detuning magnitude for each participant, we averaged relative detuning slopes across direction conditions. However, since slopes from IOI > preferred rate conditions quantified an accuracy decrease as a function of detuning, we sign-flipped these slopes before averaging. The resulting average relative detuning slopes, obtained from each participant’s single-session datasets, quantified how much the accuracy increase towards preferred rate was dependent on, in other words, sensitive to, relative detuning.” (p. 7-8)

• We added the information on the correlation analyses between average detuning slopes in Flexibility estimates.

“We further tested the relationship between the flexibility estimates (𝛽 from models where |𝚫IOI| or |+𝚫IOI| predicted accuracy) and average detuning slopes (see Preferred rate estimates) from random-order sessions. We predicted that flexible oscillators (larger 𝛽) would be less severely affected by detuning, and thus have smaller detuning slopes. Conversely, inflexible oscillators (smaller 𝛽) should have more difficulty in adapting to a large range of stimulus rates, and their adaptive abilities should be constrained around the preferred rate, as indexed by steeper relative detuning slopes.” (p. 8)

• We provided the results in Experiment 1 Results section.

“Logistic models assessing a systematic increase in accuracy toward the preferred rate estimate in each session type revealed significant main effects of IOI (linear-order session: 𝛽 = 0.264, p < .001; random-order session: 𝛽 = 0.175, p < .001), and significant interactions between IOI and direction (linear-order session: 𝛽 = -0.444, p < .001; random-order session: 𝛽 = -0.364, p < .001), indicating that accuracy increased as fast rates slowed toward the preferred rate (positive slopes) and decreased again as slow rates slowed further past the preferred rate (negative slopes), regardless of the session type. Fig. 2B illustrates the preferred rate estimation method for an example participant’s dataset and shows the predicted accuracy values from models fitted to each participant’s single-session datasets. Note that the main effect and interaction were obtained from mixed effects models that included aggregated datasets from all participants, whereas the slopes quantifying the accuracy increase as a function of detuning (i.e., relative detuning slopes) were from models fitted to single-participant datasets.” (p. 9-10)

“We tested the relationship between the flexibility estimates and single-participant relative detuning slopes from random-order sessions (Fig. 2B). The results revealed negative correlations between the relative detuning slopes and flexibility estimates, both with 𝛽 (r(23) =0.529, p = 0.007) from models where |-𝚫IOI| predicted accuracy (adapting to speeding-up trials), and 𝛽 (r(23) =-0.580, p = 0.002) from models where |+𝚫IOI| predicted accuracy (adapting to slowing-down trials). That is, the performance of individuals with less flexible oscillators suffered more as detuning increased. These results are shown in Fig. 2F.” (p. 10)

• We modified Figure 2. In Figure 2B, there are now separate subfigures with the z-scored IOI faster (left) or slower (right) than the preferred rate predicting accuracy. We illustrated the correlations between average relative detuning slopes and flexibility estimates in Figure 2F. 

Author response image 1.

Main findings of Experiment 1. A Left: Each circle represents a single participant’s preferred rate estimate from the random-order session (x axis) and linear-order session (y axis). The histograms along the top and right of the plot show the distributions of estimates for each session type. The dotted and dashed lines respectively represent 1:2 and 2:1 ratio between the axes, and the solid line represents one-to-one correspondence. Right: permutation test results. The distribution of summed residuals (distance of data points to the closest y=x, y=2*x and y=x/2 lines) of shuffled data over 1000 iterations, and the summed residual from original data (dashed line) that fell below .008 of the permutation distribution. B Top: Illustration of the preferred rate estimation method from an example participant’s linear-order session dataset. Estimates were the stimulus rates (IOI) where smoothed accuracy (orange line) was maximum (arrow). The dotted lines originating from the IOI axis delineate the stimulus rates that were faster (left, IOI < preferred rate) and slower (right, IOI > preferred rate) than the preferred rate estimate and expand those separate axes, the values of which were Z-scored for the relative-detuning analysis. Bottom: Predicted accuracy, calculated from single-participant models where accuracy in random-order (purple) and linear-order (orange) sessions was predicted by z-scored IOIs that were faster than a participant’s preferred rate estimate (left), and by those that were slower (right). Thin lines show predicted accuracy from single-participant models, solid lines show the averages across participants and the shaded areas represent standard error of the mean. Predicted accuracy is maximal at the preferred rate and decreases as a function of detuning. C Average accuracy from random-order (left, purple) and linear-order (right, orange) sessions. Each circle represents a participant’s average accuracy. D Flexibility estimates. Each circle represents an individuals’ slope (𝛽) obtained from logistic models, fitted separately to conditions where |𝚫IOI| (left, green) or |+𝚫IOI| (right blue) predicted accuracy, with greater values (arrow’s direction) indicating better oscillator flexibility. The means of the distributions of 𝛽 from both conditions were smaller than zero (dashed line), indicating a negative effect of between-trial absolute rate change on accuracy. E Participants’ average bias from |𝚫IOI| (green), and |+𝚫IOI| (blue) conditions in random-order (left) and linear-order (right) sessions. Negative bias indicates underestimation of the comparison intervals, positive bias indicates the opposite. Box plots in C-E show median (black vertical line), 25th and 75th percentiles (box edges) and extreme datapoints (whiskers). In C and E, empty circles show outlier values that remained after data cleaning procedures. F Correlations between participants’ average relative detuning slopes, indexing the steepness of the increase in accuracy towards the preferred rate estimate (from panel B), and flexibility estimates from |-𝚫IOI| (top, green), and |+𝚫IOI| (bottom, blue) conditions (from panel C). Solid black lines represent the best-fit line, dashed lines represent 95% confidence intervals.

• We discussed the results in General Discussion and emphasized that only entrainment models, compared to timekeeper models, predict a relationship between detuning and accuracy that is amplified by oscillator’s inflexibility: “we observed systematic increases in task accuracy (Experiment 1) toward the best-performance rates (i.e., preferred rate estimates), with the steepness of this increase being closely related to the effects of rate change (i.e., oscillator flexibility). Two interdependent properties of an underlying system together modulating an individual’s timing responses show strong support for the entrainment approach” (p. 24)

“As a side note, colours blue/green have a different meaning in 2B than 2D and E, which might be confusing.” 

Upon the reviewer’s recommendation, we changed the color scale across Figure 2, such that colors refer to the same set of conditions across all panels. 

(2) Second, I don't understand the additional harmonic relationship analyses in the appendix, and I suspect other readers will not either. As with the previous point, it is not my view that the analyses are faulty or inadequate, it is rather that the lack of clarity makes it challenging to evaluate whether they support an entrainment model or not. 

We decided to remove the analysis that was based on a circular approach, and we have clarified the analysis that was based on a modular approach by giving example cases: 

“We first calculated how much the slower estimate (larger IOI value) diverts, proportionally from the faster estimate (smaller IOI value) or its multiples (i.e., harmonics) by normalizing the estimates from both sessions by the faster estimate. The outcome measure was the modulus of the slower, with respect to the faster estimate, divided by the faster estimate, described as mod(max(X), min(X))/min(X) where X = [session1_estimate session2_estimate]. An example case would be a preferred rate estimate of IOI = 603 ms from the linear-order session and an estimate of IOI = 295 ms from the random-order session. In this case, the slower estimate (603 ms) diverts from the multiple of the faster estimate (295*2 = 590 ms) by 13 ms, a proportional deviation of 4% of the faster estimate (295 ms). The outcome measure in this example is calculated as mod(603,295)/295 = 0.04.” (Supplementary Information, p. 2)

Crucially, the ability of oscillators to respond to harmonically-related stimulus rates is a main distinction between entrainment and interval (timekeeper) models. In the current study, we found that each participant’s best-performance rates, the preferred rate estimates, had harmonic relationships. The additional analyses further showed that these harmonic relationships were not due to chance. This finding speaks against the interval (timekeeper) approaches and is maximally compatible with the entrainment framework. 

Here are a number of questions I would like to list to sketch my confusion: 

• The authors write: "We first normalized each participant's estimates by rescaling the slower estimate with respect to the faster one and converting the values to radians". Does slower estimate mean: "task accuracy in those trials in which IOI was slower than a participant's preferred frequency"? 

Preferred rate estimates were stimulus rates (IOI) with best performance, as described in Experiment 1 Methods section. 

“We conceptualized individuals' preferred rates as the stimulus rates where durationdiscrimination accuracy was highest. To estimate preferred rate on an individual basis, we smoothed response accuracy across the stimulus-rate (IOI) dimension for each session type, using the smoothdata function in Matlab. Estimates of preferred rate were taken as the smoothed IOI that yielded maximum accuracy” (p. 7). 

The estimation method and the resulting estimate for an example participant was provided in Figure 2B. The updated figure in the current revision has this illustration only for linear-order session. 

“Estimates were the stimulus rates (IOI) where smoothed accuracy (orange line) was maximum (arrow)” (Figure caption, p. 9).

• "We reasoned that values with integer-ratio relationships should correspond to the same phase on a unit circle". What is values here; IOI, or accuracy values for certain IOIs? And why should this correspond to the same phase? 

We removed the analysis on integer-ratio relationships that was based on a circular approach that the reviewer is referring to here. We clarified the analysis that was based on a modular approach and avoided using the term ‘values’ without specifying what values corresponded to.

• Des "integer-ratio relationships" have to do with the y=x, y=x*2 and y=x/2 relationships of the other analyses?  

Integer-ratio relationships indeed refer to y=x, y=x*2 and y=x/2 relationships. For example, if a number y is double of another number x (y = x*2), these values have an integer-ratio relationship, since 2 is an integer. This holds true also for the case where y = x/2 since x = y*2. 

• Supplementary Figure S2c shows a distribution of median divergences resulting from the modular approach. The p-value is 0.004 but the dashed line appears to be at a much higher percentile of the distribution. I find this hard to understand. 

We thank the reviewer for a detailed inspection of all figures and information in the manuscript. The reviewer’s comment led us to realize that this figure had an error. We updated the figure in Supplementary Information (Supplementary Figure S2). 

Reviewer #2 (Public Review):

To get a better understanding of the mechanisms underlying the behavioral observations, it would have been useful to compare the observed pattern of results with simulations done with existing biophysical models. However, this point is addressed if the current study is read along with this other publication of the same research group: Kaya, E., & Henry, M. J. (2024, February 5). Modeling rhythm perception and temporal adaptation: top-down influences on a gradually decaying oscillator.       https://doi.org/10.31234/osf.io/q9uvr 

We agree with the reviewer that the mechanisms underlying behavioral responses can be better understood by modeling approaches. We thank the reviewer for acknowledging our computational modeling study that addressed this concern. 

Reviewer #2 (Recommendations):

I very much appreciate the thorough work done by the authors in assessing all reviewers' concerns. In this new version they clearly state the assumptions to be tested by their experiments, added extra analyses further strengthening the conclusions and point the reader to a neurocomputational model compatible with the current observations. 

I only regret that the authors misunderstood the take home message of our Essay (Doelling & Assaneo 2021). Despite this being obviously out of the scope of the current work, I would like to take this opportunity to clarify this point. In that paper, we adopted a Stuart-Landau model not to determine how an oscillator should behave, but as an example to show that some behaviors usually used to prove or refute an underlying "oscillator like" mechanism can be falsified. We obviously acknowledge that some of the examples presented in that work are attainable by specific biophysical models, as explicitly stated in the essay: "There may well be certain conditions, equations, or parameters under which some of these commonly held beliefs are true. In that case, the authors who put forth these claims must clearly state what these conditions are to clarify exactly what hypotheses are being tested." 

This work did not mean to delineate what oscillator is (or in not), but to stress the importance of explicitly introducing biophysical models to be tested instead of relying on vague definitions sometimes reflecting the researchers' own beliefs. The take home message that we wanted to deliver to the reader appears explicitly in the last paragraph of that essay: "We believe that rather than concerning ourselves with supporting or refuting neural oscillators, a more useful framework would be to focus our attention on the specific neural dynamics we hope to explain and to develop candidate quantitative models that are constrained by these dynamics. Furthermore, such models should be able to predict future recordings or be falsified by them. That is to say that it should no longer be sufficient to claim that a particular mechanism is or is not an oscillator but instead to choose specific dynamical systems to test. In so doing, we expect to overcome our looping debate and to ultimately develop-by means of testing many model types in many different experimental conditions-a fundamental understanding of cognitive processes and the general organization of neural behavior." 

We appreciate the reviewer’s clarification of the take-home message from Doelling and Assaneo (2021). We concur with the assertions made in this essay, particularly regarding the benefits of employing computational modeling approaches. Such methodologies provide a nuanced and wellstructured foundation for theoretical predictions, thereby minimizing the potential for reductionist interpretations of behavioral or neural data.

In addition, we would like to underscore the significance of delineating the level of analysis when investigating the mechanisms underlying behavioral or neural observations. The current study or Kaya & Henry (2024) involved no electrophysiological measures. Thus, we would argue that the appropriate level of analysis across our studies concerns the theoretical mechanisms rather than how these mechanisms are implemented on the neural (physical) level. In both studies, we aimed to explore or approximate the theoretical oscillator that guides dynamic attention rather than the neural dynamics underlying these theoretical processes. That is, theoretical (attentional) entrainment may not necessarily correspond to neural entrainment, and differentiating these levels could be informative about the parallels and differences between these levels. 

References

Doelling, K. B., & Assaneo, M. F. (2021). Neural oscillations are a start toward understanding brain activity rather than the end. PLoS Biol, 19(5), e3001234. https://doi.org/10.1371/journal.pbio.3001234  Jones, M. R. (2018). Time will tell: A theory of dynamic attending. Oxford University Press. 

Kaya, E., & Henry, M. J. (2024). Modeling rhythm perception and temporal adaptation: top-down influences on a gradually decaying oscillator. PsyArxiv. https://doi.org/https://doi.org/10.31234/osf.io/q9uvr 

Large, E. W. (1994). Dynamic representation of musical structure. The Ohio State University. 

McAuley, J. D. (1995). Perception of time as phase: Toward an adaptive-oscillator model of rhythmic pattern processing Indiana University Bloomington]. 

Pikovsky, A., Rosenblum, M., & Kurths, J. (2003). Synchronization: A Universal Concept in Nonlinear Sciences. Cambridge University Press.

eLife assessment

This important study has practical and theoretical implications for understanding rhythm perception and production in human cognition. The evidence for individual frequency preferences and a deterioration in frequency adaptation with age is convincing. These findings will inform existing models of rhythm perception and production, and the reported effects of age may have clinical implications.

Reviewer #2 (Public Review):

Summary:

The current work describes a set of behavioral tasks to explore individual differences in the preferred perceptual and motor rhythms. Results show a consistent individual preference for a given perceptual and motor frequency across tasks and, while these were correlated, the latter is slower than the former one. Additionally, the adaptation accuracy to rate changes is proportional to the amount of rate variation and, crucially, the amount of adaptation decreases with age.

Strengths:

Experiments are carefully designed to measure individual preferred motor and perceptual tempo. Furthermore, the experimental design is validated by testing the consistency across tasks and test-retest, what makes the introduced paradigm a useful tool for future research.<br /> The obtained data is rigorously analyzed using a diverse set of tools, each adapted to the specificities across the different research questions and tasks.<br /> This study identifies several relevant behavioral features: (i) each individual shows a preferred and reliable motor and perceptual tempo and, while both are related, the motor is consistently slower than the pure perceptual one; (ii) the presence of hysteresis in the adaptation to rate variations; and (iii) the decrement of this adaptation with age. All these observations are valuable for the auditory-motor integration field of research, and they could potentially inform existing biophysical models to increase their descriptive power.

Weaknesses:

To get a better understanding of the mechanisms underlying the behavioral observations, it would have been useful to compare the observed pattern of results with simulations done with existing biophysical models. However, this point is addressed if the current study is read along with this other publication of the same research group: Kaya, E., & Henry, M. J. (2024, February 5). Modeling rhythm perception and temporal adaptation: top-down influences on a gradually decaying oscillator. https://doi.org/10.31234/osf.io/q9uvr

Author response:

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

Reviewer #1 (Comments to the Author):

Summary:

In this study, Xie and colleagues aimed to explore the function and potential mechanisms of the gut microbiota in a hamster model of severe leptospirosis. The results demonstrated that Leptospira infection was able to cause intestine damage and inflammation. Leptospira infection promoted an expansion of Proteobacteria, increased gut barrier permeability, and elevated LPS levels in the serum. Thus, they proposed an LPS-neutralization therapy which improved the survival rate of moribund hamsters combined with antibody therapy or antibiotic therapy.

Strengths:

The work is well-designed and the story is interesting to me. The gut microbiota is essential for immunity and systemic health. Many life-threatening pathogens, such as SARS-CoV-2 and other gut-damaged infection, have the potential to disrupt the gut microbiota in the later stages of infection, causing some harmful gut microbiota-derived substances to enter the bloodstream. It is emphasized that in addition to exogenous pathogenic pathogens, harmful substances of intestinal origin should also be considered in critically ill patients.

Weaknesses:

Q1: There are many serotypes of Leptospira, it is suggested to test another pathogenic serotype of Leptospira to validate the proposed therapy.

That’s a constructive suggestion. We have tested another pathogenic serotype of Leptospira (L. interrogans serovar Autumnalis strain 56606) to verify the LPS-neutralization therapy combined with antibiotic therapy (Supplementary Fig. S9B). The results showed that the combination of the LPS-neutralization therapy with antibody therapy or antibiotic therapy also significantly improved the survival rate of hamsters infected by 56606.

Q2: Authors should explain why the infective doses of leptospires was not consistent in different study.

Thank you for your comment. To examine the role of the gut microbiota on acute leptospirosis, the infective doses of leptospires was chosen for 106, while in other sections of the study, the infective doses of leptospires was chosen for 107. In fact, we also used 107 leptospires to infect hamsters, however, the infective doses of 107 leptospires might be overdose, there was no significant difference on the survival rate between the control group and the Abx-treated group. A previous study also highlighted that the infective doses of leptospires was important in the investigating the sex on leptospirosis, as male hamsters infected with L. interrogans are more susceptible to severe leptospirosis after exposure to lower infectious doses than females (103 leptospires but not 104 leptospires) (1).

Reference

(1) GOMES C K, GUEDES M, POTULA H H, et al. Sex Matters: Male Hamsters Are More Susceptible to Lethal Infection with Lower Doses of Pathogenic Leptospira than Female Hamsters (J). Infect Immun, 2018, 86(10).

Q3: In the discussion section, it is better to supplement the discussion of the potential link between the natural route of infection and leptospirosis.

Thank for your suggestion. We have supplemented it in the discussion (line 523-527 in the track change PDF version).

Q4: Line 231, what is the solvent of thioglycolate?

We have supplemented it in the manuscript (line 242-243 in the track change PDF version).

Q5: Lines 962-964, there are some mistakes which are not matched to Figure 7.

Thank you for pointing that out, we have corrected it in the manuscript.

Reviewer #2 (Comments to the Author):

Summary:

Severe leptospirosis in humans and some mammals often meet death in the endpoint. In this article, authors explored the role of the gut microbiota in severe leptospirosis. They found that Leptospira infection promoted a dysbiotic gut microbiota with an expansion of Proteobacteria and LPS neutralization therapy synergized with antileptospiral therapy significantly improved the survival rates in severe leptospirosis. This study is well-organized and has potentially important clinical implications not only for severe leptospirosis but also for other gut-damaged infections.

Weaknesses:

Q1: In the Introduction section and Discussion section, the authors should describe and discuss more about the differences in the effect of Leptospira infection between mice and hamsters, so that the readers can follow this study better.

Thank you for your suggestion, we have supplemented it in the manuscript (line 62-66 in the track change PDF version).

Q2: Lines 92-95, the authors should explain why they chose two different routines of infection.

Thank you for your comment, we have explained it in the manuscript (line 100 in the track change PDF version).

Q3: Line 179-180, the concentration of PMB and Dox is missed, and 0.016 μg/L is just ok.

We have corrected it in the manuscript.

Q4: "μL" or "μl" and "mL" or "ml' should be uniform in the manuscript.

Thank you for your suggestion, we have revised it in the manuscript.

Q5: In the culture of primary macrophages, how many cells are inoculated in the plates should be described clearly.

We have supplemented it in the manuscript (line 250 in the track change PDF version).

Q6: Line 271, it is better to list primers used for leptospiral detection in the text. Because it allows readers to find the information they need more directly.

Thank you for your suggestions, we have supplemented it in the manuscript (line 281-284 in the track change PDF version).

Q7: Line 366-369, Lactobacillus seems to be a kind of key bacteria during Leptospira infection. A previous study (doi: 10.1371/journal.pntd.0005870) also demonstrated that pre-treatment with Lactobacillus plantarum prevented severe pathogenesis in mice. The authors should discuss the potential probiotic for leptospirosis prevention.

We have discussed it in the manuscript (line 564-566 in the track change PDF version).

Q8: Lines 450-451, not all concentrations of fecal filtration from two groups upregulated all gene expression mentioned in the text, the authors should correct it.

Thank you for pointing that out, we have corrected it in the manuscript (line 461-462 in the track change PDF version).

Reviewer #3 (Comments to the Author):

Summary:

This is a well-prepared manuscript that presented interesting research results. The only defect is that the authors should further revise the English language.

Strengths:

The omics method produced unbiased results.

Weaknesses:

Q1: LPS neutralization is not a new method for treating leptospiral infection.

Thank you for your comment. Yes, LPS neutralization is not a new method for treating leptospiral infection, most of which might focus on leptospiral LPS. In addition, Leptospira seemed to be naturally resistant to polymyxin B (1). Recently, neutralizing gut-derived LPS was applied in other diseases which significantly relieved diseases (2-3). In this study, we found that Leptospira infection promoted an expansion of Proteobacteria, increased gut barrier permeability, and elevated LPS levels in the serum. Thus, we proposed an LPS-neutralization therapy which improved the survival rate of moribund hamsters combined with antibody therapy or antibiotic therapy.

Reference

(1) LIEGEON G, DELORY T, PICARDEAU M. Antibiotic susceptibilities of livestock isolates of leptospira (J). Int J Antimicrob Agents, 2018, 51(5):693-699.

(2) MUNOZ L, BORRERO M J, UBEDA M, et al. Intestinal Immune Dysregulation Driven by Dysbiosis Promotes Barrier Disruption and Bacterial Translocation in Rats With Cirrhosis (J). Hepatology, 2019, 70(3):925-938.

(3) ZHANG X, LIU H, HASHIMOTO K, et al. The gut-liver axis in sepsis: interaction mechanisms and therapeutic potential (J). Crit Care, 2022, 26(1):213.

Q2: The authors should further revise the English language used in the text.

Thank you for your suggestion, our manuscript has been polished by American Journal Experts (certificate number: 81C8-C5C1-9D5D-109D-3F23).

Reviewer #1 (Public Review)

Summary:

In this study, Xie and colleagues aimed to explore the function and potential mechanisms of the gut microbiota in a hamster model of severe leptospirosis. The results demonstrated that Leptospira infection was able to cause intestine damage and inflammation. Leptospira infection promoted an expansion of Proteobacteria, increased gut barrier permeability, and elevated LPS levels in the serum. Thus, they proposed an LPS-neutralization therapy which improved the survival rate of moribund hamsters combined with antibody therapy or antibiotic therapy.

Strengths:

The work is well-designed and the story are interesting to me. The gut microbiota is essential for immunity and systemic health. Many life-threatening pathogens, such as SARS-CoV-2 and other gut-damaged infection, have the potential to disrupt the gut microbiota in the later stages of infection, causing some harmful gut microbiota-derived substances to enter the bloodstream. It is emphasized that in addition to exogenous pathogenic pathogens, harmful substances of intestinal origin should also be considered in critically ill patients.

eLife assessment

The gut microbiota influences many infectious diseases; however, its role Leptospirosis remains unclear. In this fundamental work, Xie et al. use a hamster model to show that Leptospira infection leads to gut pathology, an altered gut microbiota, and increased translocation. A combined use of antibiotics and LPS neutralization prolonged survival, providing a potential new therapeutic approach. This study utilizes compelling methods to provide fundamental new insights into this emerging disease, which could be dissected further in future studies aimed at gaining mechanistic insight and assessing the translational relevance of these discoveries.

Reviewer #2 (Public Review):

Severe leptospirosis in humans and some mammals often meet death in the endpoint. In this article, authors explored the role of the gut microbiota in severe leptospirosis. They found that Leptospira infection promoted a dysbiotic gut microbiota with an expansion of Proteobacteria and LPS neutralization therapy synergized with antileptospiral therapy significantly improved the survival rates in severe leptospirosis. This study is well-organized and has potentially important clinical implications not only for severe leptospirosis but also for other gut-damaged infections.

Reviewer #3 (Public Review):

Summary:

This is a well prepared manuscript which presented interesting research result.

Strengths:

The omics method produced unbiased results.

Weaknesses:

LPS neutralization is not new method for treating leptospiral infection.

eLife assessment

This useful study investigates two secreted Mycobacterium tuberculosis proteins, ESAT-6 and CFP10, using biochemical assays, including a Biolayer Interferometry assay. Solid experimental evidence demonstrates that ESAT-6 forms a tight interaction with CFP10 as a heterodimer at neutral pH and that ESAT-6 also forms a homodimer at acidic pH. Additional, more definitive evidence is required to describe how these proteins disrupt the phagosomal membrane. While improved compared to a previous version, the revised manuscript did not address these concerns adequately.

Reviewer #1 (Public Review):

Summary:

The authors sought to establish a biochemical strategy to study ESAT-6 and CFP-10 biochemistry. They established recombinant reagents to study these protein associations in vitro revealing an unexpected relationship at low pH. They next develop much needed reagents to study these proteins in an infection context and reveal that treatment with an ESAT-6 nanobody enhances Mtb control.

Strengths:

The biochemical conclusions are supported by multiple configurations of the experiments. They combine multiple approaches to study a complex problem.

Weaknesses:

It would be valuable to understand if the nanobody is disrupting the formation of the ESAT6-CFP10 complex. It is unclear how the nanobody is functioning to enhance control in the infection context. More detail or speculation in the discussion would have been valuable. Where is the nanobody in the cell during infection?

Reviewer #2 (Public Review):

Summary:

Bates TA. et al. studied the biochemical characteristics of ESAT-6, a major virulence factor of Mycobacterium tuberculosis (Mtb), as part of the heterodimer with CFP10, a molecular chaperon of ESAT-6, as in homodimer and in homotetramer using recombinant ESAT-6 and CFP10 expressed in E. coli by applying several biochemical assays including Biolayer Interferometry (BLI) assay. The main findings show that ESAT-6 forms a tight interaction with CFP10 as a heterodimer at neutral pH, and ESAT-6 forms homodimer and even tetramer based larger molecular aggregates at acidic pH. Although the discussion of the potential problems associated with the contamination of ESAT-6 preparations with ASB-14 during the LPS removal step is interesting, but this research does not test the potential impact of residual ASB-14 contaminant on the biochemical behavior ESAT-6-CFP10 heterodimer and ESAT-6 homodimer or tetramer and their hemolytic activity in comparison with the ones without ASB-14. The main strength of this study is the generation of ESAT-6 specific nanobodies and demonstration of its anti-tuberculosis efficiency in THP-1 cell line infected with Mtb strains with reporter genes.

Strengths:

Generation and demonstration of the anti-ESAT-6 nanobodies against tuberculosis infection in cell line based Mtb infection model. Probably identifying potential anti-ESAT-6 nanobody interacting amino acid residues of ESAT-6 is critical in understanding their effects on ESAT-6 mediated membrane lytic activity.

Weaknesses:

Although the biochemistry studies provide quantitative data about the interactions of ESAT-6 with its molecular chaperon CFP10 and the interaction of ESAT-6 homodimer and tetramers, the novel information from these studies are minimal.

Reviewer #3 (Public Review):

Summary:

This manuscript describes some biochemical experiments on the crucial virulence factor EsxA (ESAT-6) of Mycobacterium tuberculosis. EsxA is secreted via the ESX-1 secretion system. Although this system is recognized to be crucial for virulence the actual mechanisms employed by the ESX-1 substrates are still mostly unknown. The EsxA substrate is attracting most attention as the central player in virulence, especially phagosomal membrane disruption. EsxA is secreted as a dimer together with EsxB. The authors show that EsxA is also able to form homodimers and even tetramers, albeit at very low pH (below 5). Furthermore addition of a nanobody that specifically binds EsxA is blocking intracellular survival, also if the nanobody is produced in the cytosol of the infected macrophages.

Strengths:

Decent biochemical characterization of EsxA and identification of a new and interesting tool to study the function of EsxA (nanobody). Well written.

Weaknesses:

The findings are not critically evaluated using extra experiments or controls.<br /> For instance, tetrameric EsxA in itself is interesting and could reveal how EsxA works. But one would say that this is a starting point to make small point mutations that specifically affect tetramer formation and then evaluate what the effect is on phagosomal membrane lysis. Also one would like to see experiments to indicate whether these structures can be produced under in vitro conditions, especially because it seems that this mainly happens when the pH is lower than 5, which is not normally happening in phagosomes that are loaded with M. tuberculosis.<br /> Also the fact that the addition of the nanobody, either directly to the bacteria or produced in the cytosol of macrophages is interesting, but again the starting point for further experimentation. As a control one would like to se the effect on an Esx-1 secretion mutant. Furthermore, does cytososlic production or direct addition of the nanobody affect phagosomal escape? What happens if an EsxA mutant is produced that does not bind the nanobody?<br /> Finally, it is a bit strange that the authors use a non-native version of esxA that has not only an additional His-tag but also an additional 12 amino acids, which makes the protein in total almost 20% bigger. Of course these additions do not have to alter the characteristics, but they might. On the other hand they easily discard the natural acetylation of EsxA by mycobacteria itself (proven for M. marinum) as not relevant for the function because it might not happen in (the close homologue) M. tuberculosis.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Will the nanobody be available to the TB research community?

Yes, we will make E11rv available upon request. Please see our materials availability statement.

Reviewer #2 (Recommendations For The Authors):

(1) It would be interesting to test the potential impact of residual ASB-14 contaminant on the biochemical behavior of ESAT-6-CFP10 heterodimer and ESAT-6 homodimer or tetramer and their hemolytic activity in comparison with the ones without ASB-14.

We agree that this is an interesting line of questioning. Based on the study by Refai et al. that we cite in the text, ESAT-6 treated with nonionic detergents ASB-14 or LDAO, but not other common detergents, undergoes a conformational change that increases its cytotoxicity in cell assays, hemolytic activity, and ability to dimerize with CFP-10. What is not known at this point, is how similar the ASB-bound conformation is to anything seen physiologically.

(2) Building on the progress in making anti-ESAT-6 nanobodies and their anti-Mtb effects in the cells, it could have been tested in human or mouse primary macrophages infected with Mtb and a mouse model of Mtb infection for its anti-Mtb efficiency.

We thank the reviewer for this suggestion, and we agree that these would be very informative next steps for determining the therapeutic potential of anti-ESAT-6 nanobodies.

Reviewer #3 (Recommendations For The Authors):

Minor comments:

Line 133: "It is well established that Mm-induced hemolysis is ESX-1 dependent, but our results suggest that Mtb must lack one or more factors necessary for efficient hemolysis.". I would tone this down a bit, as it is also known that M. tuberculosis escapes much later than M. marinum from the phagosome, which could indicate different kinetics.

We thank the reviewer for their insightful comments. We agree that the kinetics of Mtb and Mm infection are quite different and that this may impact the hemolysis assay. As described by Augenstreich et al. some hemolysis by Mtb is observed at 48 hours, though the method of normalization makes it impossible to determine absolute amount of hemolysis that occurred in their experiment. Our findings just show that the absolute amount of Mtb hemolysis in 2 hours is negligible, setting it apart from Mm. We have edited the wording of this statement in the manuscript to avoid any confusion.

Line 155: "Because Mtb often exists in an acidified compartment". First of all, the reference used here does not discuss anything about Mtb, secondly, papers that do measure the acidification of Mtb-loaded phagosomes indicate that this acidification is very mild (typically to pH 6.2).

We agree that this point should be articulated more precisely. We have added additional clarification that the pH of Mtb-containing compartments in macrophages can fall in a broad range depending on the activation state of the macrophages, and that non-activated macrophages are typically only mildly acidic. We have updated our references to better describe the current state of knowledge on this topic.

Line 339: "Whereas most of these functions rely only on the secretion of ESAT-6 into the cytoplasm, the ability of E11rv to access Mtb suggests that this communication is likely two-way." No, not necessary, there are many processes in which ESX-1 substrates affect the macrophage. This nanobody could affect EsxA functioning only once the bacteria reach the cytoplasm. I think checking phagosomal escape in these cells is therefore crucial.

We agree that phagosomal escape and subsequent direct secretion of ESAT-6 into the cytoplasm is a reasonable alternative hypothesis. We have added this point to our discussion, and we agree that looking directly at phagosomal escape is an important next step.

Figure 7 is not mentioned in the text (mistake for Fig 6).

This has been corrected.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The study is highly interesting and the applied methods are target-oriented. The biophysical characterization of viable N-protein species and several representative N-protein mutants is supported by the data, including polarity, hydrophobicity, thermodynamic stability, CD spectra, particle size, and especially protein self-association. The physicochemical parameters for viable N-protein and related coronavirus are described for comparison in detail. However, the conclusion becomes less convincing that the interaction of peptides or motifs was judged by different biophysical results, with no more direct data about peptide interaction. Additionally, the manuscript could benefit from more results involving peptide interaction to support the author's opinions or make expression more accurate when concerning the interaction of motifs. Although the authors put a lot of effort into the study, there are still some questions to answer.

We thank the Reviewer for this assessment and wholeheartedly agree that there are still many questions. The main thrust of the present work was not intended to unravel the detailed mechanistic origin of all observations, but rather to juxtapose the different observations made with different viable N-protein species across the mutant spectrum, in order to get a sense of how narrowly the biophysical phenotype is confined to ensure virus viability. Such a study has become possible for the first time with the unprecedented genomic database of SARS-CoV-2. This has led to observations of non-local effects of individual mutations that are not independent and non-additive relative to the effects of other mutations, and in that sense we have inferred ‘interactions’. These might be mediated by direct contacts or indirectly through altered chain configurations. In the revised manuscript we have clarified this point.

Meanwhile, a number of documented direct physical intra-molecular and intra-dimer interactions provide a context to our study of mutation effects. The flexibility of the IDRs provides a rich variety of contacts that have been observed in molecular dynamics and single-molecule fluorescence studies (Rozycki & Boura, Biophys Chem. 2022 and Cubuk et al, Nat Communs 2021). We have previously carried out detailed hydrodynamic studies of self-association interfaces located in the leucine-rich region. More recently, NMR data just published by the Blackledge laboratory (Botova et al., bioRxiv 2024) extend the list of intra-molecular contacts with the observation of long-range intra-molecular interactions between the NTD and the CTD, NTD and the phosphorylated SR-rich region, and NTD and the previously studied leucine-rich region. The latter contacts require the C-terminal region of the linker to loop back onto the NTD, which may well introduce susceptibility to any of the linker mutations. However, detailed linker configurations are beyond the scope of the present work.

With regard to the effects of the Omicron mutations in the N-arm IDR, we have shown hydrodynamic data directly demonstrating peptide self-association, and we are currently working on a more detailed functional follow-up study which we hope to communicate soon.

Reviewer #2 (Public Review):

Summary: This work focuses on the biochemical features of the SARS-CoV-2 Nucleocapsid (N)protein, which condenses the large viral RNA genome inside the virus and also plays other roles in the infected cell. The N protein of SARS-CoV-2 and other coronaviruses is known to contain two globular RNA-binding domains, the NTD and CTD, flanked by disordered regions. The central disordered linker is particularly well understood: it contains a long SR-rich region that is extensively phosphorylated in infected cells, followed by a leucine-rich helical segment that was shown previously by these authors to promote N protein oligomerization.

In the current work, the authors analyze 5 million viral sequence variants to assess the conservation of specific amino acids and general sequence features in the major regions of the N protein. This analysis shows that disordered regions are particularly variable but that the general hydrophobic and charge character of these regions are conserved, particularly in the SR and leucine-rich regions of the central linker. The authors then construct a series of N proteins bearing the most prevalent mutations seen in the Delta and Omicron variants, and they subject these mutant proteins to a comprehensive array of biophysical analyses (temperature sensitivity, circular dichroism, oligomerization, RNA binding, and phase separation).

Strengths:

The results include a number of novel findings that are worthy of further exploration. Most notable are the analyses of the previously unstudied P31L mutation of the Omicron variant. The authors use ColabFold and sedimentation analysis to suggest that this mutation promotes the self-association of the disordered N-terminal region and stimulates the formation of N protein condensates. Although the affinity of this interaction is low, it seems likely that this mutation enhances viral fitness by promoting N-terminal interactions. The work also addresses the impact of another unstudied mutation, D63G, that is located on the surface of the globular NTD and has no significant effect on the properties analyzed here, raising interesting questions about how this mutation enhances viral fitness. Finally, the paper ends with studies showing that another common mutant, R203K/G204R,disrupts phase separation and might thereby alter N protein function in a way that enhances viral fitness.

Thank you for highlighting the strengths of our paper.

Weaknesses:

In general, the results in the paper confirm previous ideas about the role of N protein regions. The key novelty of the paper lies in the identification of point mutations, notablyP13L, that suggest previously unsuspected functions of the N-terminal disordered region in protein oligomerization. The paper would benefit from further exploration of these possibilities.

We agree that the bioinformatic results confirm previous ideas about the role of the N protein regions. However, we believe our results go beyond the previous thinking in a crucial aspect, which is that we examine the full (so far known) mutant spectrum of N-protein. Properties previously inferred from the inspection of single consensus sequences can be misleading because of the quasispecies nature of RNA viruses. By considering the mutant spectrum we can obtain a sense for how significant differences in the physicochemical properties of the different regions are, and how much variation is possible without jeopardizing essential protein functions.

With regard to the N-arm IDR mutations we believe this deserves a separate study focusing on the apparent N-arm function. Our rationale for presenting some initial N-arm results in the current paper was to highlight how the variability of N-protein species in the mutant spectrum can even include differences in the type and number of protein self-association interfaces.

Reviewer #3 (Public Review):

Nguyen, Zhao, et al. used bioinformatic analysis of mutational variants of SARS-CoV-2Nucleocapsid (N) protein from the large genomic database of SARS-CoV-2 sequences to identify domains and regions of N where mutations are more highly represented and computationally determined the effects of these mutations on the physicochemical properties of the protein. They found that the intrinsically disordered regions (IDRs) of N protein are more highly mutated than structured regions and that these mutations can lead to higher variability in the physical properties of these domains. These computational predictions are compared to in vitro biophysical experiments to assess the effects of identified mutations on the thermodynamic stability, oligomeric state, particle formation, and liquid-liquid phase separation of a few exemplary mutants.

The paper is well-written and easy to follow, and the conclusions drawn are supported by the evidence presented. The analyses and conclusions are interesting and will be of value to virologists, cell biologists, and biophysicists studying SARS-CoV-2 function and assembly. It would be nice if some further extrapolation or comments could be made regarding the effects of the observed mutations on the in vivo behavior and properties of the virus, but I appreciate that this is much higher-order than could be addressed with the approaches employed here.

We thank the Reviewer for this positive assessment. With regard to the possible in vivo behavior of mutant species, we agree that this would require additional data beyond the scope of the present work.

However, for the N:G215C mutant we can point to a very recent preprint by Kubinski et al. (bioRxiv 2024) that describes reverse genetics experiments where the isolated N:G215C mutation caused altered in vivo pathology, enhanced viral replication, and altered virion morphology. We have cited this work in the revised manuscript.

As mentioned above, for the P13L mutation we hope to communicate a more detailed follow-up study that will allow us to extrapolate on its in vivo behavior.

Recommendations For The Authors:

Reviewer #1:

(1) Given the structure organization of N-protein in Figure 1, the authors should explain why linker region 180-247 is different from linker (175-247) mentioned in the first result.

We thank the reviewer for bringing up this point, which we agree deserves clarification. While often the NTD has been assigned a C-terminal limit of 180 (e.g., in the NMR structure by Dinesh et al, Plos Pathogens 2020), the last several residues in the NTD are already disordered and contain the S176/R177 pair and therefore may be ascribed to the beginning of the SR-rich portion of the linker. In order not to artificially truncate functional sequences of either NTD or linker, we have decided to allow the designations of the NTD and linker regions to overlap. We believe this is conservative in that possible NTD or linker properties extending into this transition region will be preserved. In order to explain this in the manuscript, we have modified Figure 1 and inserted a brief sentence “(Due to ambiguity in delineation between NTD and linker, designations overlapping in 175-180 were used to avoid artificial truncation and permit conservative evaluation of the properties of each domain.)”.

(2) Please specify the "physicochemical requirements" in the fourth paragraph of the first result, and its physicochemical meaning and references.

Thank you for pointing this out; we agree this was not well expressed. We have rephrased this (including new references) to “…we find that hydrophobicity is uniformly high and polarity correspondingly low in the folded NTD and CTD domains, which is consistent with the expectation that folded structures are stabilized by buried hydrophobic residues (Eisenberg and McLachlan, 1986; Kauzmann, 1959)”.

(3) The authors should clarify the biological meaning of the net charge and phosphorylation charge in the first result, just like the description in the results of polarity and hydrophobicity.

We agree this will improve readability, and have inserted an introductory sentence to the study of charges in the mutant spectrum: “Charges in proteins can control multiple properties related to electrostatic interactions, from functions of active sites to protein solubility, protein interactions, and conformational ensembles in IDRs (Garcia-Viloca et al., 2004; Gerstein and Chothia, 1996; Gitlin et al., 2006; Mao et al., 2010).”.

(4) The authors should clarify the calculation method and meaning of the column "occurs in % of all genomes" in Table 2.

We have inserted a footnote specifying that this is the “Percentage of all sequenced genomes carrying the specific mutation.”.

(5) Please specify what information or conclusion we can get for the shift of the intrinsic fluorescent spectrum of N: D63G in the third result paragraph 2.

We have rephrased the second sentence of this paragraph to “The presence of the N:D63G mutation in the NTD is highlighted in the shift of the intrinsic fluorescence quantum yield of this mutant in comparison to Nref ”. It confirms the structural prediction, which positions D63G at the protein surface near the NA binding site, and sets up the question whether this obligatory mutation of Delta-variant N-protein affects NA binding and thereby possibly assembly. Unexpectedly, we did not find any impact of the D63G mutation on NA binding, although we observed a modest impact on temperature-dependent particle formation by DLS.

(6) The conclusion, "some epistatic interaction between mutation of the linker and N-arm" in the third result paragraph 4, is over-interpreted from the result of the CD spectra because they didn't detect peptide interaction between mutation of the linker and N-arm.

Thank you for raising this point. We did not mean to make a strong conclusion here, and have now deleted this statement.

(7) The parallel assay for N: G215C and Nδ in SV-AUC experiments is recommended to be conducted with other groups to avoid experimental error.

I believe this may be a misunderstanding: Indeed we had carried out SV-AUC experiments for all the mutants, as shown in Figure 5A. However, since all but the N:G215C and Nδ formed only dimers as the reference protein, we did not comment on these in the results text. We have rectified this omission in the revision by inserting the sentence: “…The same behavior is observed for N:D63G, No, N:R203K/G204R, as well as N:P13L/Δ31-33 at low micromolar concentrations (Figure 5A). By contrast, the G215C mutation promotes the formation of higher oligomers…”

With regard to experimental error, SV-AUC is an absolute method based on first principles and we have maintained our instruments by performing regular calibrations, using methods developed by us and colleagues at NIST, as described in the literature (Anal Biochem 2013, PLOS ONE 2018, Eur. Biophys. J. 2021). Previously we have critically examined the accuracy of s-values by SV-AUC before and after calibration in a large multi-laboratory study (PLOS ONE 2015), and found that the accuracy of s-values is ~1%. This allows detailed comparisons of results from different runs and different points in time. To alleviate any concerns we have now mentioned our calibration methods in the methods section.

(8) The authors did not test the function of Nδ R203M mutation, so they should not mention about it like in the third result paragraph 5, which is over-interpreted from result 5A.

We accept the criticism that we have not yet examined the R203M mutation in isolation. However, we believe some speculation is in order: Nδ consists of D63G, R203M, G215C, and D377Y, of which D63G is unlikely to impact oligomeric state based on our data of N:D63G. It is therefore reasonable to assume that R203M and/or D377Y interfere with the observed promotion of oligomerization that we have observed with N:G215C. In previous work, we have traced the 215C-incuded oligomerization to the transient helix in the leucine-rich region of the linker 215-235 (Science Advances, 2023), Since 377Y is quite far away, the more proximal 203M appears to be the most plausible origin of the modulation of dimerization.

In the revision we have more clearly outlined this speculation: “ Of the three additional mutations of Nδ relative to N:G215C, we speculate that D63G does not impact dimerization (as in N:D63G, Figure 5A), and that therefore either the distant D377Y and/or R203M might cause this reduction of helicity and oligomerization relative to N:G215C, noting that R203M is proximal to the L-rich region (215-235) reshaped by 215C. ”. Later we refer to this as “any potential inhibitory role suspected of the R203M mutation on self-association…”.

(9) The description of LLPS formation lacks reference in the third result paragraph 6.

Thank you. To improve the transition to this new paragraph in the results, we have inserted “As outlined in the introduction, …” and repeated the 8 references to the fact that N-protein undergoes LLPS. The two additional, separate references refer to just those published studies that examined the temperature-dependence of LLPS, which I believe is now clearer.

(10) The authors did not test the interaction between the N-arm IDR mutation and linker IDR, it is not exponible that interaction promoted particle formation of No in the third result paragraph 8, which is over-interpreted from result 5B.

We thank the Reviewer for raising this point. In fact, we did not want to imply a direct physical interaction (in terms of binding) between the N-arm IDR mutation and that in the linker. But clearly there are non-additive effects in particle formation since P13L/Δ31-33 inhibits slightly and R203K/G204R inhibits almost completely, whereas the combination of the two (constituting No) promotes particle formation. We have rephrased this to “alter the effect of”, avoiding the term “interact with” not to suggest a picture of direct binding and invoke instead the idea of epistatic interactions.

(11) In the third result paragraph 9, why did the authors choose to examine the role of the N-arm mutations of the Omicron variants in greater detail? This reason should be added to the manuscript.

Thank you for this suggestion. Naturally, we were curious how the defining N-arm mutations of Omicron variants could impact particle formation. Even though no obvious enhancement of self-association by either Omicron N-arm or linker mutations was observed at low micromolar concentrations in SV-AUC (Figure 5A), we knew from experience with the study of the leucine-rich transient helix in the linker IDR that even weak interfaces with mM Kd can be highly relevant in the context of multivalent assemblies (Science Advances, 2023). Therefore we followed the same roadmap and focused on IDR peptides with the goal to study them at higher concentrations that might reveal weak interactions.

We have described this motivation as follows: “We were curious whether IDR mutations might alter particle formation through modulation of existing or introduction of new protein-protein interfaces. We focused on Omicron mutations as these are obligatory an all currently circulating strains, and specifically on N-arm mutations, which have recently been implicated in altered intramolecular interactions with NA-occupied NTD (Cubuk et al., 2023). Even though SV-AUC showed no indication of self-association of N:P13L/Δ31-33 at low micromolar concentrations, weak interactions with Kd > mM would not be detectable under these conditions yet could be highly relevant in the context of multi-valent complexes (Zhao et al., 2024). Following the roadmap used previously for the study of the weak self-association of the leucine-rich linker IDR (Zhao et al., 2023), we restricted the protein to the N-arm peptide such that it can be studied at much higher concentrations. To this end, we …”

(12) Why were different proteins dissolved in either high-salt buffer or low-salt buffer for biophysical experiments? Did this affect the experimental results? Explanations and evidence are required.

We appreciate this is an important point. Unfortunately, for practical reasons of available sample concentrations and quantities, it was not always possible to dialyze protein into both buffers. For example, the DSF data in Figure 4B show all proteins in low-salt buffer except N:R203K/G204R, which is in high-salt buffer. We had previously reported the absence of changes in Ti in DSF for Nref in the two buffers, which we have documented better in the revised manuscript by providing an additional Supplementary Figure S7: “As a buffer control, the difference in Ti for Nref in LS and HS buffer was measured and found to be within error of data acquisition (Supplementary Figure S7A).” This new Supplementary Figure provides an overlay of low-salt and high-salt DSF data for Nref, N:D63G, and No, which have variations in the Ti values for different buffers on the order of 0.1 °C. This is comparable to the precision of the measurement, and significantly smaller than the changes in Ti values between the different mutant protein species. Finally, we note that the one species for which we were unable to collect DSF data in low-salt buffer, N:R203K/G204R, was unremarkable relative to Nref, No, and N:P13L/Δ31-33.

In the case of CD, the only species for which we could not collect spectra in low-salt buffer was No. Again, this spectrum was similar to the group including Nref, along with N:P13L/Δ31-33, and N:D63G. In the results we interpreted significant differences from Nref for N:G215C and N:R203K/G204R.

Similarly, SV-AUC experiments were carried out in high-salt buffer, except Nref, Nδ , and N:G215C. In this case, we could observe a ≈ 5% difference in s-value for the same protein in different buffers, but the magnitude of this change is negligible compared to the ≈ 60-90% increase observed for altered oligomeric states. To clarify this we have inserted a sentence “Proteins for self-association studies were in buffer HS, except Nref, Nδ , and N:G215C were in LS, the latter causing a ≈5% increase in s-value (Supplementary Figure S7B).”, with the new Supplementary Figure S7B showing a comparison of sedimentation coefficient distributions of Nref and N:D63G in low- and high-salt buffers. Whether the small differences in s-values are indeed significant and reflective of salt-dependent conformational ensembles of IDRs will require a more detailed follow-up study, but is outside the scope of the present work.

All other experiments were carried out with uniform buffer conditions for all protein species.

(13) DLS data of N from other research suggests oligomers beyond dimer. Please address this discrepancy.

Unfortunately several previous studies in the literature did not recognize the importance of eliminating nucleic acid contaminations in the N-protein preparations, and/or did not succeed in completely removing nucleic acid from the protein. We and others have repeatedly commented on this issue. For example, Tarczewska et al (IJBM 188 (2021) 391-403) clearly demonstrate this in much detail in a study dedicated to this problem.

The clarify this point we have included a sentence in the paragraph describing the protein preparation “…the ratio of absorbance at 260 nm and 280 nm of ~0.50-0.55 confirmed absence of nucleic acid. The latter is important to eliminate higher order N-protein oligomers induced by nucleic acid binding (Carlson et al., 2020; Tarczewska et al., 2021; Zhao et al., 2021)” .

In order to strengthen the statement in the Results that the ancestral N-protein is dimeric we have added additional references from other labs that have carried out detailed biophysical analyses: “As reported previously, the ancestral N-protein at micromolar concentrations in NA-free form is a tightly linked dimer sedimenting at ≈4 S , without significant populations of higher oligomers (Forsythe et al., 2021; Ribeiro-Filho et al., 2022; Tarczewska et al., 2021; Zhao et al., 2022, 2021).”

Reviewer #2:

The key novel finding of the work lies in the evidence that P31L promotes N-terminal interactions. The paper would be strengthened by additional studies of the impact of P31Lon the oligomerization of full-length N protein. The sedimentation analysis in Fig 6 shows that high concentrations of the N arm alone self-associate, while the analysis in Fig 5 argues that P31L does not have an effect on the oligomerization of the full-length protein. Perhaps there are specific conditions or mutation combinations that would provide evidence that P31L has an effect on protein behavior that might explain the prevalence of this mutation.

We agree that the finding of P13L promoting N-terminal interactions is of great interest, and we thank the Reviewer for the suggestion to examine cross-correlations of N-arm mutations with other mutations as a tool to study its function and relevance.

The observation of self-association in Figure 6 at high concentrations is not necessarily at odds with the absence of self-association at 100fold lower concentrations. Rather, it seems to show that the interaction mediated by the N-terminal mutation P13L is weak with an effective Kd in the mM range. It will likely not be possible to reach sufficiently high protein concentrations with the full-length protein to visualize the oligomerization of N-terminal IDR. But even if it was possible to concentrate the protein enough, very likely other assembly processes would take place, including LLPS, obscuring potential P13L interfaces. Nonetheless we believe the protein-protein interface created by the N-arm IDR is highly relevant in the context of multi-valent complexes, where entropic co-localization enhances the effective N-arm IDR concentration that then can provide additional binding energy and strengthen the assembly of multi-protein complexes.

We are currently pursuing further experiments examining the properties and relevance of the N-arm mutations and intend to publish this in a separate study, not to distract from the thrust of the current work exploring of the extent of the biophysical phenotype space.

The R203K/G204R mutations have a surprising impact on LLPS in Figure 7: it is not clear how such limited mutations would alter the many nonspecific, multivalent interactions that presumably lead to phase separation. The paper would benefit from a more extensive analysis of LLPS in this mutant and in the P31L mutant, perhaps by performing the analysis at various protein concentrations and times.

Following this recommendation we have expanded the study of LLPS of Figure 7 by comparison of two different time points for Nref, N:R203K/G204R, and N:P13L in a new Supplementary Figure S6. We have also quantified the droplet distributions as shown in the new Supplementary Figure S5. Both clearly confirm the strong inhibitory effect of the R203K/G204R mutation on LLPS under our experimental conditions. What this shows is not that this protein could not undergo LLPS per se, but that the phase boundaries have shifted such that under the experimental conditions we applied LLPS does not occur yet. (In this context it is interesting to note that ≈50,000 genomes in the GISAID database have R203K/G204R as the sole N-protein mutation, without impact on viral viability.)

That individual point-mutations in IDRs can have significant impact on LLPS has been observed previously for several other proteins. Examples include SPOP [Bouchard et al., Mol Cell 72 (2018) 19-36.e8], SHP2 [Zhu et al., Cell 183 (2020) 490-502.e18], FUS [Niaki et al., Mol Cell 77 (2020) 82-94.e4], and CAPRIN1 [Kim et al., PNAS 118 (2021) 1-11]. The latter work applies NMR and reveals that promotion of LLPS is not uniform but centered in hot-spot residues of CAPRIN1.

While the precise molecular mechanism for LLPS of the N-protein is unclear, we can speculate how the effect of 203K/204R might be amplified. As shown by the coarse-grained MD simulations from Rozycki & Boura (Biophys. Chem. 2022), the linker IDR is highly flexible and the 203/204 residues make transient contacts to other residues throughout the linker as well as to distinct sites on the NTD. Furthermore, recent NMR data from the Blackledge lab (Botova et al., bioRxiv 2024, doi:10.1101/2024.02.22.579423) have revealed intra-molecular interactions, including a state where the L-rich (C-terminal) portion of the linker IDR interacts with a site on the distant NTD. (We have included a reference to this preprint in the discussion.) This intra-molecular contact observed in NMR must cause significant chain compaction and may thereby modulate the accessibility of portions of the linker IDR available to inter-molecular interactions contributing to LLPS. The residues 203/204 are in the middle between the SR-rich and L-rich region where bending of the chain must occur to allow for the intra-molecular contacts. The 203K/204R mutation may alter the dynamics or population of this intra-molecular bound state, especially considering the introduction of a bulky positively charged R replacing G204.

In summary, considering the dynamics of intra-molecular contacts and considering precedent of several other disordered proteins, we believe it is not unreasonable that the local mutation in the IDR R203K/G204R may cause a significant shift in LLPS phase boundaries. We note that this mutant also shows a very distinct behavior in the temperature-dependent DLS, entirely lacking particle formation below 70 °C. This observation seems consistent with altered inter-molecular interactions.

Reviewer #3:

I have only a few minor specific comments:

(1) Page 4, last paragraph - typo: "The large number of structural and non-structural N-protein functions poses the question of how they are conserved...". This either needs a colon or to be changed to "... poses the question of how they are conserved...".

Thank you – we have changed this sentence accordingly.

(2) Page 7, 2nd and 3rd paragraphs of "Physicochemical properties" section: why is Figure2B discussed before Figure 2A?

Initially when we present the results of polarity and hydrophobicity we refer more generally to Figure 2, as the two properties are so closely related. Later, in the section on related coronaviruses we do refer once more to Figure 2. Here we begin this section by discussing Figure 2B since in this plot the symbols for the different viruses are most recognizable.

(3) Page 11, lines 1-2: "Since this is a tell-tale of weak protein..." -> "tell-tale sign of ...".

We thank the reviewer for pointing this out and have fixed this sentence.

(4) Further down in the same paragraph, the meaning of "SV-AUC" should be spelled out at its first use.

We have double checked that SV-AUC is spelled out at its first use.

(5) Figures 1 and 2. Is there a good reason that the color scheme for the IDRs (magenta and cyan) is so close to the color scheme for the identifying mutations of Omicron and Delta (magenta and blue)? This initially led me to try to search for some connection, and it remains unclear to me if there is.

We apologize for this confusion. This was indeed a poor color choice, and we have rectified this in the revised manuscript by changing the colors of the identifying mutations of Omicron and Delta to dashed green and dotted red, respectively, so that there is no connection to the shading of the IDRs. Thank you very much for pointing this out!

(6) Figure 1: The physical limits of the subdomains, e.g. SR-rich, L-rich, C-arm1, and N3 could be more clearly delineated with lines, or some other visual representation.

Once more, we thank the reviewer for pointing this out. We have revised Figure 1 to indicate the limits between these subdomains.

(7) Figures 4, 5, and 6: are there any kind of error bars or confidence intervals on these measurements?

We appreciate this concern and have addressed it in different ways for the different methods.

For the spectra of intrinsic fluorescence in Figure 4A, we have now plotted an overlay of three acquired spectra, from which the experimental error as a function of wavelength may be assessed. It is clear that the differences between Nref and N:D63G are far greater than the measurement error.

With regard to DSF, we have provide an error estimate of 0.3 °C for the Ti-values, a value that we have revised from the previously reported errors of sequential replicates to now include Ti variation observed with different preparations of the same protein over long time periods.

For CD spectra we have included a new Supplementary Figure S3 that shows standard deviations of triplicate measurements as a function of wavelength. Since an overlay including errors for all species would be too crowded, we have created separate plots for all species in comparison with Nref. (On this occasion we discovered a 3% error in the magnitude of the Nref spectrum due to previously incorrect conversion to MRE, which we have now fixed.)

In SV-AUC, for data with typical signal-noise ratio, the statistical error is very small due to the large number (> 104 ) of raw data points included in the calculation of each c(s) trace, which each data point carrying a statistical error that is usually better than 1%. Therefore, the dominant error is systematic. In the past we have carried out large studies quantifying the accuracy of the major peaks of the sedimentation coefficient distributions, and found they are typically ≈1% in s-value and 1-2% for relative peak areas. In the AUC methods section we have now included the sentence “Typical accuracy of c(s) peaks are on the order of ≈1% for peak s-values and ≈1-2% for relative peak areas (Zhao et al., 2015).”

Finally, for the temperature-dependent DLS data we have to resort to the scatter in the temperature-dependent Rh-values. The calculated Rh-values can exhibit fluctuations once particles start to form and the distribution becomes highly polydisperse. As is characteristic for DLS under those conditions, individual Rh-values can be dominated by adventitious diffusion of few large particles into the laser focal spot. Although customarily autocorrelation functions can be filtered out through software filters (e.g., setting baseline and amplitude thresholds), this still presents the largest source of error in the Rh-values. These are systematic for the individual autocorrelation functions. We believe that the variation of Rh-values at similar temperatures outside the transition region provides a reasonable estimate for the experimental error.

(8) Figure 7: My most major comment. It would be good to somehow quantify the differences between these images. The claim is made that the LLPS droplets are different sizes, or for the P13L/\Delta31-33 variant that droplets are coalescing or changing shape over time. It would be good to quantify this rather than rely on eyeballing the pictures.

We are grateful to the Reviewer for this suggestion. As mentioned above, to improve the LLPS analysis we have now carried out segmentation of the images in Figure 7 to quantify the droplet numbers and areas. Histograms and statistical analyses are now provided in the new Supplementary Figure S5. In addition, we have added a comparison of the droplet numbers and sizes at two time-points for Nref, N:R203K/G204R, in addition to the previously shown N:P13L/Δ31-33, provided in the new Supplementary Figure S6. The results corroborate the previous conclusions, and depict how droplets in the N:P13L/Δ31-33 merge and grow in area more strongly than those from Nref.

eLife assessment

This important manuscript provides new insights into the biophysics of the SARS-CoV-2 nucleocapsid. The evidence, which relies on a convincing combination of genetic and biophysical data, nicely supports the conclusions.

Reviewer #2 (Public Review):

This work focuses on the biochemical features of the SARS-CoV-2 Nucleocapsid (N) protein, which condenses the large viral RNA genome inside the virus and also plays other roles in the infected cell. The N protein of SARS-CoV-2 and other coronaviruses is known to contain two globular RNA-binding domains, the NTD and CTD, flanked by disordered regions. The central disordered linker is particularly well understood: it contains a long SR-rich region that is extensively phosphorylated in infected cells, followed by a leucine-rich helical segment that was shown previously by these authors to promote N protein oligomerization.

In the current work, the authors analyze 5 million viral sequence variants to assess the conservation of specific amino acids and general sequence features in the major regions of the N protein. This analysis shows that disordered regions are particularly variable but that the general hydrophobic and charge character of these regions are conserved, particularly in the SR and leucine-rich regions of the central linker. The authors then construct a series of N proteins bearing the most prevalent mutations seen in the Delta and Omicron variants, and they subject these mutant proteins to a comprehensive array of biophysical analyses (temperature sensitivity, circular dichroism, oligomerization, RNA binding, and phase separation).

The results include a number of novel findings that are worthy of further exploration. Most notable are the analyses of the previously unstudied P31L mutation of the Omicron variant. The authors use ColabFold and sedimentation analysis to suggest that this mutation promotes self-association of the disordered N-terminal region and stimulates the formation of N protein condensates. Although the affinity of this interaction is low, it seems likely that this mutation enhances viral fitness by promoting N-terminal interactions. The work also addresses the impact of another unstudied mutation, D63G, that is located on the surface of the globular NTD and has no significant effect on the properties analyzed here, raising interesting questions about how this mutation enhances viral fitness. Finally, the paper ends with studies showing that another common mutant, R203K/G204R, disrupts phase separation and might thereby alter N protein function in a way that enhances viral fitness. These provocative results set the stage for in-depth analyses of these mutations in future work.

Reviewer #3 (Public Review):

Nguyen, Zhao et al. used bioinformatic analysis of mutational variants of SARS-CoV-2 Nucleocapsid (N) protein from the large genomic database of SARS-CoV-2 sequences to identify domains and regions of N where mutations are more highly represented, and computationally determined the effects of these mutations on the physicochemical properties of the protein. They found that the intrinsically disordered regions (IDRs) of N protein are more highly mutated than structured regions, and that these mutations can lead to higher variability in the physical properties of these domains. These computational predictions are compared to in vitro biophysical experiments to assess the effects of identified mutations on the thermodynamic stability, oligomeric state, particle formation, and liquid-liquid phase separation of a few exemplary mutants.

The paper is well written, easy to follow and the conclusions drawn are supported by the evidence presented. The analyses and conclusions are interesting and will be of value to virologists, cell biologists, and biophysicists studying SARS-CoV-2 function and assembly.

eLife assessment

This study represents a fundamental contribution to our understanding of how gene expression levels are controlled in bacteria. Through a series of compelling and careful experiments, relying on a mutant that blocks DNA replication but permits growth, and using various methods, the authors reveal how genome concentration rapidly becomes limiting for growth when replication is inhibited. This work contributes to our understanding of the contributions and limiting roles of DNA, mRNA, and ribosomes for growth in bacteria, and will be of considerable interest within both systems biology and microbial physiology.

Reviewer #1 (Public Review):

Summary:

The manuscript by Mäkelä et al. presents compelling experimental evidence that the amount of chromosomal DNA can become limiting for the total rate of mRNA transcription and consequently protein production in the model bacterium Escherichia coli. Specifically, the authors demonstrate that upon inhibition of DNA replication the single-cell growth rate continuously decreases, in direct proportion to the concentration of active ribosomes, as measured indirectly by single-particle tracking. The decrease of ribosomal activity with filamentation, in turn, is likely caused by a decrease of the concentration of mRNAs, as suggested by an observed plateau of the total number of active RNA polymerases. These observations are compatible with the hypothesis that DNA limits the total rate of transcription and thus translation. The authors also demonstrate that the decrease of RNAp activity is independent of two candidate stress response pathways, the SOS stress response and the stringent response, as well as an anti-sigma factor previously implicated in variations of RNAp activity upon variations of nutrient sources.

Remarkably, the reduction of growth rate is observed soon after the inhibition of DNA replication, suggesting that the amount of DNA in wild-type cells is tuned to provide just as much substrate for RNA polymerase as needed to saturate most ribosomes with mRNAs. While previous studies of bacterial growth have most often focused on ribosomes and metabolic proteins, this study provides important evidence that chromosomal DNA has a previously underestimated important and potentially rate-limiting role for growth.

Strengths:

This article links the growth of single cells to the amount of DNA, the number of active ribosomes and to the number of RNA polymerases, combining quantitative experiments with theory. The correlations observed during depletion of DNA, notably in M9gluCAA medium, are compelling and point towards a limiting role of DNA for transcription and subsequently for protein production soon after reduction of the amount of DNA in the cell. The article also contains a theoretical model of transcription-translation that contains a Michaelis-Menten type dependency of transcription on DNA availability and is fit to the data. While the model fits well with the continuous reduction of relative growth rate in rich medium (M9gluCAA), the behavior in minimal media without casamino acids is a bit less clear (see comments below).

At a technical level, single-cell growth experiments and single-particle tracking experiments are well described, suggesting that different diffusive states of molecules represent different states of RNAp/ribosome activities, which reflect the reduction of growth. However, I still have a few points about the interpretation of the data and the measured fractions of active ribosomes (see below).

Apart from correlations in DNA-deplete cells, the article also investigates the role of candidate stress response pathways for reduced transcription, demonstrating that neither the SOS nor the stringent response are responsible for the reduced rate of growth. Equally, the anti-sigma factor Rsd recently described for its role in controlling RNA polymerase activity in nutrient-poor growth media, seems also not involved according to mass-spec data. While other (unknown) pathways might still be involved in reducing the number of active RNA polymerases, the proposed hypothesis of the DNA substrate itself being limiting for the total rate of transcription is appealing.

Finally, the authors confirm the reduction of growth in the distant Caulobacter crescentus, which lacks overlapping rounds of replication and could thus have shown a different dependency on DNA concentration.

Weaknesses:

There are a range of points that should be clarified or addressed, either by additional experiments/analyses or by explanations or clear disclaimers.

First, the continuous reduction of growth rate upon arrest of DNA replication initiation observed in rich growth medium (M9gluCAA) is not equally observed in poor media. Instead, the relative growth rate is immediately/quickly reduced by about 10-20% and then maintained for long times, as if the arrest of replication initiation had an immediate effect but would then not lead to saturation of the DNA substrate. In particular, the long plateau of a constant relative growth rate in M9ala is difficult to reconcile with the model fit in Fig 4S2. Is it possible that DNA is not limiting in poor media (at least not for the cell sizes studied here) while replication arrest still elicits a reduction of growth rate in a different way? Might this have something to do with the naturally much higher oscillations of DNA concentration in minimal medium?

The authors argue that DNA becomes limiting in the range of physiological cell sizes, in particular for M9glCAA (Fig. 1BC). It would be helpful to know by how much (fold-change) the DNA concentration is reduced below wild-type (or multi-N) levels at t=0 in Fig 1B and how DNA concentration decays with time or cell area, to get a sense by how many-fold DNA is essentially 'overexpressed/overprovided' in wild-type cells.

Fig. 2: The distribution of diffusion coefficients of RpsB is fit to Gaussians on the log scale. Is this based on a model or on previous work or simply an empirical fit to the data? An exact analytical model for the distribution of diffusion constants can be found in the tool anaDDA by Vink, ..., Hohlbein Biophys J 2020. Alternatively, distributions of displacements are expressed analytically in other tools (e.g., in SpotOn).

The estimated fraction of active ribosomes in wild-type cells shows a very strong reduction with decreasing growth rate (down from 75% to 30%), twice as strong as measured in bulk experiments (Dai et al Nat Microbiology 2016; decrease from 90% to 60% for the same growth rate range) and probably incompatible with measurements of growth rate, ribosome concentrations, and almost constant translation elongation rate in this regime of growth rates. Might the different diffusive fractions of RpsB not represent active/inactive ribosomes? See also the problem of quantification above. The authors should explain and compare their results to previous work.

To measure the reduction of mRNA transcripts in the cell, the authors rely on the fluorescent dye SYTO RNAselect. They argue that 70% of the dye signal represents mRNA. The argument is based on the previously observed reduction of the total signal by 70% upon treatment with rifampicin, an RNA polymerase inhibitor (Bakshi et al 2014). The idea here is presumably that mRNA should undergo rapid degradation upon rif treatment while rRNA or tRNA are stable. However, work from Hamouche et al. RNA (2021) 27:946 demonstrates that rifampicin treatment also leads to a rapid degradation of rRNA. Furthermore, the timescale of fluorescent-signal decay in the paper by Bakshi et al. (half life about 10min) is not compatible with the previously reported rapid decay of mRNA (2-4min) but rather compatible with the slower, still somewhat rapid, decay of rRNA reported by Hamouche et al.. A bulk method to measure total mRNA as in the cited Balakrishnan et al. (Science 2022) would thus be a preferred method to quantify mRNA. Alternatively, the authors could also test whether the mass contribution of total RNA remains constant, which would suggest that rRNA decay does not contribute to signal loss. However, since rRNA dominates total RNA, this measurement requires high accuracy. The authors might thus tone down their conclusions on mRNA concentration changes while still highlighting the compelling data on RNAp diffusion.

The proteomics experiments are a great addition to the single-cell studies, and the correlations between distance from ori and protein abundance is compelling. However, I was missing a different test, the authors might have already done but not put in the manuscript: If DNA is indeed limiting the initiation of transcription, genes that are already highly transcribed in non-perturbed conditions might saturate fastest upon replication inhibition, while genes rarely transcribed should have no problem to accommodate additional RNA polymerases. One might thus want to test, whether the (unperturbed) transcription initiation rate is a predictor of changes in protein composition. This is just a suggestion the authors may also ignore, but since it is an easy analysis, I chose to mention it here.

Related to the proteomics, in l. 380 the authors write that the reduced expression close to the ori might reflect a gene-dosage compensatory mechanism. I don't understand this argument. Can the authors add a sentence to explain their hypothesis?

In Fig. 1E the authors show evidence that growth rate increases with cell length/area. While this is not a main point of the paper it might be cited by others in the future. There are two possible artifacts that could influence this experiment: a) segmentation: an overestimation of the physical length of the cell based on phase-contrast images (e.g., 200 nm would cause a 10% error in the relative rate of 2 um cells, but not of longer cells). b) time-dependent changes of growth rate, e.g., due to change from liquid to solid or other perturbations. To test for the latter, one could measure growth rate as a function of time, restricting the analysis to short or long cells, or measuring growth rate for short/long cells at selected time points. For the former, I recommend comparison of phase-contrast segmentation with FM4-64-stained cell boundaries.

Reviewer #2 (Public Review):

In this work, the authors uncovered the effects of DNA dilution on E. coli, including a decrease in growth rate and a significant change in proteome composition. The authors demonstrated that the decline in growth rate is due to the reduction of active ribosomes and active RNA polymerases because of the limited DNA copy numbers. They further showed that the change in the DNA-to-volume ratio leads to concentration changes in almost 60% of proteins, and these changes mainly stem from the change in the mRNA levels.

Reviewer #3 (Public Review):

Summary:

Mäkelä et al. here investigate genome concentration as a limiting factor on growth. Previous work has identified key roles for transcription (RNA polymerase) and translation (ribosomes) as limiting factors on growth, which enable an exponential increase in cell mass. While a potential limiting role of genome concentration under certain conditions has been explored theoretically, Mäkelä et al. here present direct evidence that when replication is inhibited, genome concentration emerges as a limiting factor.

Strengths:

A major strength of this paper is the diligent and compelling combination of experiment and modeling used to address this core question. The use of origin- and ftsZ-targeted CRISPRi is a very nice approach that enables dissection of the specific effects of limiting genome dosage in the context of a growing cytoplasm. While it might be expected that genome concentration eventually becomes a limiting factor, what is surprising and novel here is that this happens very rapidly, with growth transitioning even for cells within the normal length distribution for E. coli. Fundamentally, it demonstrates the fine balance of bacterial physiology, where the concentration of the genome itself (at least under rapid growth conditions) is no higher than it needs to be.

Weaknesses:

One limitation of the study is that genome concentration is largely treated as a single commodity. While this facilitates their modeling approach, one would expect that the growth phenotypes observed arise due to copy number limitation in a relatively small number of rate-limiting genes. The authors do report shifts in the composition of both the proteome and the transcriptome in response to replication inhibition, but while they report a positional effect of distance from the replication origin (reflecting loss of high-copy, origin-proximal genes), other factors shaping compositional shifts and their functional effects on growth are not extensively explored. This is particularly true for ribosomal RNA itself, which the authors assume to grow proportionately with protein. More generally, understanding which genes exert the greatest copy number-dependent influence on growth may aid both efforts to enhance (biotechnology) and inhibit (infection) bacterial growth.

Overall, this study provides a fundamental contribution to bacterial physiology by illuminating the relationship between DNA, mRNA, and protein in determining growth rate. While coarse-grained, the work invites exciting questions about how the composition of major cellular components is fine-tuned to a cell's needs and which specific gene products mediate this connection. This work has implications not only for biotechnology, as the authors discuss, but potentially also for our understanding of how DNA-targeted antibiotics limit bacterial growth.

Author response:

eLife assessment

This study represents a fundamental contribution to our understanding of how gene expression levels are controlled in bacteria. Through a series of compelling and careful experiments, relying on a mutant that blocks DNA replication but permits growth, and using various methods, the authors reveal how genome concentration rapidly becomes limiting for growth when replication is inhibited. This work contributes to our understanding of the contributions and limiting roles of DNA, mRNA, and ribosomes for growth in bacteria, and will be of considerable interest within both systems biology and microbial physiology.

Thank you!

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript by Mäkelä et al. presents compelling experimental evidence that the amount of chromosomal DNA can become limiting for the total rate of mRNA transcription and consequently protein production in the model bacterium Escherichia coli. Specifically, the authors demonstrate that upon inhibition of DNA replication the single-cell growth rate continuously decreases, in direct proportion to the concentration of active ribosomes, as measured indirectly by single-particle tracking. The decrease of ribosomal activity with filamentation, in turn, is likely caused by a decrease of the concentration of mRNAs, as suggested by an observed plateau of the total number of active RNA polymerases. These observations are compatible with the hypothesis that DNA limits the total rate of transcription and thus translation. The authors also demonstrate that the decrease of RNAp activity is independent of two candidate stress response pathways, the SOS stress response and the stringent response, as well as an anti-sigma factor previously implicated in variations of RNAp activity upon variations of nutrient sources.

Remarkably, the reduction of growth rate is observed soon after the inhibition of DNA replication, suggesting that the amount of DNA in wild-type cells is tuned to provide just as much substrate for RNA polymerase as needed to saturate most ribosomes with mRNAs. While previous studies of bacterial growth have most often focused on ribosomes and metabolic proteins, this study provides important evidence that chromosomal DNA has a previously underestimated important and potentially rate-limiting role for growth.

Thank you for the excellent summary of our work.

Strengths:

This article links the growth of single cells to the amount of DNA, the number of active ribosomes and to the number of RNA polymerases, combining quantitative experiments with theory. The correlations observed during depletion of DNA, notably in M9gluCAA medium, are compelling and point towards a limiting role of DNA for transcription and subsequently for protein production soon after reduction of the amount of DNA in the cell. The article also contains a theoretical model of transcription-translation that contains a Michaelis-Menten type dependency of transcription on DNA availability and is fit to the data. While the model fits well with the continuous reduction of relative growth rate in rich medium (M9gluCAA), the behavior in minimal media without casamino acids is a bit less clear (see comments below).

At a technical level, single-cell growth experiments and single-particle tracking experiments are well described, suggesting that different diffusive states of molecules represent different states of RNAp/ribosome activities, which reflect the reduction of growth. However, I still have a few points about the interpretation of the data and the measured fractions of active ribosomes (see below).

Apart from correlations in DNA-deplete cells, the article also investigates the role of candidate stress response pathways for reduced transcription, demonstrating that neither the SOS nor the stringent response are responsible for the reduced rate of growth. Equally, the anti-sigma factor Rsd recently described for its role in controlling RNA polymerase activity in nutrient-poor growth media, seems also not involved according to mass-spec data. While other (unknown) pathways might still be involved in reducing the number of active RNA polymerases, the proposed hypothesis of the DNA substrate itself being limiting for the total rate of transcription is appealing.

Finally, the authors confirm the reduction of growth in the distant Caulobacter crescentus, which lacks overlapping rounds of replication and could thus have shown a different dependency on DNA concentration.

Weaknesses:

There are a range of points that should be clarified or addressed, either by additional experiments/analyses or by explanations or clear disclaimers.

First, the continuous reduction of growth rate upon arrest of DNA replication initiation observed in rich growth medium (M9gluCAA) is not equally observed in poor media. Instead, the relative growth rate is immediately/quickly reduced by about 10-20% and then maintained for long times, as if the arrest of replication initiation had an immediate effect but would then not lead to saturation of the DNA substrate. In particular, the long plateau of a constant relative growth rate in M9ala is difficult to reconcile with the model fit in Fig 4S2. Is it possible that DNA is not limiting in poor media (at least not for the cell sizes studied here) while replication arrest still elicits a reduction of growth rate in a different way? Might this have something to do with the naturally much higher oscillations of DNA concentration in minimal medium?

We note that the total RNAP activity (abundance x active fraction) was also significantly reduced in poor media (Figure 3 -- supplement 4G and H) similarly to rich medium (Figure 3H). This is consistent with DNA being limiting. The main difference between rich and poor medium conditions is that the total ribosome activity in poor media (Figure 2 -- supplement 4G and H) was less affected in comparison to rich media (Figure 2H). Our interpretation of these results is that while DNA is limiting in all medium conditions (as shown by the RNAP data), changes in ribosome activity or mRNA degradation can compensate for the reduction in transcription in poor media and hence maintain better scaling of growth rates under DNA limitation. We understand how our current presentation made it confusing. We will reorganize the text and figures to better explain our results and interpretations. 

The authors argue that DNA becomes limiting in the range of physiological cell sizes, in particular for M9glCAA (Fig. 1BC). It would be helpful to know by how much (fold-change) the DNA concentration is reduced below wild-type (or multi-N) levels at t=0 in Fig 1B and how DNA concentration decays with time or cell area, to get a sense by how many-fold DNA is essentially 'overexpressed/overprovided' in wild-type cells.

We will provide an estimate.

Fig. 2: The distribution of diffusion coefficients of RpsB is fit to Gaussians on the log scale. Is this based on a model or on previous work or simply an empirical fit to the data? An exact analytical model for the distribution of diffusion constants can be found in the tool anaDDA by Vink, ..., Hohlbein Biophys J 2020. Alternatively, distributions of displacements are expressed analytically in other tools (e.g., in SpotOn).

We use an empirical fit of Gaussian mixture model (GMM) of three states to the data and extract the fractions of molecules in each state. This avoids making too many assumptions on the underlying processes, e.g. a Markovian system with Brownian diffusion. The model in anaDDA (Vink et al.) is currently limited to two-transitioning states with a maximal step number of 8 steps per track for a computationally efficient solution (longer tracks are truncated). Using a short subset of the trajectories is less accurate than using the entire trajectory and because of this, we consider full tracks with at least 9 displacements. Meanwhile, Spot-On supports a three-state model but it is still based on a semi-analytical model with a pre-calculated library of parameters created by fitting of simulated data. Neither of these models considers the effect of cell confinement, which plays a major role on single-molecule diffusion in small-sized cells such as bacteria. For these reasons, we opted to use an empirical fit to the data. We note that the fractions of active ribosomes in WT cells grown in different media, which we extracted from these diffusion measurements, are consistent with estimates obtained by others using similar or different approaches (Forchhammer and Lindhal 1971; Mohapatra and Weisshaar, 2018; Sanamrad et al., 2014).

The estimated fraction of active ribosomes in wild-type cells shows a very strong reduction with decreasing growth rate (down from 75% to 30%), twice as strong as measured in bulk experiments (Dai et al Nat Microbiology 2016; decrease from 90% to 60% for the same growth rate range) and probably incompatible with measurements of growth rate, ribosome concentrations, and almost constant translation elongation rate in this regime of growth rates. Might the different diffusive fractions of RpsB not represent active/inactive ribosomes? See also the problem of quantification above. The authors should explain and compare their results to previous work.

We agree that our measured range is somewhat larger than the estimated range from Dai et al, 2016. However, they use different media, strains, and growth conditions. We also note that Dai et al did not make actual measurements of the active ribosome fraction. Instead, they calculate the “active ribosome equivalent” based on a model that includes growth rate, protein synthesis rate, RNA/protein abundance, and the total number of amino acids in all proteins in the cell. Importantly, our measurements show the same overall trend as Dai et al, 2016. Furthermore, our results are in quantitative agreements with previous experimental measurements that use ribosome profiling (Forchhammer and Lindhal 1971) or single-ribosome tracking (Mohapatra and Weisshaar, 2018; Sanamrad et al., 2014), which, we believe, validates our approach. We will clarify this point in the revised manuscript.

To measure the reduction of mRNA transcripts in the cell, the authors rely on the fluorescent dye SYTO RNAselect. They argue that 70% of the dye signal represents mRNA. The argument is based on the previously observed reduction of the total signal by 70% upon treatment with rifampicin, an RNA polymerase inhibitor (Bakshi et al 2014). The idea here is presumably that mRNA should undergo rapid degradation upon rif treatment while rRNA or tRNA are stable. However, work from Hamouche et al. RNA (2021) 27:946 demonstrates that rifampicin treatment also leads to a rapid degradation of rRNA. Furthermore, the timescale of fluorescent-signal decay in the paper by Bakshi et al. (half life about 10min) is not compatible with the previously reported rapid decay of mRNA (24min) but rather compatible with the slower, still somewhat rapid, decay of rRNA reported by Hamouche et al.. A bulk method to measure total mRNA as in the cited Balakrishnan et al. (Science 2022) would thus be a preferred method to quantify mRNA. Alternatively, the authors could also test whether the mass contribution of total RNA remains constant, which would suggest that rRNA decay does not contribute to signal loss. However, since rRNA dominates total RNA, this measurement requires high accuracy. The authors might thus tone down their conclusions on mRNA concentration changes while still highlighting the compelling data on RNAp diffusion.

Thank you for bringing the Hamouche et al 2022 paper to our attention. We will address this point in the revised manuscript.

The proteomics experiments are a great addition to the single-cell studies, and the correlations between distance from ori and protein abundance is compelling. However, I was missing a different test, the authors might have already done but not put in the manuscript: If DNA is indeed limiting the initiation of transcription, genes that are already highly transcribed in non-perturbed conditions might saturate fastest upon replication inhibition, while genes rarely transcribed should have no problem to accommodate additional RNA polymerases. One might thus want to test, whether the (unperturbed) transcription initiation rate is a predictor of changes in protein composition. This is just a suggestion the authors may also ignore, but since it is an easy analysis, I chose to mention it here.

Thank you for the suggestion. We will provide the suggested analysis in the revised manuscript.

Related to the proteomics, in l. 380 the authors write that the reduced expression close to the ori might reflect a gene-dosage compensatory mechanism. I don't understand this argument. Can the authors add a sentence to explain their hypothesis?

We apologize for the confusion. This will be addressed in the revised manuscript.

In Fig. 1E the authors show evidence that growth rate increases with cell length/area. While this is not a main point of the paper it might be cited by others in the future. There are two possible artifacts that could influence this experiment: a) segmentation: an overestimation of the physical length of the cell based on phase-contrast images (e.g., 200 nm would cause a 10% error in the relative rate of 2 um cells, but not of longer cells). b) time-dependent changes of growth rate, e.g., due to change from liquid to solid or other perturbations. To test for the latter, one could measure growth rate as a function of time, restricting the analysis to short or long cells, or measuring growth rate for short/long cells at selected time points. For the former, I recommend comparison of phasecontrast segmentation with FM4-64-stained cell boundaries.

As the reviewer notes, the small increase in relative growth was just a minor observation that does not affect our story whether it is biologically meaningful or the result of a technical artefact. But we agree with the reviewer that others might cite it in future works and thus should be interpreted with caution.

An artefact associated with time-dependent changes (e.g. changing from liquid cultures to more solid agarose pads) is unlikely for two reasons. 1. We show that varying the time that cells spend on agarose pads relative to liquid cultures does not affect the cell size-dependent growth rate results (Figure 1 -- supplement 5B). 2. We show that the growth rate is stable from the beginning of the time-lapse with no transient effects upon cell placement on agarose pads for imaging (Figure 1 -- supplement 5B). These results were described in the Methods section where they could easily be missed. We will revise the text to discuss these controls more prominently in the Results section.

As for cell segmentation, we have run simulations and agree with the reviewer that a small overestimation of cell area (which is possible with any cell segmentation methods including ours) could lead to a small increase in relative growth with increasing cell areas. Since the finding is not important to our story, we will simply alert the readers to the possibility that the observation may be due to a small cell segmentation bias.

Reviewer #2 (Public Review):

In this work, the authors uncovered the effects of DNA dilution on E. coli, including a decrease in growth rate and a significant change in proteome composition. The authors demonstrated that the decline in growth rate is due to the reduction of active ribosomes and active RNA polymerases because of the limited DNA copy numbers. They further showed that the change in the DNA-tovolume ratio leads to concentration changes in almost 60% of proteins, and these changes mainly stem from the change in the mRNA levels.

Thank you for the support and accurate summary!

Reviewer #3 (Public Review):

Summary:

Mäkelä et al. here investigate genome concentration as a limiting factor on growth. Previous work has identified key roles for transcription (RNA polymerase) and translation (ribosomes) as limiting factors on growth, which enable an exponential increase in cell mass. While a potential limiting role of genome concentration under certain conditions has been explored theoretically, Mäkelä et al. here present direct evidence that when replication is inhibited, genome concentration emerges as a limiting factor.

Strengths:

A major strength of this paper is the diligent and compelling combination of experiment and modeling used to address this core question. The use of origin- and ftsZ-targeted CRISPRi is a very nice approach that enables dissection of the specific effects of limiting genome dosage in the context of a growing cytoplasm. While it might be expected that genome concentration eventually becomes a limiting factor, what is surprising and novel here is that this happens very rapidly, with growth transitioning even for cells within the normal length distribution for E. coli. Fundamentally, it demonstrates the fine balance of bacterial physiology, where the concentration of the genome itself (at least under rapid growth conditions) is no higher than it needs to be.

Weaknesses:

One limitation of the study is that genome concentration is largely treated as a single commodity. While this facilitates their modeling approach, one would expect that the growth phenotypes observed arise due to copy number limitation in a relatively small number of rate-limiting genes. The authors do report shifts in the composition of both the proteome and the transcriptome in response to replication inhibition, but while they report a positional effect of distance from the replication origin (reflecting loss of high-copy, origin-proximal genes), other factors shaping compositional shifts and their functional effects on growth are not extensively explored. This is particularly true for ribosomal RNA itself, which the authors assume to grow proportionately with protein. More generally, understanding which genes exert the greatest copy number-dependent influence on growth may aid both efforts to enhance (biotechnology) and inhibit (infection) bacterial growth.

We agree but feel that identifying the specific limiting genes is beyond the scope of the study. However, to examine other potential contributing factors and identify limiting gene candidates, we plan to carry out new correlation analyses between our proteomic/transcriptomic datasets and published genome-wide datasets that report various variables under unperturbed conditions (e.g., mRNA/protein concentration, mRNA degradation rates, fitness cost, transcription/translation initiation rates, and essentiality).

Overall, this study provides a fundamental contribution to bacterial physiology by illuminating the relationship between DNA, mRNA, and protein in determining growth rate. While coarse-grained, the work invites exciting questions about how the composition of major cellular components is fine-tuned to a cell's needs and which specific gene products mediate this connection. This work has implications not only for biotechnology, as the authors discuss, but potentially also for our understanding of how DNA-targeted antibiotics limit bacterial growth.

Good point about the DNA-targeted antibiotics. Thank you!

Author response:

Public Reviews: 

Reviewer #1 (Public Review): 

As a reviewer for this manuscript, I recognize its significant contribution to understanding the immune response to saprophytic Leptospira exposure and its implications for leptospirosis prevention strategies. The study is well-conceived, addressing an innovative hypothesis with potentially high impact. However, to fully realize its contribution to the field, the manuscript would benefit greatly from a more detailed elucidation of immune mechanisms at play, including specific cytokine profiles, antigen specificity of the antibody responses, and long-term immunity. Additionally, expanding on the methodological details, such as immunophenotyping panels, qPCR normalization methods, and the rationale behind animal model choice, would enhance the manuscript's clarity and reproducibility. Implementing functional assays to characterize effector T-cell responses and possibly investigating the microbiota's role could offer novel insights into the protective immunity mechanisms. These revisions would not only bolster the current findings but also provide a more comprehensive understanding of the potential for saprophytic Leptospira exposure in leptospirosis vaccine development. Given these considerations, I believe that after substantial revisions, this manuscript could represent a valuable addition to the literature and potentially inform future research and vaccine strategy development in the field of infectious diseases. 

We have been interested in understanding how both pathogenic and non-pathogenic Leptospira species affect each other on a mammalian reservoir host. With the current study we continue to elucidate the immune mechanisms engaged by pathogenic Leptospira interrogans versus non-pathogenic L. biflexa, as a follow up to our previous work (Shetty et al, 2021 PMID: 34249775, and Kundu et al 2022 PMID 35392072). We found that both species engaged partially overlapping myeloid immune cells and inflammatory signatures of infection. For example, some chemokines were increased, and macrophage and dendritic cells were engaged at 24h post inoculation with both species of Leptospira (PMID: 34249775). Thus, we questioned whether this robust innate immune response raised to eliminate an immunogenic but rather non-pathogenic bacterium, could also help restrain L. interrogans pathogenesis. In this study we show that L. biflexa pre-exposure to L. interrogans challenge mediates improved kidney homeostasis, mitigates leptospirosis severity and leads to increased shedding of L. interrogans in urine. This suggests an interspecies symbiotic commensalistic process that facilitates survival of the pathogenic species. These findings have high impact on the lives of millions of people in areas endemic for leptospirosis that are naturally exposed to non-pathogenic Leptospira species.

We will expand on the methodological details and will update the introduction and discussion to include answers to questions raised by the three reviewers to further clarify the importance and impact of our study.

Reviewer #2 (Public Review): 

Summary: 

The authors try to achieve a method of protection against pathogenic strains using saprophytic species. It is undeniable that the saprophytic species, despite not causing the disease, activates an immune response. However, based on these results, using the saprophytic species does not significantly impact the animal's infection by a virulent species. 

We separate concepts of exposure to a non-virulent bacterium that establishes a brief infection with engagement of an immune response (L. biflexa), from infection established by a virulent species of Leptospira that leads to pathogenesis (L. interrogans). While trying to understand how both pathogenic and non-pathogenic Leptospira species affect each other on a mammalian reservoir host, we previously found that L. biflexa induces immune responses that should affect immunity of populations naturally exposed to this spirochete. Thus, we designed this study to answer that question.

Strengths: 

Exposure to the saprophytic strain before the virulent strain reduces animal weight loss, reduces tissue kidney damage, and increases cellular response in mice.

Weaknesses: 

Even after the challenge with the saprophyte strain, kidney colonization and the release of bacteria through urine continue. Moreover, the authors need to determine the impact on survival if the experiment ends on the 15th. 

Another novel and unexpected aspect of our findings in the single exposure experiment was that L. biflexa pre-exposure mediated a homeostatic environment in the kidney (lower ColA1, healthier renal physiology) that restrained pathogenesis of L. interrogans after challenge, which resulted in better health outcomes and increased shedding of L. interrogans in urine; in contrast, if the kidney is compromised (high ColA1) by L. interrogans (without L. biflexa pre-exposure) there was lower shedding L. interrogans in urine. Interestingly, this suggests an interspecies symbiotic commensalistic process that facilitates survival of the pathogenic species. Thus, these data suggest that higher shedding of L. interrogans in urine may not be a hallmark of increased disease, but rather it could be the opposite.

We will include these concepts in the updated discussion.

We don’t think that extending this experiment to d21 or d28 would add relevant data to our findings. We provide survival curves for both experiments up to d15 post infection.

Reviewer #3 (Public Review): 

Summary: 

Kundu et al. investigated the effects of pre-exposure to a non-pathogenic Leptospira strain in the prevention of severe disease following subsequent infection by a pathogenic strain. They utilized a single or double exposure method to the non-pathogen prior to challenge with a pathogenic strain. They found that prior exposure to a non-pathogen prevented many of the disease manifestations of the pathogen. Bacteria, however, were able to disseminate, colonize the kidneys, and be shed in the urine. This is an important foundational work to describe a novel method of vaccination against leptospirosis. Numerous studies have attempted to use recombinant proteins to vaccinate against leptospirosis, with limited success. The authors provide a new approach that takes advantage of the homology between a non-pathogen and a pathogen to provide heterologous protection. This will provide a new direction in which we can approach creating vaccines against this re-emerging disease. 

Strengths: 

The major strength of this paper is that it is one of the first studies utilizing a live non-pathogenic strain of Leptospira to immunize against severe disease associated with leptospirosis. They utilize two independent experiments (a single and double vaccination) to define this strategy. This represents a very interesting and novel approach to vaccine development. This is of clear importance to the field. 

The authors use a variety of experiments to show the protection imparted by pre-exposure to the non-pathogen. They look at disease manifestations such as death and weight loss. They define the ability of Leptospira to disseminate and colonize the kidney. They show the effects infection has on kidney architecture and a marker of fibrosis. They also begin to define the immune response in both of these exposure methods. This provides evidence of the numerous advantages this vaccination strategy may have. Thus, this study provides an important foundation for future studies utilizing this method to protect against leptospirosis. 

Weaknesses: 

Although they provide some evidence of the utility of pretreatment with a non-pathogen, there are some areas in which the paper needs to be clarified and expanded. 

The authors draw their conclusions based on the data presented. However, they state the graphs only represent one of two independent experiments. Each experiment utilized 3-4 mice per group. In order to be confident in the conclusions, a power analysis needs to be done to show that there is sufficient power with 3-4 mice per group. In addition, it would be important to show both experiments in one graph which would inherently increase the power by doubling the group size, while also providing evidence that this is a reproducible phenotype between experiments. Overall, this weakens the strength of the conclusions drawn and would require additional statistical analysis or additional replicates to provide confidence in these conclusions. 

We will take these suggestions into consideration and will address as many of these issues as possible in the revised manuscript.

A direct comparison between single and double exposure to the non-pathogen is not able to be determined. The ages of mice infected were different between the single (8 weeks) and double (10 weeks) exposure methods, thus the phenotypes associated with LIC infection are different at these two ages. The authors state that this is expected, but do not provide a reasoning for this drastic difference in phenotypes. It is therefore difficult to compare the two exposure methods, and thus determine if one approach provides advantages over the other. An experiment directly comparing the two exposure methods while infecting mice at the same age would be of great relevance to and strengthen this work. 

Both experiments need to be analyzed as separate but complementary as they provide different hind sights into L. interrogans pathogenesis and potential solutions to the problem. Optimal measurements of disease progression (weight loss, survival curves) require infection of mice at 8 weeks. Based on this, a new L. biflexa double exposure experiment would have to start when mice are 4 weeks old which is just after weaning, and before the mouse immune system is fully developed.

Reviewer #3 (Public Review):

Summary:

Kundu et al. investigated the effects of pre-exposure to a non-pathogenic Leptospira strain in the prevention of severe disease following subsequent infection by a pathogenic strain. They utilized a single or double exposure method to the non-pathogen prior to challenge with a pathogenic strain. They found that prior exposure to a non-pathogen prevented many of the disease manifestations of the pathogen. Bacteria, however, were able to disseminate, colonize the kidneys, and be shed in the urine. This is an important foundational work to describe a novel method of vaccination against leptospirosis. Numerous studies have attempted to use recombinant proteins to vaccinate against leptospirosis, with limited success. The authors provide a new approach that takes advantage of the homology between a non-pathogen and a pathogen to provide heterologous protection. This will provide a new direction in which we can approach creating vaccines against this re-emerging disease.

Strengths:

The major strength of this paper is that it is one of the first studies utilizing a live non-pathogenic strain of Leptospira to immunize against severe disease associated with leptospirosis. They utilize two independent experiments (a single and double vaccination) to define this strategy. This represents a very interesting and novel approach to vaccine development. This is of clear importance to the field.

The authors use a variety of experiments to show the protection imparted by pre-exposure to the non-pathogen. They look at disease manifestations such as death and weight loss. They define the ability of Leptospira to disseminate and colonize the kidney. They show the effects infection has on kidney architecture and a marker of fibrosis. They also begin to define the immune response in both of these exposure methods. This provides evidence of the numerous advantages this vaccination strategy may have. Thus, this study provides an important foundation for future studies utilizing this method to protect against leptospirosis.

Weaknesses:

Although they provide some evidence of the utility of pretreatment with a non-pathogen, there are some areas in which the paper needs to be clarified and expanded.

The authors draw their conclusions based on the data presented. However, they state the graphs only represent one of two independent experiments. Each experiment utilized 3-4 mice per group. In order to be confident in the conclusions, a power analysis needs to be done to show that there is sufficient power with 3-4 mice per group. In addition, it would be important to show both experiments in one graph which would inherently increase the power by doubling the group size, while also providing evidence that this is a reproducible phenotype between experiments. Overall, this weakens the strength of the conclusions drawn and would require additional statistical analysis or additional replicates to provide confidence in these conclusions.

A direct comparison between single and double exposure to the non-pathogen is not able to be determined. The ages of mice infected were different between the single (8 weeks) and double (10 weeks) exposure methods, thus the phenotypes associated with LIC infection are different at these two ages. The authors state that this is expected, but do not provide a reasoning for this drastic difference in phenotypes. It is therefore difficult to compare the two exposure methods, and thus determine if one approach provides advantages over the other. An experiment directly comparing the two exposure methods while infecting mice at the same age would be of great relevance to and strengthen this work.

eLife assessment

This important study could potential provide insight into mechanisms for vaccine-mediated protection, although the evidence for live Leptospira contributing to protection against a pathogenic serovar is still incomplete. The work will be of interest to the scientists interested in host-pathogen interactions and leptospirosis.

Reviewer #1 (Public Review):

As a reviewer for this manuscript, I recognize its significant contribution to understanding the immune response to saprophytic Leptospira exposure and its implications for leptospirosis prevention strategies. The study is well-conceived, addressing an innovative hypothesis with potentially high impact. However, to fully realize its contribution to the field, the manuscript would benefit greatly from a more detailed elucidation of immune mechanisms at play, including specific cytokine profiles, antigen specificity of the antibody responses, and long-term immunity. Additionally, expanding on the methodological details, such as immunophenotyping panels, qPCR normalization methods, and the rationale behind animal model choice, would enhance the manuscript's clarity and reproducibility. Implementing functional assays to characterize effector T-cell responses and possibly investigating the microbiota's role could offer novel insights into the protective immunity mechanisms. These revisions would not only bolster the current findings but also provide a more comprehensive understanding of the potential for saprophytic Leptospira exposure in leptospirosis vaccine development. Given these considerations, I believe that after substantial revisions, this manuscript could represent a valuable addition to the literature and potentially inform future research and vaccine strategy development in the field of infectious diseases.

Reviewer #2 (Public Review):

Summary:

The authors try to achieve a method of protection against pathogenic strains using saprophytic species. It is undeniable that the saprophytic species, despite not causing the disease, activates an immune response. However, based on these results, using the saprophytic species does not significantly impact the animal's infection by a virulent species.

Strengths:

Exposure to the saprophytic strain before the virulent strain reduces animal weight loss, reduces tissue kidney damage, and increases cellular response in mice.

Weaknesses:

Even after the challenge with the saprophyte strain, kidney colonization and the release of bacteria through urine continue. Moreover, the authors need to determine the impact on survival if the experiment ends on the 15th.

Author response:

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

eLife assessment

This is a valuable contribution to the electric fish community, and to studies of active sensing more generally, in that it provides evidence that a well-studied behavior (chirping) may serve in active sensing rather than communication. For the most part, the evidence is solid. In particular, the evidence showing increased chirping in more cluttered environments and the relationship between chirping and movement are convincing. Nevertheless, evidence to support the argument that chirps are mostly used for navigation rather than communication is incomplete.

Thank you for the comment. In response to what seemed to be a generalized need for more evidence to support our hypothesis, we have extensively reviewed the manuscript, changed the existing figures and added new ones (3 new figures in the main text and 4 in the supplementary information section). Our edits include:

(1) changes to the written text to remove categorical statements ruling out the possible communication function of chirps. When necessary, we have also added details on why we believe a social communication function of chirps could interfere with a role in electrolocation.

(2) new experiments (and related figures) adding details on the behavioral correlates of chirping, on the effects of chirps on electric images (which are a way to represent current flow on the fish skin), and behavioral responses to ramp frequency playback EODs (used to test a continuous range of beat frequencies and fill the sampling gaps left by our experiments using real fish).

Public Reviews:

Reviewer #1 (Public Review):

The authors investigate the role of chirping in a species of weakly electric fish. They subject the fish to various scenarios and correlate the production of chirps with many different factors. They find major correlations between the background beat signals (continuously present during any social interactions) or some aspects of social and environmental conditions with the propensity to produce different types of chirps. By analyzing more specifically different aspects of these correlations they conclude that chirping patterns are related to navigation purposes and the need to localize the source of the beat signal (i.e. the location of the conspecific).

We thank the Reviewer for the extensive feedback received. Hereby we respond to each of the points raised.

We have better clarified that our intention is not to propose chirps as tools for “conspecific localization” intended as the pinpointing of its particular location. Instead, based on our observation of chirps being employed at very close ranges, we suggest that chirps may serve to assess other parameters related to “conspecific positioning” (which in a wide sense, it is still “electrolocation”), and that could be derived from the beat. These parameters might include size, relative orientation, or subtle changes in position during movement. While the experiments discussed in the manuscript do not provide a conclusive answer in this regard, we prioritize here the presentation of broader evidence for a different use of chirping. We are actively working on another manuscript that explores this aspect more in detail, but, due to space limitations, additional results had to be excluded.

In the abstract we mention a role of chirps in the enhancement of “electrolocation”, but - as above mentioned - it is here meant only in a broad sense. In the introduction (at the very end) we propose chirps as self-directed signals (homeoactive sensing). In the result paragraph dedicated to the novel environment exploration experiment the following lines were added “Most chirps (90%) in fact are produced within a distance corresponding to 1% of the maximum field intensity (i.e. roughly 30 cm; Figure S12B), indicating that chirping occurs way below the threshold range for beat detection (i.e. roughly in the range of 60-120 cm, depending on the study; see appendix 1: Detecting beats at a distance) and likely does not represent a way to improve it”. We conclude this paragraph mentioning “This further corroborates the hypothesized role of chirps in beat processing.”. The last result paragraph (on chirping in cluttered environments) ends with “This supports the notion of chirps as self-referenced probing cues, potentially employed to optimize short-range aspects of conspecific electrolocation, such as conspecific size, orientation, and swimming direction - a hypothesis that will certainly be explored in future studies.”. In the discussion paragraph entitled “probing with chirps”, we do provide hints to possible mechanisms implied in the role of chirps in beat processing. As mentioned, we have planned to add further details in another manuscript, currently in preparation.

The study provides a wealth of interesting observation of behavior and much of this data constitute a useful dataset to document the patterns of social interactions in these fish. Some data, in particular the high propensity to chirp in cluttered environments, raises interesting questions. Their main hypothesis is a useful addition to the debate on the function of these chirps and is worth being considered and explored further. However, the data they provide does not support strong conclusion statements arguing that these chirps are used for localization purposes and is even less convincing at rejecting previously established hypotheses on the communication purpose of the chirps.

We intentionally framed our aims a bit provocatively to underscore that, to date, the role of chirps in social communication has been supported solely by correlative evidence. While the evidence we provide to support the role of chirps as probes is also correlative, it opens at the same time critical questions on the long assumed role of chirps in social communication. In fact, chirping is strongly dependent on fish reciprocal positioning, highly constrained by beat frequency, and patterned in such ways that - in our opinion - makes the existence of links between chirp types and internal states less likely, as suggested instead by the current view. Moreover, the use of different chirp types does not appear specific to any of the social contexts analyzed but is primarily explained by DF (beat frequency). This observation, coupled with the analysis of chirp transitions (more self-referenced than reflecting an actual exchange between subjects), leads us to hypothesize with greater confidence that chirp production may be more related to sensing the environment, rather than transmitting information about a specific behavioral state.

Nevertheless, the Reviewer's comment is valid. We've tempered the study's conclusions by introducing the possibility of chirps serving both communication and electrolocation functions, as stated in the conclusion paragraph: "While our results do not completely dismiss the possibility of chirps serving a role in electrocommunication—probing cues could, for instance, function as proximity signals to signal presence, deter approaches, or coordinate behaviors like spawning (Henninger et al., 2018).". Nonetheless, we do emphasize that our hypothesis is more likely to apply - based on our data. We refrain from categorically excluding a communicative function for chirps (between subjects), but we hypothesize that this communication - if occurring - may contain the same type of information as the self-directed signaling implied by the “chirps as probes” idea (i.e. spatial information).

In response to the Reviewer's feedback, we've revised the end of the introduction, removing suggestions of conclusiveness: "Finally, by recording fish in different conditions of electrical 'visibility,' we provide evidence supporting a previously neglected role of chirps: homeoactive sensing." (edit: the word “validating” has been removed to give a less “conclusive” answer to the open functional questions about chirping).

I would suggest thoroughly revising the manuscript to provide a neutral description of the results and leaving any speculations and interpretations for the discussion where the authors should be careful to separate strongly supported hypotheses from more preliminary speculations. I detail below several instances where the argumentation and/or the analysis are flawed.

Following to the reviewer’s comment, we have revised the manuscript to emphasize the following points: 1) the need for a revision of the current view on chirping, 2) our proposal of an alternative hypothesis based on correlations between chirping and behavior, which were previously unexplored, and 3) our acknowledgment that while we offer evidence supporting a probing role of chirps (e.g., lack of behavioral correlation, DF-dependency, stereotypy in repeated trials, modulation by clutter and distance), we do not present here conclusive evidence for chirps detecting specific details of conspecific positioning. Neither do we exclude categorically a role of chirps in social communication.

They analyze chirp patterning and show that, most likely, a chirp by an individual is followed by a chirp in the same individual. They argue that it is rare that a chirp elicits a "response" in the other fish. Even if there are clearly stronger correlations between chirps in the same individual, they provide no statistical analysis that discards the existence of occasional "response" patterns. The fact that these are rare, and that the authors don't do an appropriate analysis of probabilities, leads to this unsupported conclusion.

We employed cross-correlation indices, calculated and assessed with a 3 standard deviation symmetrical boundary (which is a statistically sound and strict criterion). Median values were utilized to depict trends in each group/pair. To support our findings, we added new experiments and new figures: 1) a correlation analysis between chirps and behaviors, providing more convincing evidence of how chirps are employed during "scanning" swimming activity (backward swimming); 2) a text mining approach to underscore chirp-behavior correlations, employing alternative and statistically more robust methods.

One of the main pieces of evidence that chirps can be used to enhance conspecific localization is based on their "interference" measure. The measure is based on an analysis of "inter-peak-intervales". This in itself is a questionable choice. The nervous system encodes all parts of the stimulus, not just the peak, and disruption occurring at other phases of the beat might be as relevant. The interference will be mostly affected by the summed duration of intervals between peaks in the chirp AM. They do not explain why this varies with beat frequency. It is likely that the changes they see are simply an artifact of the simplistic measure. A clear demonstration that this measure is not adequate comes from the observation in Fig7E-H. They show that the interference value changes as the signal is weaker. This measure should be independent of the strength of the signal. The method is based on detecting peaks and quantifying the time between peaks. The only reason this measure could be affected by signal strength is if noisy recordings affect how the peak detection occurs. There is no way to argue that this phenomenon would happen the same way in the nervous system. Furthermore, they qualitatively argue that patterns of chirp production follow patterns of interference strength. No statistical demonstration is done. Even the qualitative appraisal is questionable. For example, they argue that there are relatively few chirps being produced for DFs of 60 or -60 Hz. But these are DF where they have only a very small sample size. The single pair of fish that they recorded at some of these frequencies might not have chirped by chance and a rigorous statistical analysis is necessary. Similarly, in Fig 5C they argue that the position of the chirps fall on areas of the graph where the interferences are strongest (darker blue) but this is far from obvious and, again, not proven.

We would like to clarify that the estimation of the effects of chirps on the beat (referred to as “beat interference”) was not intended to serve as the primary evidence supporting a different use of chirping. In fact, all the experiments conducted prior to that calculation already provide substantial evidence supporting the hypothesis we have proposed. In an attempt to address the Reviewer’s concern and to avoid misleading interpretations, we moved this part now to the Supplementary Information (see now Figures S8 and S9), in agreement with the non crucial relevance of this approach. We also added the following statement to the result paragraph entitled “Chirps significantly interfere with the beat and enhance electric image contrast”: “Obviously, measuring chirp-triggered beat interferences by using an elementary outlier detection algorithm on the distribution of beat cycles does not reflect any physiological process carried out by the electrosensory system and can be therefore used only as an oversimplified estimate.”.

Regarding the meaning of “beat interference” (as here estimated) from a perspective of brain physiology: chirp interference was calculated using the beat cycles as a reference. Beat peaks were used only to estimate beat cycle duration. Regardless of whether or not a beat peak is represented in the brain, beat cycle duration (estimated using the peaks) is the main determinant of p-unit rhythmic response to a beat. Regarding the effect of signal amplitude, this is also not very relevant. It is obvious that a chirp creates more - or less - interference based on the chirp FM and its duration (but also the sign of the DF and the magnitude of the amplitude modulation). If electroreceptor responses are entrained in waves of beat AMs and if “interference” is a measure of how such waves are scrambled, then “interference” is a measure of how chirps scramble waves of electroreceptor activity by affecting beat AMs.

The reason why the interference fades with the signal (previous figure 7, now Figure S12) is because it is weighted on the signal strength (the signals used as carrier for chirps are recalculated based on real measurements of signal strength at different distances). Nonetheless, the Reviewer is right: mathematically speaking interference would not change at all because it is just the result of an outlier detection algorithm. This outlier detection is actually set to have a 1% threshold (percent of beat contrast).

Regarding the comparison “chirps vs interference”, we did not make a statistical analysis because we wanted to just show a qualitative observation. Similar results can be obtained for slightly shorter or longer time windows, within certain limits of course (see added Figure S9, in the Supplementary Information). We hope that moving this analysis to the supplementary information makes it clear that this approach is not central to make our point.

The Reviewer’s point on the DF sampling is correct, we have reconsidered the low chirping at 60Hz as potentially the result of sampling bias and edited the respective result paragraph.

They relate the angle at which one fish produces chirps relative to the orientation of the mesh enclosing. They argue that this is related to the orientation of electric field lines by doing a qualitative comparison with a simplified estimate of field lines. To be convincing this analysis should include a quantitative comparison using the exact same body position of the two fish when the chirps are emitted.

We agree with the Reviewer, this type of experiment would be much better suited to illustrate the correlations between chirping and reciprocal positioning in fish. What we can see is that chirping occurs at certain orientations more often than others. This could have something to do with either field geometry or with locomotion in the particular test environment we have used. As mentioned earlier, we are currently editing a second manuscript which will include the type of analysis/experiment the Reviewer is thinking of. We preferred to focus in this first study on the broader behavioral correlates of chirping. We removed the mention to the field current lines because - we agree - the argument is vague as presented here.

They show that the very vast majority of chirps in Fig 6 occur when the fish are within a few centimeters (e.g. very large first bin in Fig6E-Type2). This is a situation when the other fish signal will be strongest and localization will be the easiest. It is hard to understand why the fish would need a mechanism to enhance localization in these conditions (this is the opposite of difficult conditions e.g. the "cluttered" environment).

Agreed, in fact we do not explicitly propose chirps as means to improve “electrolocation” (this word is used only broadly in the abstract) but instead as probes to extract spatial information (e.g. shape, motion, orientation) from a beat source. In a broader sense, all these spatial parameters contribute to any given instance of "localization." Because we were unable to explore all these aspects in greater detail, we chose to maintain a broader perspective. If chirps contribute to a better resolution of fine spatial attributes of conspecific locations, it is reasonable to expect higher chirping rates in proximity to the target fish.

The argumentation aimed at rejecting the well-established role of chirp in communication is weak at best. First, they ignored some existing data when they argue that there is no correlation between chirping and behavioral interactions. Particularly, Hupe and Lewis (2008) showed a clear temporal correlation between chirps and a decrease in bites during aggressive encounters. It could be argued that this is "causal evidence" (to reuse their wording) that chirps cause a decrease in attacks by the receiver fish (see Fig 8B of the Hupe paper and associated significant statistics). Also, Oboti et al. argue that social interactions involve "higher levels of locomotion" which would explain the use of chirps since they are used to localize. But chirps are frequent in "chirp chamber" paradigms where no movement is involved. They also point out that social context covaries with beat frequency and thus that it is hard to distinguish which one is linked to chirping propensity and then say that it is hard to disentangle this from "biophysical features of EOD fields affecting detection and localization of conspecific fish". But they don't provide any proof that beat frequency affects detection and localization so their argument is not clear. Last, they argue that tests in one species shouldn't be extrapolated to other species. But many of the studies arguing for the role of chirps in communication was done on brown ghost. In conclusion of this point, they do not provide any strong argument that rejects the role of chirps as a communication signal. A perspective that would be better supported by their data and consistent with past research would be to argue that, in addition to a role in communication, chirps could sometimes be used to help localize conspecifics.

We did not intend to disregard the extensive body of literature supporting a role of chirps in social communication. Rather, the primary goal of this study was to present a valid alternative perspective to this prevailing view. The existence of a well-established hypothesis does not imply that new evidence cannot change it; it simply indicates that changing it may be challenging either because it's genuinely difficult or because the idea has not been thoroughly explored. Whatever the case may be, proposing new hypotheses, whether complementary or alternative to established theories, is a challenging undertaking for a single study. We judged that starting from broad correlations would be the most desirable approach.

We did not ignore data from Hupé and Lewis 2008. We cited this study repeatedly and compared their findings to those of others, not only for the correlation chirp-behaviors but also for chirping distance considerations. However, following the Reviewer’s comment, we now cite this study in the context of the behavioral analysis recently added (data from the PSTH plots could possibly confirm the observation of lower chirps during attacks). We also cited the study by Triefenbach and Zakon 2008, which reports something along the same lines. See the statement: “Overall, these results provided mutually reinforcing evidence indicating that chirps are produced more often during locomotion or scanning-related motor activity and confirm previous reports of a lower occurrence of chirping during more direct aggressive contact (as shown also by Triefenbach and Zakon, 2008; Hupé and Lewis, 2008).”, in the result paragraph related to the behavioral correlates of chirping.

In our study we make it clear how we distinguish causal evidence (i.e. providing evidence that A is required for B) from correlation (i.e. evidence for A simply occurring together with B). We also make it clear that we are not going to provide causal evidence but we are going to provide new evidence for correlations that were so far not considered, in order to propose a new unexplored function of chirps.

The Reviewer's point on chirping during motion and while caged in a chirp chamber is valid. Indeed at first we were also puzzled by this finding. However, under the “chirps as probes” paradigm, chirping in a chirp-chamber can be explained by the need to obtain spatial information from an otherwise unreachable beat source (brown ghosts are typically exploring new environmental objects or conspecifics by actively swimming around them - something caged fish can’t do). So, eventually the observation of chirping under conditions of limited movement (such as in a chirp chamber experiment) is not in contradiction with our hypothesis, rather it can be used to support it. Further experiments are required - as rightfully pointed out - to evaluate the effects of beat frequency on beat detection. We added a note about this in the “probing with chirps” discussion paragraph.

The Reviewer's comment regarding generalization is unclear. We acknowledge that most studies are conducted in brown ghosts, as stated in the abstract. Our intention was to highlight that insights gained from this species have been applied to broaden the understanding of chirps in other species. Specifically, the "behavioral meaning idea" of chirping has been extended to other gymnotiform species producing EOD frequency modulations .

Our study's aim is not to dismiss the idea of chirps being used for communication but to present an alternative hypothesis and to provide supporting evidence. While our results may not align well with the communication theory, our intention is not dismissal but rather engaging in a discussion and exploration of alternative perspectives.

The discussion they provide on the possible mechanism by which chirps could help with localization of the conspecific is problematic. They imply that chirps cause a stronger response in the receptors. For most chirps considered here, this is not true. For a large portion of the beat frequencies shown in this paper, chirps will cause a de-synchronization of the receptors with no increase in firing rate. They cannot argue that this represents an enhanced response. They also discuss a role for having a broader frequency spectrum -during the chirp- in localization by making a parallel with pulse fish. There is no evidence that a similar mechanism could even work in wave-type fish.

We have already commented on the “localization” idea in our previous responses. The Reviewer is right in saying that we have provided only vague descriptions of the potential mechanisms implied by our hypothesis. The studies by Benda and others (2005, 2006) demonstrate a clear synchronizing effect of chirps on p-unit firing rates, especially at low DFs (at ranges similar to those considered in this study). This synchronization could lead to an enhanced response at the electroreceptor level, as described in these very studies, which in turn would result in a higher probability of firing in downstream neurons (E-cells in the ELL).

As also reported within the same works, chirps may also exert an opposite effect on p-units (i.e. desynchronization). This is what happens for large chirps at high DFs. Desynchronization may cause temporary lapses of p-unit firing, which in turn may lead to increased activity of I-cells in the ELL (which are indeed specifically tuned to p-unit lack of activity).

So, in general, if we consider both ON and OFF pyramidal cells (in the ELL) and small and large chirps, we could state that chirps can be potentially used to enhance the activity of peripheral electrosensory circuits through different mechanisms, contingent on the chirp type and beat frequency. Unfortunately, space constraints limited our ability to dig into these details in the present study.

However, to address the Reviewer’s rightful point, we now mention this in the manuscript: Since the beat AMs generated by the chirps always trigger reliable responses in primary electrosensory circuits (pyramidal cells in the ELL respond to both increases and decreases in beat AM), any chirp-triggered AM causing a sudden change in p-unit firing could potentially amplify the downstream signal (Marsat and Maler, 2010) and thus enhance EI contrast.” (see result paragraph on beat interference and electric images).

They write the whole paper as if males and females had been identified in their experiments. Although EOD frequency can provide some guess of the sex the method is unreliable. We can expect a non-negligible percentage of error in assigning sex.

We agree and in fact, in the method section we state:

“The limitation of this approach is that females cannot be distinguished from immature males with absolute certainty, since no post-mortem gonadal inspection was carried out.”

to this we added:

“Although a more accurate way to determine the sex of brown ghosts would be to consider other morphological features such as the shape of the snout, the body size, the occurrence of developing eggs, EOD frequency has been extensively used for this purpose.”

Moreover, the consistent behavioral differences observed in low frequency fish, measured with those behavioral experiments aimed at assessing responses to playback stimuli and swimming behavior in novel environments, could also be caused by a younger age (as opposed to femaleness). However, the size ranges of our fish (an admittedly unreliable proxy of age) were all comparable, making this possibility perhaps less likely.

Reviewer #2 (Public Review):

Studying the weakly electric brown ghost knifefish, the authors provide evidence that 'chirps' (brief modulations in the frequency and amplitude of the ongoing electric signal) function in active sensing (specifically homeoactive sensing) rather than communication. This is a behavior that has been very well studied, including numerous studies on the sensory coding of chirps and the neural mechanisms for chirp generation. Chirps are largely thought to function in communication behavior, so this alternative function is a very exciting possibility that could have a great impact on the field. The authors do provide convincing evidence that chirps may function in homeoactive sensing. However, their evidence arguing against a role for chirps in communication is not as strong, and neglects a large body of research. Ultimately, the manuscript has great potential but suffers from framing these two possibilities as mutually exclusive and dismissing evidence in favor of a communicative function.

We thank the Reviewer for the comment. Overall, we have edited the manuscript to soften our conclusions and avoid any strong categorical statement excluding the widely accepted role of chirps in social communication. We have added some new experiments with the aim to add more detail to the behavioral correlates of chirping and to the DF dependency of the production of different types of chirps. Nonetheless, based on our results, we are prone to conclude that the communication idea - although widely accepted - is not as well substantiated as it should be.

Although we do not dismiss the bulk of literature supporting a role of chirps in social communication, we think that our hypothesis (i.e. decoding of spatial parameters from the beat) may be not fully compatible with the social communication hypothesis for the following reasons:

(1) Chirp type dependency on DF makes chirps likely to be adaptive responses to beat frequency. While this idea is compatible with a role of chirps in the detection of beat parameters, their concurrent role in social communication would imply that chirps interacting at given beat frequencies (DFs) would communicate only (or mainly) by delivering a very limited range of “messages”. For instance, assuming type 2 chirps are related to aggression (as widely suggested), are female-male pairs - with larger DFs - interacting less aggressively than same sex pairs? Our experiments often suggested this is not the case. In addition, large DFs are not always indicative of opposite sex interactions, while they are very often characterized by the emission of large chirps. Not to mention that, despite the fact that opposite sex interactions in absence of breeding-like conditions, cannot be considered truly courtship-related, large chirps are often considered courtship signals, regardless of the reproductive state of the emitting fish.

(2) Chirping is highly affected by locomotion (consider female/male pairs with or without mesh divider) and distance (as shown in the novel environment exploration experiment). While the involvement of both parameters is compatible with a role of chirps in active sensing, a role of chirps in social communication implies that such signaling would occur only when fish are in very close proximity to each other. In this case, the beat is therefore heavily distorted not only by fish position/locomotion but also by chirps. Which means that when fish are close to each other, the 2 different types of information relayed by the beat (electrolocation and electrocommunication) would certainly interfere (this idea has been better phrased in the Introduction paragraph).

(3) In our playback experiments we could not see any meaningful matching (e.g. angry-chirp → angry-chirp or sexy-chirp → approach) between playback chirps and evoked chirps, raising doubts on the meaning associated so far with the different types. Considering that playback experiments are typically used to assess signal meaning based on how animals respond to them, this result is suggesting quite strongly that such meaning cannot be assigned to chirps.

(4) In playback experiments in which the same stimulus is provided multiple times, chirp type transitions (i.e. emission of a different chirp type after a given chirp) become predictable (as shown in the added playback experiments using ramping signals). This confirms that the choice to emit a given chirp type has something to do with beat frequency (or a change in this parameter) and not a communication of internal states. It would be otherwise unclear how a fish could change its internal state so quickly - and so reliably - even in the span of a few seconds.

Despite this evidence against a semantic content of chirps in the context of social communication, we conclude the manuscript reminding that we are not providing strong evidence dismissing the communication hypothesis, and that both could coexist (see the example of “proximity signals” in the mating context given in the concluding paragraph).

(1) The specific underlying question of this study is not made clear in the abstract or introduction. It becomes apparent in reading through the manuscript that the authors seek to test the hypothesis that chirps function in active sensing (specifically homeoactive sensing). This should be made explicitly clear in both the abstract and introduction, along with the rationale for this hypothesis.

In the abstract we state “Despite the success of this model in neuroethology over the past seven decades, the underlying logic of their electric communication remains unclear. This study re-evaluates this view, aiming to offer an alternative, and possibly complementary, explanation for why these freshwater bottom dwellers emit electric chirps.”. This statement is meant as a summary of our aims. However, in order to convey a clearer message, we have revised the whole manuscript to more explicitly articulate our objectives. In particular we stress that with our experiments we intend to provide correlative evidence for a different role of chirps (previously unexplored) with the idea to stimulate a discussion and possibly a revision of the current theory about the functional role of chirps.

In the introduction we have added a paragraph explaining our aim and also why we think that communicating through chirps could potentially interfere with efficient electrolocation: “Since both chirps and positional parameters (such as size, orientation or motion) can only be detected as perturbations of the beat (Petzold et al., 2016; Yu et al., 2012; Fotowat et al., 2013), and via the same electroreceptors, the inputs relaying both types of information are inevitably interfering. Moreover, as the majority of chirps are produced within a short range (< 50 cm; Zupanc et al., 2006; Hupé and Lewis 2008; Henninger et al., 2018; see appendix 1) this interference is likely to occur consistently during social interactions.

Under the communication-hypothesis, the assumption that chirps and beats are conveying different types of information (i.e. semantic value as opposed to position and related geometrical parameters) is therefore leaving this issue unresolved.”.

(2) My biggest issue with this manuscript is that it is much too strong in dismissing evidence that chirping correlates with context. This is captured in this sentence in the introduction, "We first show that the choice of different chirp types does not significantly correlate with any particular behavioral or social context." This very strong conclusion comes up repeatedly, and I disagree with it, for the following reasons:

In your behavioral observations, you found sex differences in chirping as well as differences between freely interacting and physically separated fish. Your model of chirp variability found that environmental experience, social experience, and beat frequency (DF) are the most important factors explaining chirp variability. Are these not all considered "behavioral or social context"? Beat frequency (DF) in particular is heavily downplayed as being a part of "context" but it is a crucial part of the context, as it provides information about the identity of the fish you're interacting with.

In your playback experiments, fish responded differently to small vs. large DFs, males chirped more than females, type 2 chirps became more frequent throughout a playback, and rises tended to occur at the end of a playback. These are all examples of context-dependent behavior.

We agree with the Reviewer’s comment and we think that probably we have been unclear in what the meaning of that statement was. We also agree with the Reviewer about what is defined as “context”, and that a given beat frequency (DF) can in the end represent a “behavioral context” as well. In order to make it clearer, we have rephrased this statement and changed it to: “We first show that the relative number of different chirp types in a given recording does not significantly correlate with any particular behavioral or social context.”. This new form refers specifically to the observation that - in all different social conditions examined - the relative amounts of different types of chirps is unchanged (see Figure S2). We thought the Reviewer maybe interpreted our statement as if we suggested that chirp type choice is random or unaffected by any social variable. We agree with the Reviewer that this is not the case. We also reported that sex differences in chirping are present, but we have emphasized they may have something to do with the propensity of the brown ghosts of either sex to swim/explore as opposed to seek refuge and wait (as suggested by our experiments in which FM pairs were either divided or freely interacting and our novel environment exploration experiments).

We agree DF is important, in fact it is the 3rd most important factor explaining chirp variance in our model. In our fish pair recordings, we see a strong correlation of chirp total variance with tank experience (one naïve, one experienced, both fish equally experienced) and social context (novel to each other/familiar to each other, subordinate/dominant, breeding/non breeding, accessible/not accessible) although data clustering seems to better distinguish “divided” vs “freely moving” conditions (and sex may also play a role as well because of the reversal of sexual dimorphism in chirp rates in precisely this case) more than other variables. However, we do not see a specific effect of these variables on the proportion of different types of chirps in any recording (see Figure S2).

We also edited the beginning of the first result paragraph and changed it to “Thus, if behavioral meaning can be attributed to different types of chirps, as posed by the prevailing view (e.g., Hagedorn and Heiligenberg, 1985; Larimer and MacDonald, 1968; Rose, 2004), one should be able to identify clear correlations between behavioral contexts characterizing different internal states and the relative amounts of different types of chirp”, to emphasize we are here assessing the meaning of different types of chirps (not of the total amount of chirping in general).

Further, you only considered the identity of interacting fish or stimulated fish, not their behavior during the interaction or during playback. Such an analysis is likely beyond the scope of this study, but several other studies have shown correlations between social behavior and chirping. In the absence of such data here, it is too strong to claim that chirping is unrelated to context.

We agree with the Reviewer, in fact this analysis was previously carried out but purposely left out in an attempt to limit the manuscript length. We have now made space for this experimental work which is now added (see the new Figure 6).

In summary, it is simply too strong to say that chirping does not correlate with context. Importantly, however, this does not detract from your hypothesis that chirping functions in homeoactive sensing. A given EOD behavior could serve both communication and homeoactive sensing. I actually suspect that this is quite common in electric fish. The two are not mutually exclusive, and there is no reason for you to present them as such. I recommend focusing more on the positive evidence for a homeoactive function and less on the negative evidence against a communication function.

We aimed to clarify that our reference was to the lack of correlation between "chirp type relative numbers" and the analyzed context. Regarding the communication function, we tempered negative statements. However, as this study stems from evidence within the established paradigm of "chirps as communication signals", and aims at proposing an alternative hypothesis, eliminating all references to it could undermine the study's purpose.

(3) The results were generally challenging to follow. In the first 4 sections, it is not made clear what the specific question is, what the approach to addressing that question is, and what specific experiment was carried out (the last two sections of the results were much clearer). The independent variables (contexts) are not clearly established before presenting the results. Instead they are often mentioned in passing when describing the results. They come across as an unbalanced hodgepodge of multiple factors, and it is not made clear why they were chosen. This makes it challenging to understand why you did what you did, the results, and their implications. For each set of major results, I recommend: First, pose a clear question. Then, describe the general approach to answering that question. Next, describe the specifics of the experimental design, with a rationale that appeals to the general approach described. Finally, describe the specific results.

The introductory sentences of the first result paragraphs have been edited, rendering the aim of the experiments more explicit.

(4) Results: "We thus predicted that, if behavioral meaning can be attributed to different types of chirps, as posed by the prevailing view (e.g., Hagedorn and Heiligenberg, 1985; Larimer and MacDonald, 1968; Rose, 2004)..." It should be made clear why this is the prevailing view, and this description should likely be moved to the introduction. There is a large body of evidence supporting this view and it is important to be complete in describing it, especially since the authors seem to seek to refute it.

We understand the Reviewer’s question and we tried to express in the introduction the main reasons for why this is the current view. We state “Different types of chirps are thought to carry different semantic content based on their occurrence during either affiliative or agonistic encounters (Larimer and MacDonald 1968; Bullock 1969; Hopkins 1974; Hagedorn and Heiligenberg 1985; Zupanc and Maler 1993; Engler et al. 2000; Engler and Zupanc 2001; Bastian et al., 2001).”. To this we added: “Although supported mainly by correlative evidence, this idea gained popularity because it is intuitive and because it matches well enough with the numerous behavioral observations of interacting brown ghosts.”.

We believe the prevailing view is based on intuition and a series of basic observed correlations repeated throughout the years. The crystallization of this idea is not due to negligence but mainly to technical limitations existing at the time of the first recordings. In order to assess the role of chirps in behaving fish a tight and precise temporal control over synched video-EOD recordings is most likely necessary, and this is a technical feature probably available only much later than the 50-60ies, when electric communication was first described.

(5) I am not convinced of the conclusion drawn by the analysis of chirp transitions. The transition matrices show plenty of 1-2 and 2-1 transitions occurring. Further, the cross-correlation analysis only shows that chirp timing between individuals is not phase-locked at these small timescales. It is entirely possible that chirp rates are correlated between interacting individuals, even if their precise timing is not.

We agree with the Reviewer: chirp repertoires recorded in different social contexts are not devoid of reciprocal chirp transitions (i.e. fish 1 chirp - to - fish 2 chirp, or vice versa). Yet our point is to emphasize that their abundance is way more limited when compared to the self-referenced ones (i.e. 1-1 and 2-2). This is a fair concern and in order to further address this point, we have added a whole new set of analyses and new experiments (see chirp-behavior correlations, PSTHs and more analysis based on more solid statistical methods; see Figure 6).

Reviewer #3 (Public Review):

Summary:

This important paper provides the best-to-date characterization of chirping in weakly electric fish using a large number of variables. These include environment (free vs divided fish, with or without clutter), breeding state, gender, intruder vs resident, social status, locomotion state and social and environmental experience, as well as with playback experiments. It applies state-of-the-art methods for reducing dimensionality and finding patterns of correlation between different kinds of variables (factor analysis, K-means). The exceptional strength of the evidence, collated from a large number of trials with many controls, leads to the conclusion that a number of commonly accepted truths about which variable affects chirping must be carefully rewritten or nuanced. Based on their extensive analyses, the authors suggest that chirps are mainly used as probes that help detect beats and objects.

Strengths:

The work is based on completely novel recordings using interaction chambers. The amount of new data and associated analyses is simply staggering, and yet, well organized in presentation. The study further evaluates the electric field strength around a fish (via modelling with the boundary element method) and how its decay parallels the chirp rate, thereby relating the above variables to electric field geometry.

The main conclusions are that the lack of any significant behavioural correlates for chirping, and the lack of temporal patterning in chirp time series, cast doubt on a communication goal for most chirps. Rather, the key determinants of chirping are the difference frequency between two interacting conspecifics as well as individual subjects' environmental and social experience. These conclusions by themselves will be hugely useful to the field. They will also allow scientists working on other "communication" systems to at least reconsider, and perhaps expand the precise goal of the probes used in those senses. There are a lot of data summarized in this paper, and thorough referencing to past work. For example, the paper concludes that there is a lack of evidence for stereotyped temporal patterning of chirp time series, as well as of sender-received chirp transitions beyond the known increase in chirp frequency during an interaction.

The alternative hypotheses that arise from the work are that chirps are mainly used as environmental probes for better beat detection and processing and object localization.

The authors also advance the interesting idea that the sinusoidal frequency modulations caused by chirps are the electric fish's solution to the minute (and undetectable by neural wetware) echo-delays available to it, due to the propagation of electric fields at the speed of light in water.

Weaknesses:

My main criticism is that the alternative putative role for chirps as probe signals that optimize beat detection could be better developed. The paper could be clearer as to what that means precisely.

We appreciate the Reviewer's kind comments. While we acknowledge that our exploration of chirp function in this study may be limited and not entirely satisfying, we made this decision due to space constraints, opting for a broader and diversified approach. We hope that future studies will build on these data and start filling the gaps. We are also working on another manuscript which is addressing this point more in detail.

Nonetheless, we considered the Reviewer’s criticism and added not only a new figure (to show more explicitly what chirps can do to the perceived electric fields, as simulated by electric images) but also more descriptive parts explaining how we think chirps may act to improve the spatial resolution of beat processing (see the discussion paragraph “probing with chirps”). In this paragraph we rendered more clearly how chirps could improve beat processing by phase shifting EODs and recovering eventual blind-spots on the fish skin caused by disruptive EOD interferences (resulting in lower beat contrast). We also mention that enhancement of electrosensory input triggered by chirps, could be localized not only at the level of electroreceptors (consider the synchronizing effects small chirps have on p-units at low frequency beats) but also at the level of ON and OFF pyramidal cells in the ELL. Looked at from the perspective of these neurons, any chirp would enhance the activity of these input lines, yet in opposite ways.

And there is an egg-and-chicken type issue as well, namely, that one needs a beat in order to "chirp" the beating pattern, but then how does chirping optimize the detection of the said beat? Perhaps the authors mean (as they wrote elsewhere in the paper) that the chirps could enhance electrosensory responses to the beat.

According to the Reviewer’s comment, we have now revised several instances of the misleading phrasing identified.

In the results on novel environment exploration: “If chirps enhance beat processing, for instance, chirping should occur within beat detection range but at a certain distance.”.

“This, in turn, could be used to validate our beat-interference estimates as meaningfully related to beat processing.” and “In all this, rises may represent an exception as their locations are spread over larger distances and even in presence of obstacles potentially occluding the beat source (such as shelters, plants, or walls), all of which are conditions in which beat detection or beat processing could be more difficult (this, could be coherent with the production of rises right at the end of EOD playbacks; Figure S5).”

Last result paragraph (clutter experiment): “Overall, these results indicate that chirping is significantly affected by the presence of environmental clutter partially disrupting - or simply obstructing - the processing of beat related information during locomotion”.

In the probing with chirps discussion paragraph “In theory, chirps could also be used to improve electrolocation of objects as well (as opposed to the processing of the beat).”.

In the conclusions: “optimizing the otherwise passive responses to the beat”.

A second criticism is that the study links the beat detection to underwater object localization. I did not see a sufficiently developed argument in this direction, nor how the data provided support for this argument. It is certainly possible that the image on the fish's body of an object in the environment will be slightly modified by introducing a chirp on the waveform, as this may enhance certain heterogeneities of the object in relation to its environment. The thrust of this argument seems to derive more from the notion of Fourier analysis with pulse type fish (and radar theory more generally) that the higher temporal frequencies in the beat waveform induced by the chirp will enable a better spatial resolution of objects. It remains to be seen whether this is significant.

The Reviewer is correct in noting that this point is not addressed in the manuscript. We introduced it as a speculative discussion point to mention alternative possibilities. These could be subject to further testing in future studies.

I would also have liked to see a proposal for new experiments that could test these possible new roles.

We have added clearer suggestions for future experiments throughout the discussion: these may be aimed at 1) improving playback experiments using more realistic copies of the brown ghost’s EODs (including harmonics), 2) assess fish reciprocal positioning during chirping in better detail and 3) test the use of chirping during target-reaching tasks in order to better assess the probing function of chirps.

The authors should recall for the readers the gist of Bastian's 2001 argument that the chirp "can adjust the beat frequency to levels that are better detectable" in the light of their current. Further, at the beginning of the "Probing with chirps" section, the 3rd way in which chirps could improve conspecific localization mentions the phase-shifting of the EOD. The authors should clarify whether they mean that the tuberous receptors and associated ELL/toral circuitry could deal with that cue, or that the T_unit pathway would be needed?

We thank the Reviewer for identifying this unclear point. We added reference to the p-units “Yet, this does not exclude the possibility that chirps could be used to briefly shift the EOD phase in order to avoid disruptive interferences caused by phase opposition (at the level of p-units)” in the above mentioned paragraph. We would prefer to omit a more detailed reference to t-units in order to avoid lengthy descriptions required to discuss the different electroreceptor types.

On p.17 I don't understand what is meant by most chirps being produced, possibly aligned with the field lines, since field lines are everywhere. And what is one to conclude from the comparison of Fig.6D and 7A? Likewise it was not clear what is meant by chirps having a detectable effect on randomly generated beats.

We agree on the valid point raised by the Reviewer and we have removed reference to current lines from the text.

In the section on Inconsistencies between behaviour and hypothesized signal meaning, the authors could perhaps nuance the interpretation of the results further in the context of the unrealistic copy of natural stimuli using EOD mimics. In particular, Kelly et al. 2008 argued that electrode placement mattered in terms of representation of a mimic fish onto the body of a real fish, and thus, if I properly understand the set up here, the movement would cause the mimic to vary in quality. This may nevertheless be a small confounding issue.

We agree with the Reviewer and added a comment at the beginning of the paragraph mentioned. “Nonetheless, it's plausible that playback stimuli, as employed in our study and others, may not faithfully replicate natural signals, thus potentially influencing the reliability of the observed behaviors. Future studies might consider replicating these findings using either natural signals or improved mimics, which could include harmonic components (excluded in this study).”

Recommendations for the authors:

8Reviewer #2 (Recommendations For The Authors):*

(1) Abstract: "...is probably the most intensely studied species..." is a weak, unsupported, and unnecessary statement. Just state that it has been heavily studied, or is one of the most well-studied,...

rephrased

(2) Abstract: "...are thus used as references to specific internal states during recordings - of either the brain or the electric organ..." This was not clear to me.

rephrased

(3) Abstract: "...the logic underlying this electric communication..." It is not clear to me what the authors mean here by "logic".

rephrased

(4) I strongly recommend clearly defining homeoactive sensing and distinguishing it from allocative sensing when this term is first introduced in the introduction. This is not a commonly used term. Most readers likely think they understand what is meant by the term active sensing, however I recommend first defining it, and then distinguishing amongst these two different types of active sensing.

rephrased

(5) Introduction: "Together with a few other species (Rose, 2004),..." More than a few. There are hundreds of species with electric organs. It is certainly not a "unique" capability.

rephrased

(6) Introduction: "But the real advantage of active electrolocation can be appreciated in the context of social interaction." This is unclear. Why is this the "real advantage" of active electrolocation when an electrically silent fish could detect an electrically communicating fish just fine without interference? Active electrolocation is needed to detect objects that are not actively emitting an electric field. It is not needed to detect signaling individuals.

rephrased

(7) Introduction: why is active sensing using EODs limited to distances of 6-12 cm? Why does it not work at closer range?

Here we meant to give a range based on published data. We rephrased it to “up to 12”.

(8) Introduction: electric fields decay with the cubed of distance, as you show in appendix 1.

rephrased

(9) Introduction: it is not clear what is meant by "blurred EOD amplitude".

rephrased (“noisy”)

(10) Figure 2C is very challenging to interpret. I recommend spending more time in the manuscript walking the reader through this analysis and its presentation.

We are grateful for the comment as we probably overlooked this point. We now added a small paragraph to explain these data in better detail.

(11) Results: "This was done by calculating the ratio between the duration of the beat cycles affected by the chirp (beat interpeak intervals) and the total duration of the beat cycles detected within a fixed time window (roughly double the size of the maximum chirp duration, 700 ms)." This was not clear to me.

We now rephrased to “Estimates of beat interference were made by calculating the ratio between the cumulative duration of the beat cycles affected by a given chirp (1 beat cycle corresponding to the beat comprised by two consecutive beat peaks, or - more simply - the beat inter-peak interval) over the cumulative duration of all the beat cycles within the time window used as a reference (700 ms; other analysis windows were tested Figure S9)” to clarify this method.

(12) Results: "For each chirp, the interference values obtained for 4 different phases (90{degree sign} steps) were averaged." Why was this done?

To consider an average effect across phases. Although it is true that chirp parameters may have a different impact on the beat, depending on EOD phase, including this parameter in our figure/s would have considerably increased the volume of data reported giving too much emphasis to an analysis we judged not crucially important. In addition, since we did not consider EOD phase in our recordings, we opted for an average estimate encompassing different phase values.

(13) Discussion: "Third, observations in a few species are generalized to all other gymnotiforms without testing for species differences (Turner et al., 2007; Smith et al., 2013; Petzold et al., 2016)." I strongly disagree with this statement. First, the studies referenced here do explicitly compare chirps across species. Second, you only studied one species here, so it is not clear to me how this is a relevant concern in interpreting your findings.

Here we have probably been unclear in the writing: the point we wanted to make is that the idea of chirps having semantic content has been generalized to other species without investigating the nature of their chirping with as much detail as done for brown ghosts.

We have now rephrased the statement and changed it to: “Second, observations in a few species are generalized to all other gymnotiforms without testing whether chirping may have similar functions in other species (Turner et al., 2007; Smith et al., 2013; Petzold et al., 2016)”

(14) Discussion: "The two beats could be indistinguishable (assuming that the mechanism underlying the discrimination of the sign of DF at low DFs, and thought to be the basis of the so called jamming avoidance response (JAR; Metzner, 1999), is not functional at higher DFs)." Why would you assume this?

What we meant here is that it is unlikely that the two DFs are not discriminated by the same mechanisms implied in the JAR, even if the DF is higher than the levels at which usually JARs are detected (i.e. DF = 1-10 Hz?). To improve clarity, we rephrased this statement. “The two beats could be indistinguishable (assuming - perhaps not realistically - that the same mechanism involved in DF discrimination at lower DF values would not work in this case; Metzner, 1999)”.

(15) Discussion: "...an idea which seems congruent with published electrophysiological studies..." How so?

Rephrased to “Based on our beat interference estimates, we propose that the occurrence of the different types of chirps at more positive DFs (such as in male-to-female chirping) may be explained by their different effect on the beat (Figure 5D; Benda et al., 2006; Walz et al., 2013).”

Reviewer #3 (Recommendations For The Authors):

On p.2 there is a discrepancy between the quoted ranges for active sensing of objects, first 10-12 cm, and then 6-12 cm further down. And in the following paragraph right below this passage, electric fields are said to decay with the squared distance (appendix 1). That expression has a cos(theta) which is inversely proportional to the distance, and so one is really dealing, as expected for dipolar fields, with a drop-off that decays with the distance cubed.

We thank the Reviewer for the comment, we have now corrected the mistake and added “cubed”. We also removed the imprecise reference to the range 6-12 cm, rephrased to “up to 12 cm”.

At the end of the section on Inconsistencies..., it is not clear what "activity levels" refers to. It should also be made clearer at the outset, and reminded in this section too, that for the authors, behavioural context does not include social experience, which is somewhat counter-intuitive.

We now specified we meant “locomotor activity levels”. Regarding the social experience we included it as “behavioral context”, we now made it clearer in the first result paragraph. We hope we resolved the confusion.

The caption of Fig.8 could use more clarity in terms of what is being compared in (C) (and is "1*2p" a typo?)

We corrected the typo and edited the figure to make the references more clear.

The concept of "high self-correlation of chirp time series" is presented only in the Conclusion using those words. The word self-correlation is not used beforehand. This needs to be fixed so the reader knows clearly what is being referred to.

Thank you for noting this. We have now changed the wording using the term “auto-correlation” and changed a statement at the beginning of the “interference” result paragraph accordingly, removing references to self-correlation.

eLife assessment

This is a valuable contribution to the electric fish community, and to studies of active sensing, in that it provides evidence that a well-studied behavior (chirping) may serve in active sensing rather than communication. This is likely to stimulate follow-up behavioral and physiological studies to determine whether the active sensing component of the behavior is pre-eminent, or whether their major function is communication. For the most part, the evidence for increased chirping in more cluttered environments and the relationship between chirping and movement are convincing. However, the evidence used to argue that chirping does not vary with behavioral context is less so, and the arguments against a communicative function of chirps are not strong. The main conclusions are only supported by correlations and remain for now at the level of an interesting hypothesis to explore.

Reviewer #1 (Public Review):

The authors investigate the role of chirping in a species of weakly electric fish. They subject the fish to various scenarios and correlate the production of chirps with many different factors. They find major correlations between the background beat signals (continuously present during any social interactions) or some aspects of social and environmental conditions with the propensity to produce different types of chirps. By analyzing more specifically different aspects of these correlations they conclude that chirping patterns are related to navigation purposes and the need to localize the source of the beat signal (i.e. the location of the conspecific).

The study provides a wealth of interesting observations of behavior and much of this data constitutes a useful dataset to document the patterns of social interactions in these fish. Some data, in particular the high propensity to chirp in cluttered environments, raises interesting questions. Their main hypothesis is a useful addition to the debate on the function of these chirps and is worth considering and exploring further.

After the initial reviewers' comments, the authors performed a welcome revision of the way the results are presented. Overall the study has been improved by the revision. However, one piece of new data is perplexing to me. The new Figure 7 presents the results of a model analysis of the strength of the EI caused by a second fish to localize when the focal fish is chirping. From my understanding of this type of model, EOD frequency is not a parameter in the model since it evaluates the strength of the field at a given point in time. Therefore the only thing that matters is the phase relationship and strength of the EOD. Assuming that the second fish's EOD is kept constant and the phases relationship is also the same, the only difference during a chirp that could affect the result of the calculation is the potential decrease in EOD amplitude during the chirp. It is indeed logical that if the focal fish decreased its EOD amplitude the target fish's EOD becomes relatively stronger. Where things are harder to understand is why the different types of chirps (e.g. type 1 vs type 2) lead to the same increase in signal even though they are typically associated with different levels of amplitude modulations. Also, it is hard to imagine that a type 2 chirps that is barely associated with any decrease in EOD amplitude (0-10% maybe), would cause doubling of the EI strength. There might be something I don't understand but the authors should provide a lot more details on how this result is obtained and convince us that it makes sense.

Reviewer #2 (Public Review):

Studying Apteronotus leptorhynchus (the weakly electric brown ghost knifefish), the authors provide evidence that 'chirps' (brief modulations in the frequency and amplitude of the ongoing electric signal) function in active sensing (specifically homeoactive sensing) rather than communication. Chirping is a behavior that has been well studied, including numerous studies on the sensory coding of chirps and the neural mechanisms for chirp generation. Chirps are largely thought to function in communication behavior, so this alternative function is a very exciting possibility that could have a great impact on the field. The authors do provide convincing evidence that chirps may function in homeoactive sensing. However, their evidence arguing against a role for chirps in communication is not as strong, and fails to sufficiently consider the evidence from a large body of existing research. Ultimately, the manuscript presents very interesting data that is sure to stimulate discussion and follow-up studies, but it suffers from dismissing evidence in support of, or consistent with, a communicative function for chirps. The authors do acknowledge that chirps could function as both a communication and homeactive sensing signal, but it seems clear they wish to argue against the former and for the latter, and the evidence is not yet there to support this.

In the introduction, the authors state, "Since both chirps and positional parameters (such as size, orientation or motion) can only be detected as perturbations of the beat, and via the same electroreceptors, the inputs relaying both types of information are inevitably interfering." I disagree with this statement, which seems to be a key assumption. Both of these features certainly modulate the activity of electroreceptors, but that does not mean those modulations are ambiguous as to their source. You do not know whether the two types of modulations can be unambiguously decoded from electroreceptor afferent population activity.

My biggest issue with this manuscript is that it is much too strong in dismissing evidence that chirping correlates with context. In your behavioral observations, you found sex differences in chirping as well as differences between freely interacting and physically separated fish. Chirps tended to occur in close proximity to another fish. Your model of chirp variability found that environmental experience, social experience, and beat frequency (DF) are the most important factors explaining chirp variability. Are these not all considered behavioral or social context? Beat frequency (DF) in particular is heavily downplayed as being a part of "context" but it is a crucial part of the context, as it provides information about the identity of the fish you're interacting with. The authors show quite convincingly that the types of chirps produced do not vary with these contexts, but chirp rates do.

Further, in your playback experiments, fish responded differently to small vs. large DFs, males chirped more than females, type 2 chirps became more frequent throughout a playback, and rises tended to occur at the end of a playback. These are all examples of context-dependent behavior.

In the results, the authors state, "Overall, the majority of chirps were produced by male subjects, in comparable amounts regardless of environmental experience (resident, intruder or equal; Figure S1A,C), social status (dominant or subordinate; Figure S1B) or social experience (novel or experienced; Figure S1D)." This is not what is shown in Figure S1. S1A shows clear differences between resident vs. intruder males, S1B shows clear differences between dominant vs. subordinate males, and S1D shows clear differences between naïve and experienced males. The analysis shown in Figure 2 would seem to support this. Indeed, the authors state, "Overall, this analysis indicated that environmental and social experience, together with beat frequency (DF) are the most important factors explaining chirp variability."

The choice of chirp type varied widely between individuals but was relatively consistent within individuals across trials of the same experiment. The authors interpret this to mean that chirping does not vary with internal state, but is it not likely that the internal states of individuals are stable under stable conditions, and that individuals may differ in these internal states across the same conditions? Stable differences in communication signals between individuals are frequently interpreted as reflecting differences between those individuals in certain characteristics, which are being communicated by these signals.

I am not convinced of the conclusion drawn by the analysis of chirp transitions. The transition matrices show plenty of 1-2 and 2-1 transitions occurring. Further, the cross-correlation analysis only shows that chirp timing between individuals is not phase-locked at these small timescales. It is entirely possible that chirp rates are correlated between interacting individuals, even if their precise timing is not. Further, it is not clear to me how "transitions" were defined. The methods do not make this clear, and it is not clear to me how you can have zero chirp transitions between two individuals when those two individuals are both generating chirps throughout an interaction.

In the results, "Although all chirp types were used during aggressive interactions, these seemed to be rather less frequent in the immediate surround of the chirps (Figure 6A)." A lack of precise temporal correlation on short timescales does not mean there is no association between the two behaviors. An increased rate of chirping during aggression is still a correlation between the two behaviors, even if chirps and specific aggressive behaviors are not tightly time-locked.

In summary, it is simply too strong to say that chirping does not correlate with context, or to claim that there is convincing evidence arguing against a communication function of chirps. Importantly, however, this does not detract from your exciting and well-supported hypothesis that chirping functions in homeoactive sensing. A given EOD behavior could serve both communication and homeoactive sensing. I actually suspect this is quite common in electric fish (both gymnotiforms and mormyrids), and perhaps in other actively sensing species such as echolocating animals. The two are not mutually exclusive.

Reviewer #3 (Public Review):

Summary:

This important paper provides the best-to-date characterization of chirping in weakly electric fish using a large number of variables. These include environment (free vs divided fish, with or without clutter), breeding state, gender, intruder vs resident, social status, locomotion state and social and environmental experience, without and with playback experiments. It applies state-of-the-art methods for reducing the dimensionality of the data and finding patterns of correlation between different kinds of variables (factor analysis, K-means). The strength of the evidence, collated from a large number of trials with many controls, leads to the conclusion that the traditionally assumed communication function of chirps may be secondary to its role in environmental assessment and exploration that takes social context into account. Based on their extensive analyses, the authors suggest that chirps are mainly used as probes that help detect beats caused by other fish and as well as objects.

Strengths:

The work is based on completely novel recordings using interaction chambers. The amount of new data and associated analyses is simply staggering, and yet, well organized in presentation. The study further evaluates the electric field strength around a fish (via modelling with the boundary element method) and how its decay parallels the chirp rate, thereby relating the above variables to electric field geometry.

The main conclusions are that the lack of any significant behavioural correlates for chirping, and the lack of temporal patterning in chirp time series, cast doubt on a primary communication goal for most chirps. Rather, the key determinants of chirping are the difference frequency between two interacting conspecifics as well as individual subjects' environmental and social experience. The paper concludes that there is a lack of evidence for stereotyped temporal patterning of chirp time series, as well as of sender-receiver chirp transitions beyond the known increase in chirp frequency during an interaction.

These conclusions by themselves will be very useful to the field. They will also allow scientists working on other "communication" systems to perhaps reconsider and expand the goals of the probes used in those senses. A lot of data are summarized in this paper, with thorough referencing to past work.

The alternative hypotheses that arise from the work are that chirps are mainly used as environmental probes for better beat detection and processing and object localization, and in this sense are self-directed signals. This led to their prediction that environmental complexity ("clutter") should increase chirp rate, which is fact was revealed by their new experiments. The authors also argue that waveform EODs have less power across high spatial frequencies compared to pulse-type fish, with a resulting relatively impoverished power of resolution. Chirping in wave-type fish could temporarily compensate for the lower frequency resolution while still being able to resolve EOD perturbations with a good temporal definition (which pulse-type fish lack due to low pulse rates).

The authors also advance the interesting idea that the sinusoidal frequency modulations caused by chirps are the electric fish's solution to the minute (and undetectable by neural wetware) echo-delays available to it, due to the propagation of electric fields at the speed of light in water. The paper provides a number of experimental avenues to pursue in order to validate the non-communication role of chirps.

Weaknesses:

My main criticism is that the alternative putative role for chirps as probe signals that optimize beat detection could be better developed. The paper could be clearer as to what that means precisely, especially since beating - and therefore detection of some aspects of beating due to the proximity of a conspecific - most often precedes chirping. One meaning the authors suggest, tentatively, is that the chirps could enhance electrosensory responses to the beat, for example by causing beat phase shifts that remediate blind spots in the electric field of view.

A second criticism is that the study links the beat detection to underwater object localization. The paper does not significantly develop that line of thought given their data - the authors tread carefully here given the speculative aspect of this link. It is certainly possible that the image on the fish's body of an object in the environment will be slightly modified by introducing a chirp on the waveform, as this may enhance certain heterogeneities of the object in relation to its environment. The thrust of this argument derives mainly from the notion of Fourier analysis with pulse type fish EOD waveforms (see above, and radar theory more generally), where higher temporal frequencies in the beat waveform induced by the chirp will enable a better spatial resolution of objects. It remains to be seen whether experiments can show this to be significant.

eLife assessment

This valuable study reports single-nucleus multiomics-based profiling of transcriptome and chromatin accessibility of mouse XX and XY primordial germ cells (PGCs). Solid data generally support the main conclusions. However, data presentation and interpretation need improvement for clarity and accuracy. The study will be of interest to developmental and reproductive biologists, as well as andrologists.

Reviewer #1 (Public Review):

Summary:

This study uses single nucleus multiomics to profile the transcriptome and chromatin accessibility of mouse XX and XY primordial germ cells (PGCs) at three time-points spanning PGC sexual differentiation and entry of XX PGCs into meiosis (embryonic days 11.5-13.5). They find that PGCs can be clustered into sub-populations at each time point, with higher heterogeneity among XX PGCs and more switch-like developmental transitions evident in XY PGCs. In addition, they identify several transcription factors that appear to regulate sex-specific pathways as well as cell-cell communication pathways that may be involved in regulating XX vs XY PGC fate transitions. The findings are important and overall rigorous. The study could be further improved by a better connection to the biological system, including the addition of experiments to validate the 'omics-based findings in vivo and putting the transcriptional heterogeneity of XX PGCs in the context of findings that meiotic entry is spatially asynchronous in the fetal ovary. Overall, this study represents an advance in germ cell regulatory biology and will be a highly used resource in the field of germ cell development.

Strengths:

(1) The multiomics data is mostly rigorously collected and carefully interpreted.

(2) The dataset is extremely valuable and helps to answer many long-standing questions in the field.

(3) In general, the conclusions are well anchored in the biology of the germ line in mammals.

Weaknesses:

(1) The nature of replicates in the data and how they are used in the analysis are not clearly presented in the main text or methods. To interpret the results, it is important to know how replicates were designed and how they were used. Two "technical" replicates are cited but it is not clear what this means.

(2) Transcriptional heterogeneity among XX PGCs is mentioned several times (e.g., lines 321-323) and is a major conclusion of the paper. It has been known for a long time that XX PGCs initiate meiosis in an anterior-to-posterior wave in the fetal ovary starting around E13.5. Some heterogeneity in the XX PGC populations could be explained by spatial position in the ovary without having to invoke novel sub-populations.

(3) There is essentially no validation of any of the conclusions. Heterogeneity in the expression of a given marker could be assessed by immunofluorescence or RNAscope.

(4) The paper sometimes suffers from a problem common to large resource papers, which is that the discussion of specific genes or pathways seems incomplete. An example here is from the analysis of the regulation of the Bnc2 locus, which seems superficial. Relatedly, although many genes and pathways are nominated for important PGC functions, there is no strong major conclusion from the paper overall.

Reviewer #2 (Public Review):

Summary:

This manuscript by Alexander et al describes a careful and rigorous application of multiomics to mouse primordial germ cells (PGCs) and their surrounding gonadal cells during the period of sex differentiation.

Strengths:

In thoughtfully designed figures, the authors identify both known and new candidate gene regulatory networks in differentiating XX and XY PGCs and sex-specific interactions of PGCs with supporting cells. In XY germ cells, novel findings include the predicted set of TFs regulating Bnc2, which is known to promote mitotic arrest, as well as the TFs POU6F1/2 and FOXK2 and their predicted targets that function in mitosis and signal transduction. In XX germ cells, the authors deconstruct the regulation of the premeiotic replication regulator Stra8, which reveals TFs involved in meiosis, retinoic acid signaling, pluripotency, and epigenetics among predictions; this finding, along with evidence supporting the regulatory potential of retinoic acid receptors in meiotic gene expression is an important addition to the debate over the necessity of retinoic acid in XX meiotic initiation. In addition, a self-regulatory network of other TFs is hypothesized in XX differentiating PGCs, including TFAP2c, TCF5, ZFX, MGA, and NR6A1, which is predicted to turn on meiotic and Wnt signaling targets. Finally, analysis of PGC-support cell interactions during sex differentiation reveals more interactions in XX, via WNTs and BMPs, as well as some new signaling pathways that predominate in XY PGCs including ephrins, CADM1, Desert Hedgehog, and matrix metalloproteases. This dataset will be an excellent resource for the community, motivating functional studies and serving as a discovery platform.

Weaknesses:

My one major concern is that the conclusion that PGC sex differentiation (as read out by transcription) involves chromatin priming is overstated. The evidence presented in the figures includes a select handful of genes including Porcn, Rimbp1, Stra8, and Bnc2 for which chromatin accessibility precedes expression. Given that the authors performed all of their comparisons between XX versus XY datasets at each timepoint, have they missed an important comparison that would be a more direct test of chromatin priming: between timepoints for each sex? Furthermore, it remains possible that common mechanisms of differentiation to XX and XY could be missing from this analysis that focused on sex-specific differences.

Reviewer #3 (Public Review):

Summary:

Alexander et al. reported the gene-regulatory networks underpinning sex determination of murine primordial germ cells (PGCs) through single-nucleus multiomics, offering a detailed chromatin accessibility and gene expression map across three embryonic stages in both male (XY) and female (XX) mice. It highlights how regulatory element accessibility may precede gene expression, pointing to chromatin accessibility as a primer for lineage commitment before differentiation. Sexual dimorphism in these elements and gene expression increases over time, and the study maps transcription factors regulating sexually dimorphic genes in PGCs, identifying sex-specific enrichment in various transcription factors.

Strengths:

The study includes step-wise multiomic analysis with some computational approach to identify candidate TFs regulating XX and XY PGC gene expression, providing a detailed timeline of chromatin accessibility and gene expression during PGC development, which identifies previously unknown PGC subpopulations and offers a multimodal reference atlas of differentiating PGC clusters. Furthermore, the study maps a complex network of transcription factors associated with sex determination in PGCs, adding depth to our understanding of these processes.

Weaknesses:

While the multiomics approach is powerful, it primarily offers correlational insights between chromatin accessibility, gene expression, and transcription factor activity, without direct functional validation of identified regulatory networks.

eLife assessment

In this fundamental study, the authors use innovative fine-scale motion capture technologies to study visual vigilance with high-acuity vision, to estimate the visual fixation of free-feeding pigeons. The authors present convincing evidence for use of the fovea to inspect predator cues, the behavioral state influencing the latency for fovea use, and the use of the fovea decreasing the latency to escape of both the focal individual and other flock members. The work will be of broad interest to behavioral ecologists.

Reviewer #1 (Public Review):

Summary:

The authors were using an innovative technic to study the visual vigilance based on high-acuity vision, the fovea. Combining motion-capture features and visual space around the head, the authors were able to estimate the visual fixation of free-feeding pigeon at any moment. Simulating predator attacks on screens, they showed that 1) pigeons used their fovea to inspect predators cues, 2) the behavioural state (feeding or head-up) influenced the latency to use the fovea and 3) the use of the fovea decrease the latency to escape of both the individual that foveate the predators cues but also the other flock members.

Strengths:

The paper is very interesting, and combines innovative technic well adapted to study the importance of high-acuity vision for spotting a predator, but also of improving the behavioural response (escaping). The results are strong and the models used are well-adapted. This paper is a major contribution to our understanding of the use of visual adaptation in a foraging context when at risk. This is also a major contribution to the understanding of individual interaction in a flock.

Weaknesses:

I have identified only two weaknesses:

(1) The authors often mixed the methods and the results, Which reduces the readability and fluidity of the manuscript. I would recommend the authors to re-structure the manuscript.<br /> (2) In some parts, the authors stated that they reconstructed the visual field of the pigeon, which is not true. They identified the foveal positions, but not the visual fields, which involve different sectors (binocular, monocular or blind). Similarly, they sometimes mix-up the area centralis and the fovea, which are two different visual adaptations.

eLife assessment

This useful study aims to add fresh insights into the sharing of lymphoid and CDP (common DC precursor) lineage origin of plasmacytoid dendritic cells (pDCs). The evidence for a small subset of pDCs sharing its origin with B cell progenitors and depending on BCL11a expression is solid, although further functional characterization of the reported pDC subset would significantly enhance the significance of the study. The study will be of relevance to cellular immunologists interested in the ontogeny of plasmacytoid dendritic cells.

Reviewer #1 (Public Review):

Summary:

Plasmacytoid dendritic cells (pDCs) represent a specialized subset of dendritic cells (DCs) known for their role in producing type I interferons (IFN-I) in response to viral infections. It was believed that pDCs originated from common DC progenitors (CDP). However, recent studies by Rodrigues et al. (Nature Immunology, 2018) and Dress et al. (Nature Immunology, 2019) have challenged this perspective, proposing that pDCs predominantly develop from lymphoid progenitors expressing IL-7R and Ly6D. A minor subset of pDCs arising from CDP has also been identified as functionally distinct, exhibiting reduced IFN-I production but a strong capability to activate T-cell responses. On the other hand, clonal lineage tracing experiments, as recently reported by Feng et al. (Immunity, 2022), have demonstrated a shared origin between pDCs and conventional DCs (cDCs), suggesting a contribution of common DC precursors to the pDC lineage.

In this context, Araujo et al. investigated the heterogeneity of pDCs in terms of both development and function. Their findings revealed that approximately 20% of pDCs originate from lymphoid progenitors common to B cells. Using Mb1-Cre x Bcl11a floxed mice, the authors demonstrated that the development of this subset of pDCs, referred to as "B-pDCs," relied on the transcription factor BCL11a. Functionally, B-pDCs exhibited a diminished capacity to produce IFN-I in response to TLR9 agonists but secreted more IL-12 compared to conventional pDCs. Moreover, B-pDCs, either spontaneously or upon activation, exhibited increased expression of activation markers (CD80/CD86/MHC-II) and a heightened ability to activate T-cell responses in vitro compared to conventional pDCs. Finally, Araujo et al. characterized these B-pDCs at the transcriptomic level using bulk and single-cell RNA sequencing, revealing them as a unique subset of pDCs expressing certain B cell markers such as Mb1, as well as specific markers (Axl) associated with cells recently described as transitional DCs.

Thus, in contrast to previous findings, this study posits that a small proportion of pDCs derive from B cell-committed lymphoid progenitors, and this subset of B-pDCs exhibits distinct functional characteristics, being less specialized in IFN-I production but rather in T cell activation.

Strengths:

Previously, the same research group delineated the significance of BCL11a as a critical transcription factor in pDC development (Ippolito et al., PNAS, 2014). This study elucidates the precise stage during hematopoiesis at which BCL11a expression becomes essential for the emergence of a distinct subset of pDCs, substantiated by robust genetic evidence in vivo. Furthermore, it underscores the shared developmental origin between pDCs and B cells, reinforcing prior research in the field that suggests a lymphoid origin of pDCs. Finally, this work attributes specific functional properties to pDCs originating from these lymphoid progenitors shared with B cells, emphasizing the early imprinting of functional heterogeneity during their development.

Weaknesses:

The authors delineate a subset of pDCs dependent on the BCL11a transcription factor, originating from lymphoid progenitors, and compare it to conventional pDCs, which they suggest differentiate from common DC progenitors of myeloid origin. However, this interpretation lacks support from the authors' data. Their single-cell RNA sequencing data identifies cells corresponding to progenitors (Prog2), from which the majority of pDCs, termed conventional pDCs, likely originate. This progenitor cell population expresses Il7r, Siglech, and Ly6D, but not Csfr1. The authors describe this progenitor as resembling a "pro-pDC myeloid precursor," yet these cells align more closely with lymphoid (Il7r+) progenitors described by Rodrigues et al. (Nature Immunology, 2018) and Dress et al. (Nature Immunology, 2019). Furthermore, analysis of their Mb1 reporter mice reveals that only a fraction of common lymphoid progenitors (CLP) express YFP, giving rise to a fraction of YFP+ pDCs. However, this does not exclude the possibility that YFP- CLP could also give rise to pDCs. The authors could address this caveat by attempting to differentiate pDCs from both YFP+ and YFP- CLPs in vitro in the presence of FLT3L. Additionally, transfer experiments using these lymphoid progenitors could be conducted in vivo to assess their differentiation potential in competitive settings.

Using their Mb1-reporter mice, the authors demonstrate that YFP pDCs originating from lymphoid progenitors are functionally distinct from conventional pDCs, mostly in vitro, but their in vivo relevance remains unknown. It is crucial to investigate how Bcl11a conditional deficiency in Mb1-expressing cells affects the anti-viral immune response, for example, using the M-CoV infection model as described by Sulczewski et al. in Nature Immunology, 2023. Particularly, the authors suggest that their B-pDCs act as antigen-presenting cells involved in T-cell activation compared to conventional pDCs. However, these findings contrast with those of Rodrigues et al., who have shown that pDCs of myeloid origin are more effective than pDCs of lymphoid origin in activating T-cell responses. The authors should discuss these discrepancies in greater detail. It is also notable that B-PDCs acquire the expression of ID2 (Figure S3A), commonly a marker of conventional/myeloid DCs. The authors could analyze in more detail the acquisition of specific myeloid features (CD11c, CX3CR1) by this B-PDCs subset and discuss how the expression of ID2 may impair classical pDC features, as ID2 is a repressor of E2-2, a master regulator of pDC fate.

Finally, through the analysis of their single-cell RNA sequencing data, the authors show that the subset of B-pDCs they identified expresses Axl, confirmed at the protein level. Given this specific expression profile, the authors suggest that B-pDCs are related to a previously described subset of transitional DCs, which were reported to share a common developmental path with pDCs, (Sulczewski et al. in Nature Immunology, 2023). While intriguing, this observation requires further phenotypic and functional characterization to substantiate this claim.

Reviewer #2 (Public Review):

Summary:

The origin of plasmatoid dendritic cells and their subclasses continues to be a debated field, akin to any immune cell field that is determined through the expression of surface markers (relative to clear subclass separation based on functional biology and experimentation). In this context, in this manuscript by Araujo et al, the authors attempt to demonstrate that a subtype of pDCs comes from lymphoid origin due to the presence of some B cell gene expression markers. They nomenclature these cells as B-pDCs. Strikingly, pDCs function via expression of IFNa where as B-pDCs do not express IFNa - thereby raising the question of what are their physiological or pathophysiological properties. B-pDCs also express AXL, a marker not seen in mouse pDCs but observed in human pDCs. Overall, using a combination of gene expression profiling of immune cells isolated from mice via RNA-seq and single-cell profiling the authors propose that B-pDCs are a novel subtype of pDCs in mice that were not previously identified and characterized.

Weaknesses:

My two points of discussion about this manuscript are as follows.

(1) How new are these observations that pDCs could also originate from common lymphoid progenitors. This fact has been previously outlined by many laboratories including Shigematsu et al, Immunity 2004. These studies in the manuscript can be considered new based on the single-cell profiling presented, only if the further characterization of the isolated B-pDCs is performed at the functional biology level. Overlapping gene expression profiles are often seen in developing immune cell types- especially when only evaluated at the RNA expression level- and can lead to cell type complexity (and identification of new cell types) that are not biologically and functionally relevant.

(2) The authors hardly perform any experiments to interrogate the function of these B-pDCs. The discussion on this topic can be enhanced. Ideally, some biological experiments would confirm that B-pDCs are important.

eLife assessment

This useful study identifies amino acid residues in the C. elegans RNA-binding protein NHL-2 that are required for RNA binding in vitro and NHL-2 function in vivo. The evidence in support of the authors' mechanistic model is currently incomplete, as data implicating specific NHL-2 amino acids in RNA binding per se in vivo are not presented. This manuscript will be of interest to scientists working in the area of gene regulation.

Reviewer #1 (Public Review):

Summary:

C. elegans NHL-2 is a member of the conserved TRIM-NHL RNA binding protein family, with known functions in promoting small regulatory RNA function, including the conserved let-7 family microRNAs. Since NHL-2 promotes microRNA function, the authors seek to address if this function is due to direct binding of a mRNA target shared with the miRNA pathway. They successfully solve the crystal structure of NHL-2's NHL domain and discover residues Tyr935/Arg978 are required for RNA binding in vitro. In C. elegans, they establish that Tyr935/Arg978 are required for nhl-2 to promote let-7 microRNA function. Processing body (P body) size is increased in nhl-2 (Y935A R978A) and null mutants. The microRNA Argonautes, ALG-1 and ALG-2, also show increased binding to known let-7 mRNA targets in nhl-2 null mutants. Together these data suggest a lack of mRNA turnover in the absence of functional NHL-2. NHL-2 may function with CGH-1 and IFET-1 to promote let-7 miRISC function.

Strengths:

The authors successfully solve the structure of NHL-2's NHL domain. Although unable to crystalize it bound to RNA they are able to predict residues important for RNA binding based on charge, position and comparison with other known NHL domain structures crystalized with RNA. In vitro RNA binding assays confirm that Tyr935/Arg978 are required for RNA binding in vitro.

Weaknesses:

(1) In vivo, authors use a combination of established let-7 microRNA genetics and a 3' UTR reporter assay to establish that Tyr935/Arg978 are required for nhl-2 to promote let-7 microRNA function. However, they do not demonstrate that full length NHL-2 actually binds RNA directly in vivo in the Tyr935/Arg978 mutated background. While the presented genetic evidence suggests nhl(RBlf) acts much like the nhl-2 null, it is never demonstrated that full length NHL-2(RBlf) is actually RNA binding defective/dead in vivo. Yet several times in the text this is implied or stated. For example,<br /> o page 8, section title. "RNA binding is essential for NHL-2 function in heterochronic pathway"<br /> o page 9 - line 13-14. "Together, these data indicate that the RING and NHL domains are required for the normal function of NHL-2, but that the loss of RNA-binding activity has a more pronounced phenotype, suggesting that RNA-binding is critical for NHL-2 function."<br /> o page 11, line 3-4. "Together these experiments support the conclusion that... RNA binding is essential for its function"<br /> The language should be softened (e.g., page 8: "Residues required for RNA binding in vitro are required for NHL-2 function in heterochronic path") or additional experiments should be performed to support that NHL-2(RBlf) is in fact RNA binding defective/dead, like wild-type NHL-2 vs NHL-2(RBlf) RIP-qPCR for let-7 targets.

(2) Authors report that Processing body (P body) size is dependent on nhl-2 and the Tyr935/Arg978 residues. microRNA Argonautes, ALG-1 and ALG-2, also show increased binding to known let-7 mRNA targets in nhl-2 null mutants (unfortunately requirement of Tyr935/Arg978 is not tested). However total levels of these mRNAs are unchanged. Authors propose these data together support a role for nhl-2 in promoting microRNA target turnover. Unfortunately, it is unclear how increased P body size with no observed increase of microRNA target levels are to be resolved.

(3) The authors propose a model where NHL-2, CGH-1(DDX6) and IFET-1(eIF4E-transporter/4E-T) promote microRNA mediated translational repression and possibly turnover based on nhl-2-dependent IFET-1 interaction with ALG-1, cgh-1's synthetic interaction with both nhl-2 and ifet-1 to enhance let-7-mediated alae development, and conservation of known interactions between Dead Box helicases and eiF4A, which is supplemented by ALPHAFold modelling of IFET-1. The Boag lab previously characterized ifet-1 as a translational repressor required for germline P granule formation (Sengupta 2013 J Cell Sci). The role of NHL-2 RNA binding is unclear in this model as is any more molecular evidence of direct NHL-2, CGH-1 and IFET-1 interaction.

(4) In Figure 5, adult nhl-2(ok818) worms express the mCherry when the putative NHL-2 binding sites in the lin-28 3'UTR reporter are mutated. Couldn't this be interpreted as suggesting that the observed phenotype is nhl-2 independent? The authors mention this as an "interesting" observation in text, but I find it concerning. The authors should address this issue more directly. The reporter expression data needs to be quantified.

(5) I am frankly confused at the direction the manuscript takes in the Discussion section. The role of NHL-2 RNA binding, which has been the core of the paper, is seemingly disregarded and exchanged for what is mainly speculation about protein-protein level regulation with CGH-1 and IFET-1. This is all based on only a few pieces of data that do not include any analysis using the nhl-2(RBlf): nhl-2-dependent IFET-1 interaction with ALG-1, cgh-1's synthetic interaction with both nhl-2 and ifet-1 to enhance let-7-mediated alae development, and conservation of known interactions between Dead Box helicases and eiF4A, which is supplemented by ALPHAFold modelling of IFET-1. I'd strongly suggest reworking the text to better integrate IFET-1 or skip it and refocus the Discussion around the majority of the data characterizing NHL-2 RNA binding.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors provide structural analysis of the NHL domain for C. elegans NHL-2 and provide functional analysis of the NHL RNA binding domain. Their data support a model in which NHL-2 binding to mRNA targets through U rich motifs to promote miRISC regulation of translation and mRNA stability.

Strengths:

The authors present convincing data to describe the structure of the NHL-2 NHL domain along with functional analysis that supports an important role for two amino acids that are required for RNA binding activity. The function of these two amino acids were further studied through phenotypic assays to analyze their contribution to miRNA mediated regulation through the let-7 pathway. These data support an important role for RNA binding activity of NHL-2 in the regulation of miRNA dependent pathways. Genetic interactions support a role for the eIF4E binding protein IFET-1 in the miRISC activity.

Weaknesses:

The use of phenotypic assays to monitor let-7 pathway activity could be better explained so that the reader can more easily follow the significance of changes in alae formation or col-19::gfp expression.

The challenges of comparing expression levels using extrachromosomal arrays should be acknowledged.

The figure legends need to be revised to more clearly and accurately explain what is shown in the figures.

Reviewer #3 (Public Review):

Summary:

The manuscript by Saadat et al., examines the structure and function of the NHL-2 RNA binding domain in miRNA-mediated gene regulation in C. elegans. NHL-2 has previously been shown to function in miRNA and other smRNA pathways in C. elegans but its mechanism of action is unclear. The authors present a crystal structure that revealed candidate RNA binding residues. In vitro binding assays confirmed that these amino acids were required for RNA binding. The authors tested the importance of the RING and NHL domains in NHL-2 by mutating the endogenous gene using CRISPR and analyzing developmental and molecular effects in C. elegans. They concluded that the RNA binding domain of NHL-2 and co-factors, including CGH-1 and IFET-1, are important for the regulation of some miRNA targets in developing C. elegans.

Strengths:

The NHL-2 structural work and in vitro analyses of RNA binding activity are rigorous. The work is important for providing new structural information for an important post-transcriptional regulator.

Weaknesses:

The in vivo studies to better understand the role of NHL and several cofactors require further controls, replicates or better explanations of the methods and analyses in order to support the conclusions. In particular, protein levels of the mutant NHL-2 strains should be analyzed to rule out differences in expression contributing to the results; the reporter strategy would be improved by showing it is dependent on miRNA regulation, including an internal control and adding quantitative data; validation of similar levels of ALG-1 protein in the immunoprecipitation experiments would add confidence for the differences in levels of miRNA targets detected.

eLife assessment

This study presents a light-entrainable synthetic oscillator in bacteria, the optorepressilator. The authors develop a toolbox using optogenetics that makes the cellular oscillator easily controllable. This toolbox is valuable, contributing both to bioengineering and to the understanding of biological dynamical systems. The comparison with a mathematical model, population, and single-cell measurements demonstrate convincingly that the planned system was achieved and is suitable to control and study biological oscillators.

Reviewer #1 (Public Review):

Summary:

The "optorepressilator", an optically controllable genetic oscillator based on the famous E. coli 3-repressor (LacI, TetR, CI) oscillator "repressilator", was developed. An individual repressilator shows a stable oscillation of the protein levels with a relatively long period that extends a few doubling times of E. coli, but when many cells oscillate, their phases tend to desynchronize. The authors introduced an additional optically controllable promoter through a conformal change of CcaS protein and let it control how much additional CI is produced. By tightly controlling the leak from the added promoter, the authors successfully kept the original repressilator oscillation when the added promoter was not activated. In contrast, the oscillation was stopped by expressing the additional CI. Using this system, the authors showed that it is possible to synchronise the phase of the oscillation, especially when the activation happens as a short pulse at the right phase of the repressilator oscillation. The authors further show that, by changing the frequency of the short pulses, the repressilator was entrained to various ratios to the pulse period, and the author could reconstruct the so-called "Arnold tongues", the signature of entrainment of the nonlinear oscillator to externally added periodic perturbation. The behaviour is consistent with the simplified mathematical model that simulates the protein concentration using ordinary differential equations.

Strengths:

Optical control of the oscillation of the protein clock is a powerful and clean tool for studying the synthetic oscillator's response to perturbation in a well-controlled and tunable manner. The article utilizes the plate reader setup for population average measurements and the mother machine setup for single-cell measurements, and they compensate nicely to acquire necessary information.

Weaknesses:

The current paper added the optogenetically controlled perturbation to control the phase of oscillation and entrainment, but there are a few other works that add external perturbation to a collection of cells that individually oscillate to study phase shift and/or entrainment. The current paper lacks discussion about the pros and cons of the current system compared to previously analyzed systems.

Reviewer #2 (Public Review):

Summary:

In this manuscript by Cannarsa et. al., the authors describe the engineering of a light-entrainable synthetic biological oscillator in bacteria. It is based on an upgraded version of one of the first synthetic circuits to be constructed, the repressilator. The authors sought to make this oscillator entrainable by an external forcing signal, analogous to the way natural biological oscillators (like the circadian clock) are synchronized. They reasoned that an optogenetic system would provide a convenient and flexible means of manipulation. To this end, the authors exploited the CcaS-CcaA light-switchable system, which allows activation and deactivation of transcription by green and red light, respectively. They used this system to make the expression of one of the repressilator's transcription factors (lacI) light-controlled, from a construct separated from the main repressilator plasmid. This way, under red light the oscillator runs freely, but exposure to green light causes overexpression of the lacI, pushing the system into a specific state. Consequently, returning to red light will restore the oscillations from the same phase in all cells, effectively synchronizing the cell population.

After demonstrating the functionality of the basic concept, the authors combined modeling and experiments to show how periodic exposure to green light enables efficient entrainment, and how the frequency of the forcing signal affects the oscillatory behavior (detuning).

This work provides an important demonstration of engineering tunability into a foundational genetic circuit, expands the synthetic biology toolbox, and provides a platform to address critical questions about synchronization in biological oscillators. Due to the flexibility of the experimental system, it is also expected to provide a fertile ground for future testing of theoretical predictions regarding non-linear oscillators.

Strengths:

* The study provides a simple and elegant mechanism for the entertainment of a synthetic oscillator. The design relies on optogenetic proteins, which enable efficient experimentation compared to alternative approaches (like using chemical inducers). This way, a static culture (without microfluidics or change of growth media) can be easily exposed to flexible temporal sequences of the zeitgeber, and continuously measured through time.

* The study makes use of both plate-reader-based population-level readout and mother-machine single-cell measurements. Synchronization through entrainment is a single cell level phenomenon, but with a clear population-level manifestation. Thus, this experimental approach combination provides a strong validation to their system. At the same time, differences between the readout from the two systems have emerged, and provided a further opportunity for model refinement and testing.

* The authors correctly identified the main optimization goal, namely the effective leakiness of their construct even under red light. Then, they successfully overcame this issue using synthetic biology approaches.

* The work is supported by a simplified model of the repressilator, which provides a convenient analytical and numerical means to draw testable predictions. The model predictions are well aligned with the experimental evidence.

Weaknesses:

* Even after optimizing the expression level of the light-sensitive gene, the system is very sensitive, i.e., a very short exposure is sufficient to elicit the strongest entertainment. This limited dynamic range might hamper some model testing and future usage.

* As a result of the previous point, the system is entrained by transiently "breaking" the oscillator: each pulse of green light represents a Hopf bifurcation into a single attractor. it means that the system cannot oscillate in constant green light. In comparison, this is generally not the case for natural zeitgebers like light and temperature for the circadian rhythms. Extreme values might prevent oscillations (not necessarily due to breaking the core oscillator), but usually, free running is possible in a wide range of constant conditions. In some cases, the free-running period length will vary as a function of the constant value.

While the approach presented in this manuscript is valid, a comprehensive analysis of more subtle modes of repressilator entrainment could also be of value.

* The entire work makes use of a single intensity and single duration of the green pulse to force entrainment. While the model has clear predictions for how those modalities should affect entrainment, none of the experiments attempted to validate those predictions.

Author response:

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

We thank you for the time you took to review our work and for your feedback! 

The major changes to the manuscript are:

(1) We have added visual flow speed and locomotion velocity traces to Figure 5 as suggested.

(2) We have rephrased the abstract to more clearly indicate that our statement regarding acetylcholine enabling faster switching of internal representations in layer 5 is speculative.

(3) We have further clarified the positioning of our findings regarding the basal forebrain cholinergic signal in visual cortex in the introduction.

(4) We have added a video (Video S1) to illustrate different mouse running speeds covered by our data.

A detailed point-by-point response to all reviewer concerns is provided below.

Reviewer #1 (Recommendations For The Authors):

The authors have addressed most of the concerns raised in the initial review. While the paper has been improved, there are still some points of concern in the revised version. 

Major comments

(1) Page 1, Line 21: The authors claim, "Our results suggest that acetylcholine augments the responsiveness of layer 5 neurons to inputs from outside of the local network, enabling faster switching between internal representations during locomotion." However, it is not clear which specific data or results support the claim of "switching between internal representations." ... 

Authors' response: "... That acetylcholine enables a faster switching between internal representations in layer 5 is a speculation. We have attempted to make this clearer in the discussion. ..." 

In the revised version, there is no new data added to directly support the claim - "Our results suggest acetylcholine ..., enabling faster switching between internal representations during locomotion" (in the abstract). The authors themselves acknowledge that this statement is speculative. The present data only demonstrate that ACh reduces the response latency of L5 neurons to visual stimuli, but not that ACh facilitates quicker transitions in neuronal responses from one visual stimulus to another. To maintain scientific rigor and clarity, I recommend the authors amend this sentence to more accurately reflect the findings. 

This might be a semantic disagreement? We would argue both a gray screen and a grating are visual stimuli. Hence, we are not sure we understand what the reviewer means by “but not that ACh facilitates quicker transitions in neuronal responses from one visual stimulus to another”. We concur, our data only address one of many possible transitions, but it is a switch between distinct visual stimuli that is sped up by ACh. Nevertheless, we have rephrased the sentence in question by changing “our data suggest” to “based on this we speculate” - but are not sure whether this addresses the reviewer’s concern.  

(2) Page 4, Line 103: "..., a direct measurement of the activity of cholinergic projection from basal forebrain to the visual cortex during locomotion has not been made." This statement is incorrect. An earlier study by Reimer et al. indeed imaged cholinergic axons in the visual cortex of mice running on a wheel. 

Authors' response: "We have clarified this as suggested. However, we disagree slightly with the reviewer here. The key question is whether the cholinergic axons imaged originate in basal forebrain. While Reimer et al. 2016 did set out to do this, we believe a number of methodological considerations prevent this conclusion: ... Collins et al. 2023 inject more laterally and thus characterize cholinergic input to S1 and A1, ..."

The authors pointed out some methodological caveats in previous studies that measured the BF input in V1, and I agree with them on several points. Nonetheless, the statement that "a direct measurement of the activity of cholinergic projection from basal forebrain to visual cortex during locomotion has not been made. ... Prior measurements of the activity of cholinergic axons in visual cortex have all relied on data from a cross of ChAT-Cre mice with a reporter line ..." (Page 4, Line 103) seems to be an oversimplification. In fact, contrary to what the authors noted, Collins et al. (2023) conducted direct imaging of BF cholinergic axons in V1 (Fig. 1) - "Selected axon segments were chosen from putative retrosplenial, somatosensory, primary and secondary motor, and visual cortices". They used a viral approach to express GCaMP in BF axons to bypass the limitations associated with the use of a GCaMP reporter mouse line - "Viral injections were used for BF- ACh studies to avoid imaging axons or dendrites from cholinergic projections not arising from the BF (e.g. cortical cholinergic interneurons)." The authors should reconsider the text. 

The reason we think that our statement here was – while simplified – accurate, is that Collins et al. do record from cholinergic axons in V1, but they don’t show these data (they only show pooled data across all recordings sites). By superimposing the recording locations of the Collins paper on the Allen mouse brain atlas (Figure R1), we estimate that of the approximately 50 recording sites, most are in somatosensory and somatomotor areas of cortex, and only 1 appears to be in V1, something that is often missed as it is not really highlighted in that paper. If this is indeed correct, we would argue that the data in the Collins et al. paper are not representative of cholinergic activity in visual cortex (we fear only the authors would know for sure). Nevertheless, we have rephrased again. 

Author response image 1.

Overlay of the Collins et al. imaging sites (red dots, black outline and dashed circle) on the Allen mouse brain atlas (green shading). Very few (we estimate that it was only 1) of the recording sites appear to be in V1 (the lightest green area), and maybe an additional 4 appear to be in secondary visual areas.  

Minor comments

(1) It is unclear which BF subregion(s) were targeted in this study. 

Authors' response: Thanks for pointing this out. We targeted the entire basal forebrain (medial septum, vertical and horizontal limbs of the diagonal band, and nucleus basalis) with our viral injections. ... We have now added the labels for basal forebrain subregions targeted next to the injection coordinates in the manuscript. 

The authors provided the coordinates for their virus injections targeting the BF subregions - "(AP, ML, DV (in mm): ... ; +0.6, +0.6, -4.9 (nucleus basalis) ..." Is this the right coordinates for the nucleus basalis? 

Thank you for catching this - this was indeed incorrect. The coordinates were correct, but our annotation of brain region was not (as the reviewer correctly points out, these coordinates are in the horizontal limb of the diagonal band, not the nucleus basalis). We have corrected this.

Reviewer #2 (Recommendations For The Authors):

Thank you for addressing most of the points raised in my original review. I still some concerns relating to the analysis of the data. 

(1) I appreciate the authors point that getting mice to reliably during head-fixed recordings can require training. Since mice in this study were not trained to run, their low speed of locomotion limits the interpretation of the results. I think this is an important potential caveat and I have retained it in the public review. 

This might be a misunderstanding. The Jordan paper was a bit of an outlier in that we needed mice to run at very high rates due to fact that our recording times was only minutes. Mice were chosen such that they would more or less continuously run, to maximize the likelihood that they would run during the intracellular recordings. This was what we tried to convey in our previous response. The speed range covered by the analysis in this paper is 0 cm/s to 36 cm/s. 36 cm/s is not far away from the top speed mice can reach on this treadmill (30 cm/s is 1 revolution of the treadmill per second). In our data, the top speed we measured across all mice was 36 cm/s. In the Jordan paper, the peak running speed across the entire dataset was 44 cm/s. Based on the reviewer’s comment, we suspect that the reviewer may be under the impression that 30 cm/s is a relatively slow running speed. To illustrate what this looks like we have made added a video (Video S1) to illustrate different running speeds. 

(2) The majority of the analyses in the revised manuscript focus on grand average responses, which may mask heterogeneity in the underlying neural populations. This could be addressed by analysing the magnitude and latency of responses for individual neurons. For example, if I understand correctly, the analyses include all neurons, whether or not they are activated, inhibited, or unaffected by visual stimulation and locomotion. For example, while on average layer 2/3 neurons are suppressed by the grating stimulus (Figure 4A), presumable a subset are activated. Evaluating the effects of optogenetic stimulation and locomotion without analyzing them at the level of individual neurons could result in misleading conclusions. This could be presented in the form of a scatter plot, depicting the magnitude of neuronal responses in locomotion vs stationary condition, and opto+ vs no opto conditions. 

We might be misunderstanding. The first part of the comment is a bit too unspecific to address directly. In cases in which we find the variability is relevant to our conclusions, we do show this for individual cells (e.g.the latencies to running onset are shown as histograms for all cells and axons in Figure S1). It is also unclear to us what the reviewer means by “Evaluating the effects of optogenetic stimulation and locomotion without analyzing them at the level of individual neurons could result in misleading conclusions”. Our conclusions relate to the average responses in L2/3, consistent with the analysis shown. All data will be freely available for anyone to perform follow-up analysis of things we may have missed. E.g., the specific suggestion of presenting the data shown in Figure 4 as a scatter plot is shown below (Figure R2). This is something we had looked at but found not to be relevant to our conclusions. The problem with this analysis is that it is difficult to estimate how much the different sources of variability contribute to the total variability observed in the data, and no interesting pattern is clearly apparent. All relevant and clear conclusions are already captured by the mean differences shown in Figure 4. 

Author response image 2.

Optogenetic activation of cholinergic axons in visual cortex primarily enhances responses of layer 5, but not layer 2/3 neurons. Related to Figure 4. (A) Average calcium response of layer 2/3 neurons in visual cortex to full field drifting grating in the absence or presence of locomotion. Each dot is the average calcium activity of an individual neuron during the two conditions. (B) As in A, but for layer 5 neurons. (C) As in A, but comparing the average response while the mice were stationary, to that while cholinergic axons were optogenetically stimulated. (D) As in C, but for layer 5 neurons. (E) Average calcium response of layer 2/3 neurons in visual cortex to visuomotor mismatch, without and with optogenetic stimulation of cholinergic axons in visual cortex. (F) As in E, but for layer 5 neurons. (G) Average calcium response of layer 2/3 neurons in visual cortex to locomotion onset in closed loop, without and with optogenetic stimulation of cholinergic axons in visual cortex. (H) As in G, but for layer 5 neurons.

(3) To help the reader understand the experimental conditions in open loop experiments, please include average visual flow speed traces for each condition in Figure 5. 

We have added the locomotion velocity and visual flow speeds to the corresponding conditions in Figure

eLife assessment

This important study by Yogesh and Keller provides a set of results describing the response properties of cholinergic input and its functional impacts in the mouse visual cortex. They found that cholinergic inputs are elevated by locomotion in a binary manner regardless of locomotor speeds, and activation of cholinergic input differently modulated the activity of Later 2/3 and Layer 5 visual cortex neurons induced by bottom-up (visual stimuli) and top-down (visuomotor mismatch) inputs. The experiments are cutting-edge and well-executed, and the results are convincing.

Reviewer #1 (Public Review):

The paper submitted by Yogesh and Keller explores the role of cholinergic input from the basal forebrain (BF) in the mouse primary visual cortex (V1). The study aims to understand the signals conveyed by BF cholinergic axons in the visual cortex, their impact on neurons in different cortical layers, and their computational significance in cortical visual processing. The authors employed two-photon calcium imaging to directly monitor cholinergic input from BF axons expressing GCaMP6 in mice running through a virtual corridor, revealing a strong correlation between BF axonal activity and locomotion. This persistent activation during locomotion suggests that BF input provides a binary locomotion state signal. To elucidate the impact of cholinergic input on cortical activity, the authors conducted optogenetic and chemogenetic manipulations, with a specific focus on L2/3 and L5 neurons. They found that cholinergic input modulates the responses of L5 neurons to visual stimuli and visuomotor mismatch, while not significantly affecting L2/3 neurons. Moreover, the study demonstrates that BF cholinergic input leads to decorrelation in the activity patterns of L2/3 and L5 neurons.

This topic has garnered significant attention in the field, drawing the interest of many researchers actively investigating the role of BF cholinergic input in cortical activity and sensory processing. The experiments and analyses were thoughtfully designed and conducted with rigorous standards, providing evidence of layer-specific differences in the impact of cholinergic input on neuronal responses to bottom-up (visual stimuli) and top-down inputs (visuomotor mismatch).

Reviewer #2 (Public Review):

The manuscript investigates the function of basal forebrain cholinergic axons in mouse primary visual cortex (V1) during locomotion using two-photon calcium imaging in head-fixed mice. Cholinergic modulation has previously been proposed to mediate the effects of locomotion on V1 responses. The manuscript concludes that the activity of basal forebrain cholinergic axons in visual cortex provides a signal which is more correlated with binary locomotion state than locomotion velocity of the animal and finds no evidence for modulation of cholinergic axons by locomotion velocity. Cholinergic axons did not seem to respond to grating stimuli or visuomotor prediction error. Optogenetic stimulation of these axons increased the amplitude of responses to visual stimuli and decreased the response latency of layer 5 excitatory neurons, but not layer 2/3 neurons. Moreover, optogenetic or chemogenetic stimulation of cholinergic inputs reduced pairwise correlation of neuronal responses. These results provide insight into the role of cholinergic modulation to visual cortex and demonstrate that it affects different layers of visual cortex in a distinct manner. The experiments are well executed and the data appear to be of high quality. However, further analyses may be required to fully support some of the study's conclusions. Specifically, the analyses of the effects of locomotion and stimulation of cholinergic inputs present grand averages of responses across all neurons, and therefore may mask heterogeneity across layer 2/3 and layer 5 neurons.

Author response: 

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing.

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks.

Strengths:

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models.

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation.

(2) Multiple quantification metrics and controls are used to support the main conclusions and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.

(3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model.

Weaknesses:

Major problems with the work are: (1) mechanistic explanation of the results in specific E-I networks, (2) parameter exploration, and (3) the functional significance of the specific E-I model.

(1) The main problem with the paper is a lack of mechanistic analysis of the models. The models are treated like biological entities and only tested with different assays and metrics to describe their different features (e.g. different geometry of representation in Fig. 4). Given that all the key parameters of the models are known and can be changed (unlike biological networks), it is expected to provide a more analytical account of why specific networks show the reported results. For instance, what is the key mechanism for medium amplification in specific E/I network models (Fig. 3)? How does the specific geometry of representation/manifolds (in Fig. 4) emerge in terms of excitatory-inhibitory interactions, and what are the main mechanisms/parameters? Mechanistic account and analysis of these results are missing in the current version of the paper.

We agree with the reviewer that a mechanistic analysis of manifold geometry is of high interest and we will address this issue in our revisions. We are currently exploring approaches to better understand how amplification of activity is controlled in E/I assemblies, and how geometric modifications can be described in terms of elementary excitatory and inhibitory interactions. We expect these approaches to provide new mechanistic insights into representational manifolds.

(2) The second major issue with the study is a lack of systematic exploration and analysis of the parameter space. Some parameters are biologically constrained, but not all the parameters. For instance, it is not clear what the justification for the choice of synaptic time scales are (with E synaptic time constants being larger than inhibition: tau_syn_i = 10 ms, tau_syn_E = 30 ms). How would the results change if they are varying these - and other unconstrained - parameters? It is important to show how the main results, especially the manifold localisation, would change by doing a systematic exploration of the key parameters and performing some sensitivity analysis. This would also help to see how robust the results are, which parameters are more important and which parameters are less relevant, and to shed light on the key mechanisms.

We varied neuronal and network parameters in the past and we are currently performing additional systematic parameter variations to further address this comment. Preliminary results indicate that networks with similar properties can be obtained with equal synaptic time constants and biophysical parameters for all E and I neurons, thus supporting the notion that representational geometry is determined primarily by connectivity. Results of parameter variations will be reported in the revised manuscript.

(3) It is not clear what the main functional advantage of the specific E-I network model is compared to random networks. In terms of activity, they show that specific E-I networks amplify the input more than random networks (Fig. 3). But when it comes to classification, the effect seems to be very small (Fig. 5c). Description of different geometry of representation and manifold localization in specific networks compared to random networks is good, but it is more of an illustration of different activity patterns than proving a functional benefit for the network. The reader is still left with the question of what major functional benefits (in terms of computational/biological processing) should be expected from these networks, if they are to be a good model for olfactory processing and learning.

One possibility for instance might be that the tasks used here are too easy to reveal the main benefits of the specific models - and more complex tasks would be needed to assess the functional enhancement (e.g. more noisy conditions or more combination of odours). It would be good to show this more clearly - or at least discuss it in relation to computation and function.

We agree that further insights into potential benefits of manifold representations would be interesting. In the initial manuscript we performed analyses of pattern classification primarily to examine whether the structured E/I networks studied here can support pattern classification at all, given that they do not exhibit discrete attractor states or global pattern completion. As structured E/I networks still support pattern classification when activity is read out from neuronal subsets, we concluded that structured E/I networks are not in conflict with the general notion of pattern classification by autoassociation. In addition, manifold representations may support a variety of other computations that we discussed only superficially.  In the revised we are planning to address this issue in more depth by additional discussion and analyses. In particular, we are planning to address the hypothesis that manifold geometry provides a continuous distance metric to analyze relationships between inputs and relevant stimuli (learned odors) in the presence of irrelevant stimulus components (non-learned odors).

Reviewer #2 (Public Review):

Summary:

The authors conducted a comparative analysis of four networks, varying in the presence of excitatory assemblies and the architecture of inhibitory cell assembly connectivity. They found that co-tuned E-I assemblies provide network stability and a continuous representation of input patterns (on locally constrained manifolds), contrasting with networks with global inhibition that result in attractor networks.

Strengths:

The findings presented in this paper are very interesting and cutting-edge. The manuscript effectively conveys the message and presents a creative way to represent high-dimensional inputs and network responses. Particularly, the result regarding the projection of input patterns onto local manifolds and continuous representation of input/memory is very Intriguing and novel. Both computational and experimental neuroscientists would find value in reading the paper.

Weaknesses:

Intuitively, classification (decodability) in discrete attractor networks is much better than in networks that have continuous representations. This could also be shown in Figure 5B, along with the performance of the random and tuned E-I networks. The latter networks have the advantage of providing network stability compared to the Scaled I network, but at the cost of reduced network salience and, therefore, reduced input decodability. The authors may consider designing a decoder to quantify and compare the classification performance of all four networks.

As suggested by the reviewer, we will explicitly examine decodability by different types of networks in the revised manuscript.

Networks featuring E/I assemblies could potentially represent multistable attractors by exploring the parameter space for their reciprocal connectivity and connectivity with the rest of the network. However, for co-tuned E-I networks, the scope for achieving multistability is relatively constrained compared to networks employing global or lateral inhibition between assemblies. It would be good if the authors mentioned this in the discussion. Also, the fact that reciprocal inhibition increases network stability has been shown before and should be cited in the statements addressing network stability (e.g., some of the citations in the manuscript, including Rost et al. 2018, Lagzi & Fairhall 2022, and Vogels et al. 2011 have shown this).

We thank the reviewer for this comment and will revise the manuscript accordingly.

Providing raster plots of the pDp network for familiar and novel inputs would help with understanding the claims regarding continuous versus discrete representation of inputs, allowing readers to visualize the activity patterns of the four different networks. (similar to Figure 1B).

We will follow the suggestion by the reviewer and include raster plots of responses to both familiar and novel inputs in the revised manuscript.

Reviewer #3 (Public Review):

Summary:

This work investigates the computational consequences of assemblies containing both excitatory and inhibitory neurons (E/I assembly) in a model with parameters constrained by experimental data from the telencephalic area Dp of zebrafish. The authors show how this precise E/I balance shapes the geometry of neuronal dynamics in comparison to unstructured networks and networks with more global inhibitory balance. Specifically, E/I assemblies lead to the activity being locally restricted onto manifolds - a dynamical structure in between high-dimensional representations in unstructured networks and discrete attractors in networks with global inhibitory balance. Furthermore, E/I assemblies lead to smoother representations of mixtures of stimuli while those stimuli can still be reliably classified, and allow for more robust learning of additional stimuli.

Strengths:

Since experimental studies do suggest that E/I balance is very precise and E/I assemblies exist, it is important to study the consequences of those connectivity structures on network dynamics. The authors convincingly show that E/I assemblies lead to different geometries of stimulus representation compared to unstructured networks and networks with global inhibition. This finding might open the door for future studies for exploring the functional advantage of these locally defined manifolds, and how other network properties allow to shape those manifolds.

The authors also make sure that their spiking model is well-constrained by experimental data from the zebrafish pDp. Both spontaneous and odor stimulus triggered spiking activity is within the range of experimental measurements. But the model is also general enough to be potentially applied to findings in other animal models and brain regions.

Weaknesses:

I find the point about pattern completion a bit confusing. In Fig. 3 the authors argue that only the Scaled I network can lead to pattern completion for morphed inputs since the output correlations are higher than the input correlations. For me, this sounds less like the network can perform pattern completion but it can nonlinearly increase the output correlations. Furthermore, in Suppl. Fig. 3 the authors show that activating half the assembly does lead to pattern completion in the sense that also non-activated assembly cells become highly active and that this pattern completion can be seen for Scaled I, Tuned E+I, and Tuned I networks. These two results seem a bit contradictory to me and require further clarification, and the authors might want to clarify how exactly they define pattern completion.

We believe that this comment concerns a semantic misunderstanding and apologize for any lack of clarity. The reviewer is correct that “pattern completion” in morphing experiments can be described as a nonlinear increase in output correlations in response to related inputs. This is different from the results obtained by simulated current injections because currents were targeted to subsets of assembly neurons and the analysis focused on firing rates within and outside assemblies. We referred to results of both experiments as “pattern completion” because this has been standard in the neurobiological and in the computer science literature, respectively. However, we agree that this can cause confusion and we will revise the manuscript to clarify this issue.

The authors argue that Tuned E+I networks have several advantages over Scaled I networks. While I agree with the authors that in some cases adding this localized E/I balance is beneficial, I believe that a more rigorous comparison between Tuned E+I networks and Scaled I networks is needed: quantification of variance (Fig. 4G) and angle distributions (Fig. 4H) should also be shown for the Scaled I network. Similarly in Fig. 5, what is the Mahalanobis distance for Scaled I networks and how well can the Scaled I network be classified compared to the Tuned E+I network? I suspect that the Scaled I network will actually be better at classifying odors compared to the E+I network. The authors might want to speculate about the benefit of having networks with both sources of inhibition (local and global) and hence being able to switch between locally defined manifolds and discrete attractor states.

As pointed out already in response to reviewer 1, we agree that the potential computational benefits of continuous manifold representations in comparison to discrete attractor states is an important point that merits further exploration and discussion. We are therefore planning to include a more in-depth discussion and to perform further analyses. The specific suggestions of the reviewer will be addressed.

At a few points in the manuscript, the authors use statements without actually providing evidence in terms of a Figure. Often the authors themselves acknowledge this, by adding the term "not shown" to the end of the sentence. I believe it will be helpful to the reader to be provided with figures or panels in support of the statements.

Thank you for this comment. We shall be happy to include additional data figures in the revised manuscript.

Reviewer #3 (Public Review):

Summary:

This work investigates the computational consequences of assemblies containing both excitatory and inhibitory neurons (E/I assembly) in a model with parameters constrained by experimental data from the telencephalic area Dp of zebrafish. The authors show how this precise E/I balance shapes the geometry of neuronal dynamics in comparison to unstructured networks and networks with more global inhibitory balance. Specifically, E/I assemblies lead to the activity being locally restricted onto manifolds - a dynamical structure in between high-dimensional representations in unstructured networks and discrete attractors in networks with global inhibitory balance. Furthermore, E/I assemblies lead to smoother representations of mixtures of stimuli while those stimuli can still be reliably classified, and allow for more robust learning of additional stimuli.

Strengths:

Since experimental studies do suggest that E/I balance is very precise and E/I assemblies exist, it is important to study the consequences of those connectivity structures on network dynamics. The authors convincingly show that E/I assemblies lead to different geometries of stimulus representation compared to unstructured networks and networks with global inhibition. This finding might open the door for future studies for exploring the functional advantage of these locally defined manifolds, and how other network properties allow to shape those manifolds.

The authors also make sure that their spiking model is well-constrained by experimental data from the zebrafish pDp. Both spontaneous and odor stimulus triggered spiking activity is within the range of experimental measurements. But the model is also general enough to be potentially applied to findings in other animal models and brain regions.

Weaknesses:

I find the point about pattern completion a bit confusing. In Fig. 3 the authors argue that only the Scaled I network can lead to pattern completion for morphed inputs since the output correlations are higher than the input correlations. For me, this sounds less like the network can perform pattern completion but it can nonlinearly increase the output correlations. Furthermore, in Suppl. Fig. 3 the authors show that activating half the assembly does lead to pattern completion in the sense that also non-activated assembly cells become highly active and that this pattern completion can be seen for Scaled I, Tuned E+I, and Tuned I networks. These two results seem a bit contradictory to me and require further clarification, and the authors might want to clarify how exactly they define pattern completion.

The authors argue that Tuned E+I networks have several advantages over Scaled I networks. While I agree with the authors that in some cases adding this localized E/I balance is beneficial, I believe that a more rigorous comparison between Tuned E+I networks and Scaled I networks is needed: quantification of variance (Fig. 4G) and angle distributions (Fig. 4H) should also be shown for the Scaled I network. Similarly in Fig. 5, what is the Mahalanobis distance for Scaled I networks and how well can the Scaled I network be classified compared to the Tuned E+I network? I suspect that the Scaled I network will actually be better at classifying odors compared to the E+I network. The authors might want to speculate about the benefit of having networks with both sources of inhibition (local and global) and hence being able to switch between locally defined manifolds and discrete attractor states.

At a few points in the manuscript, the authors use statements without actually providing evidence in terms of a Figure. Often the authors themselves acknowledge this, by adding the term "not shown" to the end of the sentence. I believe it will be helpful to the reader to be provided with figures or panels in support of the statements.

eLife assessment

This important study introduces a biologically constrained model of telencephalic area of adult zebrafish to highlight the significance of precisely balanced memory networks in olfactory processing. The authors convincingly show that their model performs better in multiple situations (for e.g. in terms of network stability and shaping the geometry of representations), compared to traditional attractor networks and persistent activity. However the study lacks a mechanistic understanding of the results in terms of parameter sensitivity analysis. The work supports recent studies reporting functional E/I subnetworks in several sensory cortexes, and will be of interest to both theoretical and experimental neuroscientists studying network dynamics based on structured excitatory and inhibitory interactions.

Reviewer #1 (Public Review):

Summary:

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing.

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks.

Strengths:

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models.

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation.<br /> (2) Multiple quantification metrics and controls are used to support the main conclusions and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.<br /> (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model.

Weaknesses:

Major problems with the work are: (1) mechanistic explanation of the results in specific E-I networks, (2) parameter exploration, and (3) the functional significance of the specific E-I model.

(1) The main problem with the paper is a lack of mechanistic analysis of the models. The models are treated like biological entities and only tested with different assays and metrics to describe their different features (e.g. different geometry of representation in Fig. 4). Given that all the key parameters of the models are known and can be changed (unlike biological networks), it is expected to provide a more analytical account of why specific networks show the reported results. For instance, what is the key mechanism for medium amplification in specific E/I network models (Fig. 3)? How does the specific geometry of representation/manifolds (in Fig. 4) emerge in terms of excitatory-inhibitory interactions, and what are the main mechanisms/parameters? Mechanistic account and analysis of these results are missing in the current version of the paper.

(2) The second major issue with the study is a lack of systematic exploration and analysis of the parameter space. Some parameters are biologically constrained, but not all the parameters. For instance, it is not clear what the justification for the choice of synaptic time scales are (with E synaptic time constants being larger than inhibition: tau_syn_i = 10 ms, tau_syn_E = 30 ms). How would the results change if they are varying these - and other unconstrained - parameters? It is important to show how the main results, especially the manifold localisation, would change by doing a systematic exploration of the key parameters and performing some sensitivity analysis. This would also help to see how robust the results are, which parameters are more important and which parameters are less relevant, and to shed light on the key mechanisms.

(3) It is not clear what the main functional advantage of the specific E-I network model is compared to random networks. In terms of activity, they show that specific E-I networks amplify the input more than random networks (Fig. 3). But when it comes to classification, the effect seems to be very small (Fig. 5c). Description of different geometry of representation and manifold localization in specific networks compared to random networks is good, but it is more of an illustration of different activity patterns than proving a functional benefit for the network. The reader is still left with the question of what major functional benefits (in terms of computational/biological processing) should be expected from these networks, if they are to be a good model for olfactory processing and learning.<br /> One possibility for instance might be that the tasks used here are too easy to reveal the main benefits of the specific models - and more complex tasks would be needed to assess the functional enhancement (e.g. more noisy conditions or more combination of odours). It would be good to show this more clearly - or at least discuss it in relation to computation and function.

Reviewer #2 (Public Review):

Summary:

The authors conducted a comparative analysis of four networks, varying in the presence of excitatory assemblies and the architecture of inhibitory cell assembly connectivity. They found that co-tuned E-I assemblies provide network stability and a continuous representation of input patterns (on locally constrained manifolds), contrasting with networks with global inhibition that result in attractor networks.

Strengths:

The findings presented in this paper are very interesting and cutting-edge. The manuscript effectively conveys the message and presents a creative way to represent high-dimensional inputs and network responses. Particularly, the result regarding the projection of input patterns onto local manifolds and continuous representation of input/memory is very Intriguing and novel. Both computational and experimental neuroscientists would find value in reading the paper.

Weaknesses:

Intuitively, classification (decodability) in discrete attractor networks is much better than in networks that have continuous representations. This could also be shown in Figure 5B, along with the performance of the random and tuned E-I networks. The latter networks have the advantage of providing network stability compared to the Scaled I network, but at the cost of reduced network salience and, therefore, reduced input decodability. The authors may consider designing a decoder to quantify and compare the classification performance of all four networks.

Networks featuring E/I assemblies could potentially represent multistable attractors by exploring the parameter space for their reciprocal connectivity and connectivity with the rest of the network. However, for co-tuned E-I networks, the scope for achieving multistability is relatively constrained compared to networks employing global or lateral inhibition between assemblies. It would be good if the authors mentioned this in the discussion. Also, the fact that reciprocal inhibition increases network stability has been shown before and should be cited in the statements addressing network stability (e.g., some of the citations in the manuscript, including Rost et al. 2018, Lagzi & Fairhall 2022, and Vogels et al. 2011 have shown this).

Providing raster plots of the pDp network for familiar and novel inputs would help with understanding the claims regarding continuous versus discrete representation of inputs, allowing readers to visualize the activity patterns of the four different networks. (similar to Figure 1B).

Author response:

eLife assessment

The authors present an algorithm and workflow for the inference of developmental trajectories from single-cell data, including a mathematical approach to increase computational efficiency. While such efforts are in principle useful, the absence of benchmarking against synthetic data and a wide range of different single-cell data sets make this study incomplete. Based on what is presented, one can neither ultimately judge if this will be an advance over previous work nor whether the approach will be of general applicability.

We thank the eLife editor for the valuable feedback. We wish to emphasize that both, benchmarking against other methods and validation on a synthetic dataset (“dyntoy”) are indeed presented in Supplementary Note, although we failed to sufficiently emphasize it in the main text. 

We will extend the benchmarking to more TI methods and we will improve the results and discussion sections to present those facts more clearly to the reader.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors present tviblindi, a computational workflow for trajectory inference from molecular data at single-cell resolution. The method is based on (i) pseudo-time inference via expecting hitting time, (ii) sampling of random walks in a directed acyclic k-NN where edges are oriented away from a cell of origin w.r.t. the involved nodes' expected hitting times, and (iii) clustering of the random walks via persistent homology. An extended use case on mass cytometry data shows that tviblindi can be used elucidate the biology of T cell development.

Strengths:

- Overall, the paper is very well written and most (but not all, see below) steps of the tviblindi algorithm are explained well.

- The T cell biology use case is convincing (at least to me: I'm not an immunologist, only a bioinformatician with a strong interest in immunology).

We thank the reviewer for feedback and suggestions that we will accommodate, we respond point-by-point below

Weaknesses:

- The main weakness of the paper is that a systematic comparison of tviblindi against other tools for trajectory inference (there are many) is entirely missing. Even though I really like the algorithmic approach underlying tviblindi, I would therefore not recommend to our wet-lab collaborators that they should use tviblindi to analyze their data. The only validation in the manuscript is the T cell development use case. Although this use case is convincing, it does not suffice for showing that the algorithms's results are systematically trustworthy and more meaningful (at least in some dimension) than trajectories inferred with one of the many existing methods.

We have compared tviblindi to several trajectory inference methods (Supplementary note section 8.2: Comparison to state-of-the-art methods, namely Monocle3 (v1.3.1) Cao et al. (2019), Stream (v1.1) Chen et al. (2019), Palantir (v1.0.0) Setty et al. (2019), VIA (v0.1.89) Stassen et al. (2021) and PAGA (scanpy==1.9.3) Wolf et al. (2019).) We will add thorough and systematic comparisons to the other algorithms mentioned by reviewers. We will include extended evaluation on publically available datasets.

Also, we have successfully used tviblindi to investigate human B-cell development in primary immunodeficiency (manuscript in revisions), double negative T-cells development in ALPS (Autoimmune Lymphoproliferative Syndrome) by mass cytometry (project in progress).

- The authors' explanation of the random walk clustering via persistent homology in the Results (subsection "Real-time topological interactive clustering") is not detailed enough, essentially only concept dropping. What does "sparse regions" mean here and what does it mean that "persistent homology" is used? The authors should try to better describe this step such that the reader has a chance to get an intuition how the random walk clustering actually works. This is especially important because the selection of sparse regions is done interactively. Therefore, it's crucial that the users understand how this selection affects the results. For this, the authors must manage to provide a better intuition of the maths behind clustering of random walks via persistent homology.

In order to satisfy both reader types: the biologist and the mathematician, we explain the mathematics in detail in the Supplementary Note, section 4. We will improve the Results text to better point the reader to the mathematical foundations in the Supplementary Note.

- To motivate their work, the authors write in the introduction that "TI methods often use multiple steps of dimensionality reduction and/or clustering, inadvertently introducing bias. The choice of hyperparameters also fixes the a priori resolution in a way that is difficult to predict." They claim that tviblindi is better than the original methods because "analysis is performed in the original high-dimensional space, avoiding artifacts of dimensionality reduction." However, in the manuscript, tviblindi is tested only on mass cytometry data which has a much lower dimensionality than scRNA-seq data for which most existing trajectory inference methods are designed. Since tviblindi works on a k-NN graph representation of the input data, it is unclear if it could be run on scRNA-seq data without prior dimensionality reduction. For this, cell-cell distances would have to be computed in the original high-dimensional space, which is problematic due to the very high dimensionality of scRNA-seq data. Of course, the authors could explicitly reduce the scope of tviblindi to data of lower dimensionality, but this would have to be stated explicitly.

In the manuscript we tested the framework on the scRNA-seq data from Park et al 2020 (DOI: 10.1126/science.aay3224). To illustrate that tviblindi can work directly in the high-dimensional space, we applied the framework successfully on imputed 2000 dimensional data.

The idea behind tviblindi is to be able to work without the necessity to use non-linear dimensionality reduction techniques, which reduce the dimensionality to a very low number of dimensions and whose effects on the data distribution are difficult to predict. On the other hand the use of (linear) dimensionality reduction techniques which effectively suppress noise in the data such as PCA is a good practice (see also response to reviewer 2). We will emphasize this in the revised version and add the results of the corresponding analysis.

- Also tviblindi has at least one hyper-parameter, the number k used to construct the k-NN graphs (there are probably more hidden in the algorithm's subroutines). I did not find a systematic evaluation of the effect of this hyper-parameter.

Detailed discussion of the topic is presented in the Supplementary Note, section 8.1, where Spearman correlation coefficient between pseudotime estimated using k=10 and k=50 nearest neighbors was 0.997.   The number k however does affect the number of candidate endpoints. But even when larger k causes spurious connection between unrelated cell fates, the topological clustering of random walks allows for the separation of different trajectories. We will expand the “sensitivity to hyperparameters section” also in response to reviewer 2.

Reviewer #2 (Public Review):

Summary:

In Deconstructing Complexity: A Computational Topology Approach to Trajectory Inference in the Human Thymus with tviblindi, Stuchly et al. propose a new trajectory inference algorithm called tviblindi and a visualization algorithm called vaevictis for single-cell data. The paper utilizes novel and exciting ideas from computational topology coupled with random walk simulations to align single cells onto a continuum. The authors validate the utility of their approach largely using simulated data and establish known protein expression dynamics along CD4/CD8 T cell development in thymus using mass cytometry data. The authors also apply their method to track Treg development in single-cell RNA-sequencing data of human thymus.

The technical crux of the method is as follows: The authors provide an interactive tool to align single cells along a continuum axis. The method uses expected hitting time (given a user input start cell) to obtain a pseudotime alignment of cells. The pseudotime gives an orientation/direction for each cell, which is then used to simulate random walks. The random walks are then arranged/clustered based on the sparse region in the data they navigate using persistent homology.

We thank the reviewer for feedback and suggestions that we will accommodate, we respond point-by-point below.

Strengths:

The notion of using persistent homology to group random walks to identify trajectories in the data is novel.

The strength of the method lies in the implementation details that make computationally demanding ideas such as persistent homology more tractable for large scale single-cell data.

This enables the authors to make the method more user friendly and interactive allowing real-time user query with the data.

Weaknesses:

The interactive nature of the tool is also a weakness, by allowing for user bias leading to possible overfitting for a specific data.

tviblindi is not designed as a fully automated TI tool (although it implements a fully automated module), but as a data driven framework for exploratory analysis of unknown data. There is always a risk of possible bias in this type of analysis - starting with experimental design, choice of hyperparameters in the downstream analysis, and an expert interpretation of the results. The successful analysis of new biological data involves a great deal of expert knowledge which is difficult to a priori include in the computational models.

tvilblindi tries to solve this challenge by intentionally overfitting the data and keeping the level of resolution on a single random walk. In this way we aim to capture all putative local relationships in the data. The on-demand aggregation of the walks using the global topology of the data allows researchers to use their expert knowledge to choose the right level of detail (as demonstrated in the Figure 4 of the manuscript) while relying on the topological structure of the high dimensional point cloud. At all times tviblindi allows to inspect the composition of the trajectory to assess the variance in the development, possible hubs on the KNN-graph etc.

The main weakness of the method is lack of benchmarking the method on real data and comparison to other methods. Trajectory inference is a very crowded field with many highly successful and widely used algorithms, the two most relevant ones (closest to this manuscript) are not only not benchmarked against, but also not sited. Including those that specifically use persistent homology to discover trajectories (Rizvi et.al. published Nat Biotech 2017). Including those that specifically implement the idea of simulating random walks to identify stable states in single-cell data (e.g. CellRank published in Lange et.al Nat Meth 2022), as well as many trajectory algorithms that take alternative approaches. The paper has much less benchmarking, demonstration on real data and comparison to the very many other previous trajectory algorithms published before it. Generally speaking, in a crowded field of previously published trajectory methods, I do not think this one approach will compete well against prior work (especially due to its inability to handle the noise typical in real world data (as was even demonstrated in the little bit of application to real world data provided).

We provide comparisons of tviblindi and vaevictis in the Supplementary Note, section 8.2, where we compare it to Monocle3 (v1.3.1) Cao et al. (2019), Stream (v1.1) Chen et al. (2019), Palantir (v1.0.0) Setty et al. (2019), VIA (v0.1.89) Stassen et al. (2021) and PAGA (scanpy==1.9.3) Wolf et al. (2019). We use two datasets: artificial Dyntoy and real mass cytometry thymus+peripheral blood dataset. We thank the reviewer for suggesting specific methods.  CellRank was excluded from the benchmarking as it was originally designed for RNA-velocity data (not available in mass cytometry data), but will include recent upgrade CellRank2 (preprint at doi.org/10.1101/2023.07.19.549685) which offers more flexibility.

We will add further benchmarking as suggested by the reviewer in the course of revisions.

Beyond general lack of benchmarking there are two issues that give me particular concern. As previously mentioned, the algorithm is highly susceptible to user bias and overfitting. The paper gives the example (Figure 4) of a trajectory which mistakenly shows that cells may pass from an apoptotic phase to a different developmental stage. To circumvent this mistake, the authors propose the interactive version of tviblindi that allows users to zoom in (increase resolution) and identify that there are in fact two trajectories in one. In this case, the authors show how the author can fix a mistake when the answer is known. However, the point of trajectory inference is to discover the unknown. With so much interactive options for the user to guide the result, the method is more user/bias driven than data-driven. So a rigorous and quantitative discussion of robustness of the method, as well as how to ensure data-driven inference and avoid over-fitting would be useful.

Local directionality in expression data is a challenge which is not, to our knowledge, solved. And we are not sure it can be solved entirely, even theoretically. The random walks passing “through” the apoptotic phase are biologically infeasible, but it is an (unbiased) representation of what the data look like based on the diffusion model. It is a property of the data (or of the panel design), which has to be interpreted properly rather than a mistake. Of note, except for Monocle3 (which does not provide the directionality) other tested methods did not discover this trajectory at all.

The “zoom in” has in fact nothing to do with “passing through the apoptosis”. We show how the researcher can investigate the suggested trajectory to see if there is an additional structure of interest and/or relevance. This investigation is still data driven (although not fully automated). Anecdotally in this particular case this branching was discovered by an bioinformatician, who knew nothing about the presence of beta-selection in the data. 

We show that the trajectory of apoptosis of cortical thymocytes consists of 2 trajectories corresponding to 2 different checkpoints (beta-selection and positive/negative selection). This type of structure, where 2 (or more) trajectories share the same path for most of the time, then diverge only to be connected at a later moment (immediately from the point of view of the beta-selection failure trajectory) is a challenge for TI algorithms and none of tested methods gave a correct result. More importantly there seems to be no clear way to focus on these kinds of structures (common origin and common fate) in TI methods.

Of note, the “zoom in” is a recommended and convenient method to look for an inner structure, but it does not necessarily mean addition of further homological classes. Indeed, in this case the reason that the structure is not visible directly is the limitation of the dendrogram complexity (only branches containing at least 10% of simulated random walks are shown by default).

In summary, tviblindi effectively handled all noise in the data that obscured biologically valid trajectories for other methods. We will improve the discussion of the robustness in the reviewed version. 

Second, the paper discusses the benefit of tviblindi operating in the original high dimensions of the data. This is perhaps adequate for mass cytometry data where there is less of an issue of dropouts and the proteins may be chosen to be large independent. But in the context of single-cell RNA-sequencing data, the massive undersampling of mRNA, as well as high degree of noise (e.g. ambient RNA), introduces very large degree of noise so that modeling data in the original high dimensions leads to methods being fit to the noise. Therefore ALL other methods for trajectory inference work in a lower dimension, for very good reason, otherwise one is learning noise rather than signal. It would be great to have a discussion on the feasibility of the method as is for such noisy data and provide users with guidance. We note that the example scRNA-seq data included in the paper is denoised using imputation, which will likely result in the trajectory inference being oversmoothed as well.

We agree with the reviewer. In our manuscript we wanted to showcase that tviblindi can directly operate in high-dimensional space (thousands of dimensions) and we used MAGIC imputation for this purpose. This was not ideal. More standard approach, which uses 30-50 PCs as input to the algorithm resulted in equivalent trajectories. We will add this analysis to the study.

In summary, the fact that tviblindi scales well with dimensionality of the data and is able to work in the original space does not mean that it is always the best option. We will emphasize in the revised paper that we aim to avoid the non-linear dimensional reduction techniques as a data preprocessing tool, as the effect of the reduction is difficult to predict. We will also discuss the preprocessing of scRNA-seq data in greater detail.

Reviewer #3 (Public Review):

Summary:

Stuchly et al. proposed a single-cell trajectory inference tool, tviblindi, which was built on a sequential implementation of the k-nearest neighbor graph, random walk, persistent homology and clustering, and interactive visualization. The paper was organized around the detailed illustration of the usage and interpretation of results through the human thymus system.

Strengths:

Overall, I found the paper and method to be practical and needed in the field. Especially the in-depth, step-by-step demonstration of the application of tviblindi in numerous T cell development trajectories and how to interpret and validate the findings can be a template for many basic science and disease-related studies. The videos are also very helpful in showcasing how the tool works.

Weaknesses:

I only have a few minor suggestions that hopefully can make the paper easier to follow and the advantage of the method to be more convincing.

(1) The "Computational method for the TI and interrogation - tviblindi" subsection under the Results is a little hard to follow without having a thorough understanding of the tviblindi algorithm procedures. I would suggest that the authors discuss the uniqueness and advantages of the tool after the detailed introduction of the method (moving it after the "Connectome - a fully automated pipeline".

We thank the reviewer for the suggestion and we will accommodate it to improve readability of the text.

Also, considering it is a computational tool paper, inevitably, readers are curious about how it functions compared to other popular trajectory inference approaches. I did not find any formal discussion until almost the end of the supplementary note (even that is not cited anywhere in the main text). Authors may consider improving the summary of the advantages of tviblindi by incorporating concrete quantitative comparisons with other trajectory tools.

We provide comparisons of tviblindi and vaevictis in the Supplementary Note, section 8.2, where we compare it to Monocle3 (v1.3.1) Cao et al. (2019), Stream (v1.1) Chen et al. (2019), Palantir (v1.0.0) Setty et al. (2019), VIA (v0.1.89) Stassen et al. (2021) and PAGA (scanpy==1.9.3) Wolf et al. (2019). We use two datasets: artificial Dyntoy and real mass cytometry thymus+peripheral blood dataset. We will also add CellRank2 into comparisons and we will strengthen the message of the benchmarking results in the Discussion section.

(2) Regarding the discussion in Figure 4 the trajectory goes through the apoptotic stage and reconnects back to the canonical trajectory with counterintuitive directionality, it can be a checkpoint as authors interpret using their expert knowledge, or maybe a false discovery of the tool. Maybe authors can consider running other algorithms on those cells and see which tracks they identify and if the directionality matches with the tviblindi.

We have indeed used the thymus dataset for comparison of all TI algorithms listed above. Except for Monocle 3 they failed to discover the negative selection branch (Monocle 3 does not offer directionality information). Therefore, a valid topological trajectory with incorrect (expert-corrected) directionality was partly or entirely missed by other algorithms.

(3) The paper mainly focused on mass cytometry data and had a brief discussion on scRNA-seq. Can the tool be applied to multimodality data such as CITE-seq data that have both protein markers and gene expression? Any suggestions if users want to adapt to scATAC-seq or other epigenomic data?

The analysis of multimodal data is the logical next step and is the topic of our current research. At this moment tviblindi cannot be applied directly to multimodal data. It is possible to use the KNN-graph based on multimodal data (such as weighted nearest neighbor graph implemented in Seurat) for pseudotime calculation and random walk simulation. However, we do not have a fully developed triangulation for the multimodal case yet.

eLife assessment

The authors present an algorithm and workflow for the inference of developmental trajectories from single-cell data, including a mathematical approach to increase computational efficiency. While such efforts are in principle useful, the absence of benchmarking against synthetic data and a wide range of different single-cell data sets make this study incomplete. Based on what is presented, one can neither ultimately judge if this will be an advance over previous work nor whether the approach will be of general applicability.

Reviewer #1 (Public Review):

Summary:

The authors present tviblindi, a computational workflow for trajectory inference from molecular data at single-cell resolution. The method is based on (i) pseudo-time inference via expecting hitting time, (ii) sampling of random walks in a directed acyclic k-NN where edges are oriented away from a cell of origin w.r.t. the involved nodes' expected hitting times, and (iii) clustering of the random walks via persistent homology. An extended use case on mass cytometry data shows that tviblindi can be used elucidate the biology of T cell development.

Strengths:

- Overall, the paper is very well written and most (but not all, see below) steps of the tviblindi algorithm are explained well.

- The T cell biology use case is convincing (at least to me: I'm not an immunologist, only a bioinformatician with a strong interest in immunology).

Weaknesses:

- The main weakness of the paper is that a systematic comparison of tviblindi against other tools for trajectory inference (there are many) is entirely missing. Even though I really like the algorithmic approach underlying tviblindi, I would therefore not recommend to our wet-lab collaborators that they should use tviblindi to analyze their data. The only validation in the manuscript is the T cell development use case. Although this use case is convincing, it does not suffice for showing that the algorithms's results are systematically trustworthy and more meaningful (at least in some dimension) than trajectories inferred with one of the many existing methods.

- The authors' explanation of the random walk clustering via persistent homology in the Results (subsection "Real-time topological interactive clustering") is not detailed enough, essentially only concept dropping. What does "sparse regions" mean here and what does it mean that "persistent homology" is used? The authors should try to better describe this step such that the reader has a chance to get an intuition how the random walk clustering actually works. This is especially important because the selection of sparse regions is done interactively. Therefore, it's crucial that the users understand how this selection affects the results. For this, the authors must manage to provide a better intuition of the maths behind clustering of random walks via persistent homology.

- To motivate their work, the authors write in the introduction that "TI methods often use multiple steps of dimensionality reduction and/or clustering, inadvertently introducing bias. The choice of hyperparameters also fixes the a priori resolution in a way that is difficult to predict." They claim that tviblindi is better than the original methods because "analysis is performed in the original high-dimensional space, avoiding artifacts of dimensionality reduction." However, in the manuscript, tviblindi is tested only on mass cytometry data which has a much lower dimensionality than scRNA-seq data for which most existing trajectory inference methods are designed. Since tviblindi works on a k-NN graph representation of the input data, it is unclear if it could be run on scRNA-seq data without prior dimensionality reduction. For this, cell-cell distances would have to be computed in the original high-dimensional space, which is problematic due to the very high dimensionality of scRNA-seq data. Of course, the authors could explicitly reduce the scope of tviblindi to data of lower dimensionality, but this would have to be stated explicitly.

- Also tviblindi has at least one hyper-parameter, the number k used to construct the k-NN graphs (there are probably more hidden in the algorithm's subroutines). I did not find a systematic evaluation of the effect of this hyper-parameter.

Reviewer #2 (Public Review):

Summary: In Deconstructing Complexity: A Computational Topology Approach to Trajectory Inference in the Human Thymus with tviblindi, Stuchly et al. propose a new trajectory inference algorithm called tviblindi and a visualization algorithm called vaevictis for single-cell data. The paper utilizes novel and exciting ideas from computational topology coupled with random walk simulations to align single cells onto a continuum. The authors validate the utility of their approach largely using simulated data and establish known protein expression dynamics along CD4/CD8 T cell development in thymus using mass cytometry data. The authors also apply their method to track Treg development in single-cell RNA-sequencing data of human thymus.

The technical crux of the method is as follows: The authors provide an interactive tool to align single cells along a continuum axis. The method uses expected hitting time (given a user input start cell) to obtain a pseudotime alignment of cells. The pseudotime gives an orientation/direction for each cell, which is then used to simulate random walks. The random walks are then arranged/clustered based on the sparse region in the data they navigate using persistent homology.

Strengths:<br /> The notion of using persistent homology to group random walks to identify trajectories in the data is novel.<br /> The strength of the method lies in the implementation details that make computationally demanding ideas such as persistent homology more tractable for large scale single-cell data. This enables the authors to make the method more user friendly and interactive allowing real-time user query with the data.

Weaknesses:<br /> The interactive nature of the tool is also a weakness, by allowing for user bias leading to possible overfitting for a specific data.

The main weakness of the method is lack of benchmarking the method on real data and comparison to other methods. Trajectory inference is a very crowded field with many highly successful and widely used algorithms, the two most relevant ones (closest to this manuscript) are not only not benchmarked against, but also not sited. Including those that specifically use persistent homology to discover trajectories (Rizvi et.al. published Nat Biotech 2017). Including those that specifically implement the idea of simulating random walks to identify stable states in single-cell data (e.g. CellRank published in Lange et.al Nat Meth 2022), as well as many trajectory algorithms that take alternative approaches. The paper has much less benchmarking, demonstration on real data and comparison to the very many other previous trajectory algorithms published before it. Generally speaking, in a crowded field of previously published trajectory methods, I do not think this one approach will compete well against prior work (especially due to its inability to handle the noise typical in real world data (as was even demonstrated in the little bit of application to real world data provided).

Beyond general lack of benchmarking there are two issues that give me particular concern. As previously mentioned, the algorithm is highly susceptible to user bias and overfitting. The paper gives the example (Figure 4) of a trajectory which mistakenly shows that cells may pass from an apoptotic phase to a different developmental stage. To circumvent this mistake, the authors propose the interactive version of tviblindi that allows users to zoom in (increase resolution) and identify that there are in fact two trajectories in one. In this case, the authors show how the author can fix a mistake when the answer is known. However, the point of trajectory inference is to discover the unknown. With so much interactive options for the user to guide the result, the method is more user/bias driven than data-driven. So a rigorous and quantitative discussion of robustness of the method, as well as how to ensure data-driven inference and avoid over-fitting would be useful.

Second, the paper discusses the benefit of tviblindi operating in the original high dimensions of the data. This is perhaps adequate for mass cytometry data where there is less of an issue of dropouts and the proteins may be chosen to be large independent. But in the context of single-cell RNA-sequencing data, the massive undersampling of mRNA, as well as high degree of noise (e.g. ambient RNA), introduces very large degree of noise so that modeling data in the original high dimensions leads to methods being fit to the noise. Therefore ALL other methods for trajectory inference work in a lower dimension, for very good reason, otherwise one is learning noise rather than signal. It would be great to have a discussion on the feasibility of the method as is for such noisy data and provide users with guidance. We note that the example scRNA-seq data included in the paper is denoised using imputation, which will likely result in the trajectory inference being oversmoothed as well.

Reviewer #3 (Public Review):

Summary:<br /> Stuchly et al. proposed a single-cell trajectory inference tool, tviblindi, which was built on a sequential implementation of the k-nearest neighbor graph, random walk, persistent homology and clustering, and interactive visualization. The paper was organized around the detailed illustration of the usage and interpretation of results through the human thymus system.

Strengths:<br /> Overall, I found the paper and method to be practical and needed in the field. Especially the in-depth, step-by-step demonstration of the application of tviblindi in numerous T cell development trajectories and how to interpret and validate the findings can be a template for many basic science and disease-related studies. The videos are also very helpful in showcasing how the tool works.

Weaknesses:<br /> I only have a few minor suggestions that hopefully can make the paper easier to follow and the advantage of the method to be more convincing.<br /> (1) The "Computational method for the TI and interrogation - tviblindi" subsection under the Results is a little hard to follow without having a thorough understanding of the tviblindi algorithm procedures. I would suggest that the authors discuss the uniqueness and advantages of the tool after the detailed introduction of the method (moving it after the "Connectome - a fully automated pipeline".<br /> Also, considering it is a computational tool paper, inevitably, readers are curious about how it functions compared to other popular trajectory inference approaches. I did not find any formal discussion until almost the end of the supplementary note (even that is not cited anywhere in the main text). Authors may consider improving the summary of the advantages of tviblindi by incorporating concrete quantitative comparisons with other trajectory tools.<br /> (2) Regarding the discussion in Figure 4 the trajectory goes through the apoptotic stage and reconnects back to the canonical trajectory with counterintuitive directionality, it can be a checkpoint as authors interpret using their expert knowledge, or maybe a false discovery of the tool. Maybe authors can consider running other algorithms on those cells and see which tracks they identify and if the directionality matches with the tviblindi.<br /> (3) The paper mainly focused on mass cytometry data and had a brief discussion on scRNA-seq. Can the tool be applied to multimodality data such as CITE-seq data that have both protein markers and gene expression? Any suggestions if users want to adapt to scATAC-seq or other epigenomic data?

Author response:

Reviewer #1 (Public Review):

Summary:

The manuscript focuses on the role of the deubiquitinating enzyme UPS-50/USP8 in endosome maturation. The authors aimed to clarify how this enzyme drives the conversion of early endosomes into late endosomes. Overall, they did achieve their aims in shedding light on the precise mechanisms by which UPS-50/USP8 regulates endosome maturation. The results support their conclusions that UPS-50 acts by disassociating RABX-5 from early endosomes to deactivate RAB-5 and by recruiting SAND-1/Mon1 to activate RAB-7. This work is commendable and will have a significant impact on the field. The methods and data presented here will be useful to the community in advancing our understanding of endosome maturation and identifying potential therapeutic targets for diseases related to endosomal dysfunction. It is worth noting that further investigation is required to fully understand the complexities of endosome maturation. However, the findings presented in this manuscript provide a solid foundation for future studies.

We thank this reviewer for the instructive suggestions and encouragement.

Strengths:

The major strengths of this work lie in the well-designed experiments used to examine the effects of UPS-50 loss. The authors employed confocal imaging to obtain a picture of the aftermath of the USP-50 loss. Their findings indicated enlarged early endosomes and MVB-like structures in cells deficient in USP-50/USP8.

We thank this reviewer for the instructive suggestions and encouragement.

Weaknesses:

Specifically, there is a need for further investigation to accurately characterize the anomalous structures detected in the ups-50 mutant. Also, the correlation between the presence of these abnormal structures and ESCRT-0 is yet to be addressed, and the current working model needs to be revised to prevent any confusion between enlarged early endosomes and MVBs.

Excellent suggestions. The EM imaging indeed revealed an increase in enlarged cellular vesicles containing various contents in usp-50 mutants. However, the detailed molecular features of these vesicles remain unclear. Therefore, we plan to utilize ESCRT components for double staining with early or late endosome markers. This will enable us to accurately characterize the anomalous structures detected in the usp-50 mutants.

Reviewer #2 (Public Review):

Summary:

In this study, the authors study how the deubiquitinase USP8 regulates endosome maturation in C. elegans and mammalian cells. The authors have isolated USP8 mutant alleles in C. elegans and used multiple in vivo reporter lines to demonstrate the impact of USP8 loss-of-function on endosome morphology and maturation. They show that in USP8 mutant cells, the early endosomes and MVB-like structures are enlarged while the late endosomes and lysosomal compartments are reduced. They elucidate that USP8 interacts with Rabx5, a guanine nucleotide exchange factor (GEF) for Rab5, and show that USP8 likely targets specific lysine residue of Rabx5 to dissociate it from early endosomes. They also find that the localization of USP8 to early endosomes is disrupted in Rabx5 mutant cells. They observe that in both Rabx5 and USP8 mutant cells, the Rab7 GEF SAND-1 puncta which likely represents late endosomes are diminished, although Rabex5 is accumulated in USP8 mutant cells. The authors provide evidence that USP8 regulates endosomal maturation in a similar fashion in mammalian cells. Based on their observations they propose that USP8 dissociates Rabex5 from early endosomes and enhances the recruitment of SAND-1 to promote endosome maturation.

We thank this reviewer for the instructive suggestions and encouragement.

Strengths:

The major highlights of this study include the direct visualization of endosome dynamics in a living multi-cellular organism, C. elegans. The high-quality images provide clear in vivo evidence to support the main conclusions. The authors have generated valuable resources to study mechanisms involved in endosome dynamics regulation in both the worm and mammalian cells, which would benefit many members of the cell biology community. The work identifies a fascinating link between USP8 and the Rab5 guanine nucleotide exchange factor Rabx5, which expands the targets and modes of action of USP8. The findings make a solid contribution toward the understanding of how endosomal trafficking is controlled.

We thank this reviewer for the instructive suggestions and encouragement.

Weaknesses:

-The authors utilized multiple fluorescent protein reporters, including those generated by themselves, to label endosomal vesicles. Although these are routine and powerful tools for studying endosomal trafficking, these results cannot tell whether the endogenous proteins (Rab5, Rabex5, Rab7, etc.) are affected in the same fashion.

Good suggestion. Indeed, to test whether the endogenous proteins (Rab5, Rabex5, Rab7, etc.) are affected in the same fashion as fluorescent protein reporters, we supplemented our approach with the utilization of endogenous markers. These markers, including Rab5, RAB-5, Rabex5, RABX-5, and EEA1 for early endosomes, as well as RAB-7, Mon1a, and Mon1b for late endosomes, were instrumental in our investigations (refer to Figure 3, Figure 6, Sup Figure 4, Sup Figure 5, and Sup Figure 7). Our comprehensive analysis, employing various methodologies such as tissue-specific fused proteins, CRISPR/Cas9 knock-in, and antibody staining, consistently highlights the critical role of USP8 in early-to-late endosome conversion.

-The authors clearly demonstrated a link between USP8 and Rabx5, and they showed that cells deficient in both factors displayed similar defects in late endosomes/lysosomes. However, the authors didn't confirm whether and/or to which extent USP8 regulates endosome maturation through Rabx5. Additional genetic and molecular evidence might be required to better support their working model.

Excellent point. We plan to conduct additional genetic analyses, including the construction of double mutants between usp-50 and various rabex-5 mutations, to further elucidate the extent to which USP8 regulates endosome maturation via Rabex5.

Reviewer #3 (Public Review):

Summary:

The authors were trying to elucidate the role of USP8 in the endocytic pathway. Using C. elegans epithelial cells as a model, they observed that when USP8 function is lost, the cells have a decreased number and size in lysosomes. Since USP8 was already known to be a protein linked to ESCRT components, they looked into what role USP8 might play in connecting lysosomes and multivesicular bodies (MVB). They observed fewer ESCRT-associated vesicles but an increased number of "abnormal" enlarged vesicles when USP8 function was lost. At this specific point, it's not clear what the objective of the authors was. What would have been their hypothesis addressing whether the reduced lysosomal structures in USP8 (-) animals were linked to MVB formation? Then they observed that the abnormally enlarged vesicles, marked by the PI3P biosensor YFP-2xFYVE, are bigger but in the same number in USP8 (-) compared to wild-type animals, suggesting homotypic fusion. They confirmed this result by knocking down USP8 in a human cell line, and they observed enlarged vesicles marked by YFP-2xFYVE as well. At this point, there is quite an important issue. The use of YFP-2xFYVE to detect early endosomes requires the transfection of the cells, which has already been demonstrated to produce differences in the distribution, number, and size of PI3P-positive vesicles (doi.org/10.1080/15548627.2017.1341465). The enlarged vesicles marked by YFP-2xFYVE would not necessarily be due to the loss of UPS8. In any case, it appears relatively clear that USP8 localizes to early endosomes, and the authors claim that this localization is mediated by Rabex-5 (or Rabx-5). They finally propose that USP8 dissociates Rabx-5 from early endosomes facilitating endosome maturation.

Weaknesses:

The weaknesses of this study are, on one side, that the results are almost exclusively dependent on the overexpression of fusion proteins. While useful in the field, this strategy does not represent the optimal way to dissect a cell biology issue. On the other side, the way the authors construct the rationale for each approximation is somehow difficult to follow. Finally, the use of two models, C. elegans and a mammalian cell line, which would strengthen the observations, contributes to the difficulty in reading the manuscript.

The findings are useful but do not clearly support the idea that USP8 mediates Rab5-Rab7 exchange and endosome maturation, In contrast, they appear to be incomplete and open new questions regarding the complexity of this process and the precise role of USP8 within it.

We thank this reviewer for the insightful comments. Fluorescence-fused proteins serve as potent tools for visualizing subcellular organelles both in vivo and in live settings. Specifically, in epidermal cells of worms, the tissue-specific expression of these fused proteins is indispensable for studying organelle dynamics within living organisms. This approach is necessitated by the inherent limitations of endogenously tagged proteins, whose fluorescence signals are often weak and unsuitable for live imaging or genetic screening purposes. Acknowledging concerns raised by the reviewer regarding potential alterations in organelle morphology due to overexpression of certain fused proteins, we supplemented our approach with the utilization of endogenous markers. These markers, including Rab5, RAB-5, Rabex5, RABX-5, and EEA1 for early endosomes, as well as RAB-7, Mon1a, and Mon1b for late endosomes, were instrumental in our investigations (refer to Figure 3, Figure 6, Sup Figure 4, Sup Figure 5, and Sup Figure 7). Our comprehensive analysis, employing various methodologies such as tissue-specific fused proteins, CRISPR/Cas9 knock-in, and antibody staining, consistently highlights the critical role of USP8 in early-to-late endosome conversion. Specifically, we discovered that the recruitment of USP-50/USP8 to early endosomes is depending on Rabex5. However, instead of stabilizing Rabex5, the recruitment of USP-50/USP8 leads to its dissociation from endosomes, concomitantly facilitating the recruitment of the Rab7 GEF SAND-1/Mon1. In cells with loss-of-function mutations in usp-50/usp8, we observed enhanced RABX-5/Rabex5 signaling and mis-localization of SAND-1/Mon1 proteins from endosomes. Consequently, this disruption impairs endolysosomal trafficking, resulting in the accumulation of enlarged vesicles containing various intraluminal contents and rudimentary lysosomal structures.

Through an unbiased genetic screen, verified by cultured mammalian cell studies, we observed that loss-of-function mutations in usp-50/usp8 result in diminished lysosome/late endosomes. To elucidate the underlying mechanisms, we investigated the formation of multivesicular bodies (MVBs), a process tightly linked to USP8 function. Extensive electron microscopy (EM) analysis indicated that MVB-like structures are largely intact in usp-50 mutant cells, suggesting that USP8/USP-50 likely regulate lysosome formation through alternative pathways in addition to their roles in MVB formation and ESCRT component function. USP8 is known to regulate the endocytic trafficking and stability of numerous transmembrane proteins. Interestingly, loss-of-function mutations in usp8 often lead to the enlargement of early endosomes, yet the mechanisms underlying this phenomenon remain unclear. Given that lysosomes receive and degrade materials generated by endocytic pathways, we hypothesized that the abnormally enlarged MVB-like vesicular structures observed in usp-50 or usp8 mutant cells correspond to the enlarged vesicles coated by early endosome markers. Indeed, in the absence of usp8/usp-50, the endosomal Rab5 signal is enhanced, while early endosomes are significantly enlarged. Given that Rab5 guanine nucleotide exchange factor (GEF), Rabex5, is essential for Rab5 activation, we further investigated its dynamics. Additional analyses conducted in both worm hypodermal cells and cultured mammalian cells revealed an increase of endosomal Rabex5 in response to usp8/usp-50 loss-of-function. Live imaging studies further demonstrated active recruitment of USP8 to newly formed Rab5-positive vesicles, aligning spatiotemporally with Rabex5 regulation. Through systematic exploration of putative USP-50 binding partners on early endosomes, we identified its interaction with Rabex5. Comprehensive genetics and biochemistry experiments demonstrated that USP8 acts through K323 site de-ubiquitination to dissociate Rabex5 from early endosomes and promotes the recruitment of the Rab7 GEF SAND-1/Mon1. In summary, our study began with an unbiased genetic screen and subsequent examination of established theories, leading to the formulation of our own hypothesis. Through multifaceted approaches, we unveiled a novel function of USP8 in early-to-late endosome conversion.

Reviewer #2 (Public Review):

Summary:

This manuscript reports interesting findings about the navigational behavior of mice. The authors have dissected this behavior in various components using a sophisticated behavioral maze and statistical analysis of the data. ​

Strengths:

The results are solid and they support the main conclusions, which will be of considerable value to many scientists.

Weaknesses:

Figure 1: In some trials the mice seem to be doing thigmotaxis, walking along the perimeter of the maze. This is perhaps due to the fear of the open arena. But, these paths along the perimeter would significantly influence all metrics of navigation, e.g. the distance or time to reward. Perhaps analysis can be done that treats such behavior separately and the factors it out from the paths that are away from the perimeter. 

Figure 1c: the color axis seems unusual. Red colors indicate less frequently visited regions (less than 25%) and white corresponds to more frequently visited places (>25%)? Why use such a binary measure instead of a graded map as commonly done?

Some figures use linear scale and others use logarithmic scale. Is there a scientific justification? For example, average latency is on a log scale and average speed is on a linear scale, but both quantify the same behavior. The y-axis in panel 1-I is much wider than the data. Is there a reason for this? Or can the authors zoom into the y-axis so that the reader can discern any pattern?<br /> <br /> 1F shows no significant reduction in distance to reward. Does that mean there is no improvement with experience and all the improvement in the latency is due to increasing running speed with experience?

Figure 3: The distance traveled was reduced by nearly 10-fold and speed increased by by about 3fold. So, the time to reach the reward should decrease by only 3 fold (t=d/v) but that too reduced by 10fold. How does one reconcile the 3fold difference between the expected and observed values? 

Figure 4: The reader is confused about the use of a binary color scheme here for the checking behavior: gray for a large amount of checking, and pink for small. But, there is a large ellipse that is gray and there are smaller circles that are also gray, but these two gray areas mean very different things as far as the reader can tell. Is that so? Why not show the entire graded colormap of checking probability instead of such a seemingly arbitrary binary depiction? 

Figure 4C: What would explain the large amount of checking behavior at the perimeter? Does that occur predominantly during thigmotaxis? 

Was there a correlation between the amount of time spent by the animals in a part of the maze and the amount of reward checking? Previous studies have shown that the two behaviors are often positively correlated, e.g. reference 20 in the manuscript.  How does this fit with the path integration hypothesis? 

"Scratches and odor trails were eliminated by washing and rotating the maze floor between trials." Can one eliminate scratches by just washing the maze floor? Rotation of the maze floor between trials can make these cues unreliable or variable but will not eliminate them. Ditto for odor cues.

"Possible odor gradient cues were eliminated by experiments where such gradients were prevented with vacuum fans (Fig. S6E)" What tests were done to ensure that these were *eliminated* versus just diminished? 

"Probe trials of fully trained mice resulted in trajectories and initial hole checking identical to that of regular trials thereby demonstrating that local odor cues are not essential for spatial learning." As far as the reader can tell, probe trials only eliminated the food odor cues but did not eliminate all other odors. If so, this conclusion can be modified accordingly. <br /> The interpretation of direction selectivity is a bit tricky. At different places in this manuscript, this is interpreted as a path integration signal that encodes goal location, including the Consync cells. However, studies show that (e.g. Acharya et al. 2016) direction selectivity in virtual reality is comparable to that during natural mazes, despite large differences in vestibular cues and spatial selectivity. How would one reconcile these observations with path integration interpretation? 

The manuscript would be improved if the speculations about place cells, grid cells, BTSP, etc. were pared down. I could easily imagine the outcome of these speculations to go the other way and some claims are not supported by data. "We note that the cited experiments were done with virtual movement constrained to 1D and in the presence of landmarks. It remains to be shown whether similar results are obtained in our unconstrained 2D maze and with only self-motion cues available." There are many studies that have measured the evolution of place cells in non-virtual mazes, look up papers from the 1990s. Reference 43 reports such results in a 2D virtual maze.

eLife assessment

This important work presents a creative and thoughtful analysis of mouse foraging behavior and its dependence on body reference frame-based vs world reference frame-based cues. It convincingly demonstrates that a robust map capable of supporting taking novel shortcuts is learned based primarily on self-motion cues from a known starting location and this can be done in contexts where there is little reliance on distal visual landmarks; this may be a unique finding outside of the human literature. The discussion is rich with ideas about the role of the hippocampus in supporting the behavior that should be interesting to test in future analyses of brain recordings as mice perform the tasks considered by the study.

Reviewer #1 (Public Review):

Assessment:

This important work advances our understanding of navigation and path integration in mammals by using a clever behavioral paradigm. The paper provides compelling evidence that mice are able to create and use a cognitive map to find "short cuts" in an environment, using only the location of rewards relative to the point of entry to the environment and path integration, and need not rely on visual landmarks.

Summary:

The authors have designed a novel experimental apparatus called the 'Hidden Food Maze (HFM)' and a beautiful suite of behavioral experiments using this apparatus to investigate the interplay between allothetic and idiothetic cues in navigation. The results presented provide a clear demonstration of the central claim of the paper, namely that mice only need a fixed start location and path integration to develop a cognitive map. The experiments and analyses conducted to test the main claim of the paper -- that the animals have formed a cognitive map -- are conclusive. While I think the results are quite interesting and sound, one issue that needs to be addressed is the framing of how landmarks are used (or not), as discussed below, although I believe this will be a straightforward issue for the authors to address.

Strengths:

The 90-degree rotationally symmetric design and use of 4 distal landmarks and 4 quadrants with their corresponding rotationally equivalent locations (REL) lends itself to teasing apart the influence of path integration and landmark-based navigation in a clever way. The authors use a really complete set of experiments and associated controls to show that mice can use a start location and path integration to develop a cognitive map and generate shortcut routes to new locations.

Weaknesses:

I have two comments. The second comment is perhaps major and would require rephrasing multiple sentences/paragraphs throughout the paper.

(1) The data clearly indicate that in the hidden food maze (HFM) task mice did not use external visual "cue cards" to navigate, as this is clearly shown in the errors mice make when they start trials from a different start location when trained in the static entrance condition. The absence of visual landmark-guided behavior is indeed surprising, given the previous literature showing the use of distal landmarks to navigate and neural correlates of visual landmarks in hippocampal formation. While the authors briefly mention that the mice might not be using distal landmarks because of their pretraining procedure - I think it is worth highlighting this point (about the importance of landmark stability and citing relevant papers) and elaborating on it in greater detail. It is very likely that mice do not use the distal visual landmarks in this task because the pretraining of animals leads to them not identifying them as stable landmarks. For example, if they thought that each time they were introduced to the arena, it was "through the same door", then the landmarks would appear to be in arbitrary locations compared to the last time. In the same way, we as humans wouldn't use clouds or the location of people or other animate objects as trusted navigational beacons. In addition, the animals are introduced to the environment without any extra-maze landmarks that could help them resolve this ambiguity. Previous work (and what we see in our dome experiments) has shown that in environments with 'unreliable' landmarks, place cells are not controlled by landmarks - https://www.sciencedirect.com/science/article/pii/S0028390898000537, https://pubmed.ncbi.nlm.nih.gov/7891125/. This makes it likely that the absence of these distal visual landmarks when the animal first entered the maze ensured that the animal does not 'trust' these visual features as landmarks.

(2) I don't agree with the statement that 'Exogenous cues are not required for learning the food location'. There are many cues that the animal is likely using to help reduce errors in path integration. For example, the start location of the rat could act as a landmark/exogenous cue in the sense of partially correcting path integration errors. The maze has four identical entrances (90-degree rotationally symmetric). Despite this, it is entirely plausible that the animal can correct path integration errors by identifying the correct start entrance for a given trial, and indeed the distance/bearing to the others would also help triangulate one's location. Further, the overall arena geometry could help reduce PI error. For example, with a food source learned to be "near the middle" of the arena, the animal would surely not estimate the position to be near the far wall (and an interesting follow-on experiment would be to have two different-sized, but otherwise nearly identical arenas). As the rat travels away from the start location, small path integration errors are bound to accumulate, these errors could be at least partially corrected based on entrance and distal wall locations. If this process of periodically checking the location of the entrance to correct path integration errors is done every few seconds, path integration would be aided 'exogenously' to build a cognitive map. While the original claim of the paper still stands, i.e. mice can learn the location of a hidden food size when their starting point in the environment remains constant across trials. I would advise rewording portions of the paper, including the discussion throughout the paper that states claims such as "Exogenous cues are not required for learning the food location" to account for the possibility that the start and the overall arena geometry could be used as helpful exogenous cues to correct for path integration errors.

Reviewer #3 (Public Review):

Summary:

How is it that animals find learned food locations in their daily life? Do they use landmarks to home in on these learned locations or do they learn a path based on self-motion (turn left, take ten steps forward, turn right, etc.). This study carefully examines this question in a well-designed behavioral apparatus. A key finding is that to support the observed behavior in the hidden food arena, mice appear to not use the distal cues that are present in the environment for performing this task. Removal of such cues did not change the learning rate, for example. In a clever analysis of whether the resulting cognitive map based on self-motion cues could allow a mouse to take a shortcut, it was found that indeed they are. The work nicely shows the evolution of the rodent's learning of the task, and the role of active sensing in the targeted reduction of uncertainty of food location proximal to its expected location.

Strengths:

A convincing demonstration that mice can synthesize a cognitive map for the finding of a static reward using body frame-based cues. This shows that the uncertainty of the final target location is resolved by an active sensing process of probing holes proximal to the expected location. Showing that changing the position of entry into the arena rotates the anticipated location of the reward in a manner consistent with failure to use distal cues.

Weaknesses:

The task is low stakes, and thus the failure to use distal cues at most costs the animal a delay in finding the food; this delay is likely unimportant to the animal. Thus, it is unclear whether this result would generalize to a situation where the animal may be under some time pressure, urgency due to food (or water) restriction, or due to predatory threat. In such cases, the use of distal cues to make locating the reward robust to changing start locations may be more likely to be observed.

Author response:

We would like to thank all the reviewers and editors for their thoughtful and detailed comments, critiques and suggestions. We will revise our manuscript in accordance with all the points raised by the reviewers. Here we summarize some of the main points that we intend to address in our revised manuscript.

The reviewers noted that we were not sufficiently careful in identifying possible exogenous cues that the mice might be using to locate the cues and that we did not consider why such cues might be ineffective. As the reviewers point out, the mice may be ignoring the visual landmarks (and floor scratches) because they are not reliable cues and their relation to the food varies with the entrance the mice have used. In particular, a reviewer refers to papers that show that “in environments with 'unreliable' landmarks, place cells are not controlled by landmarks”. These papers were known to the authors but failed to make final cut of our extensive discussion. This important point will be thoroughly addressed.

Another critical point was the mice were often doing thigmotaxis. The literature on thigmotaxis was known to us and we will now directly refer to this point. We do note that the final average start to food trajectory (TEV) is directly to the food. In other words, the thigmotaxic trajectories and “towards the center” trajectories effectively average out.

There was a very cogent point about the difficulty of totally eliminating odor cues that we will now address. Finally, based on studies using a virtual reality environment, one reviewer questioned the use of “path integration” as a signal that encodes goal location. The relevance of path integration to spatial learning and performance is a very difficult issue that, to our knowledge, has never been entirely settled in the vast spatial learning literature. We do not think that our data can “settle’ this issue but will try to at least be explicit re the complexity of the path integration hypothesis as it applies to both our own data and the virtual reality literature. In particular, we will discuss the potential roles of optic flow versus proprioceptive and vestibular inputs to a putative path integration mechanism.

Finally, the reviewers raised many important technical points re statistics reporting and how the figures are presented. In our revision, we will completely comply with all these helpful critiques.

Author response:

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

eLife assessment

Chang et al. provide glutamate co-expression profiles in the central noradrenergic system and test the requirement of Vglut2-based glutamatergic release in respiratory and metabolic activity under physiologically relevant gas challenges. Their experiments provide compelling evidence that conditional deletion of Vglut2 in noradrenergic neurons does not impact steadystate breathing or metabolic activity in room air, hypercapnia, or hypoxia. This study provides an important contribution to our understanding of how noradrenergic neurons regulate respiratory homeostasis in conscious adult mice.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Chang et al. provide glutamate co-expression profiles in the central noradrenergic system and test the requirement of Vglut2-based glutamatergic release in respiratory and metabolic activity under physiologically relevant gas challenges. Their experiments show that conditional deletion of Vglut2 in NA neurons does not impact steady-state breathing or metabolic activity in room air, hypercapnia, or hypoxia. Their observations challenge the importance of glutamatergic signaling from Vglut2 expressing NA neurons in normal respiratory homeostasis in conscious adult mice.

Strengths:

The comprehensive Vglut1, Vglut2, and Vglut3 co-expression profiles in the central noradrenergic system and the combined measurements of breathing and oxygen consumption are two major strengths of this study. Observations from these experiments provide previously undescribed insights into (1) expression patterns for subtypes of the vesicular glutamate transporter protein in the noradrenergic system and (2) the dispensable nature of Vglut2-dependent glutamate signaling from noradrenergic neurons to breathing responses to physiologically relevant gas challenges in adult conscious mice.

Weaknesses:

Although the cellular expression profiles for the vesicular glutamate transporters are provided, the study fails to document that glutamatergic-based signaling originating from noradrenergic neurons is evident at the cellular level under normal, hypoxic, and/or hypercapnic conditions. This limits the reader's understanding of why conditional Vglut2 knockdown is dispensable for breathing under the conditions tested.

We thank the reviewers for their positive evaluation of our work. First, we would like to highlight that multiple studies have provided anatomical evidence of innervation of multiple cardio-respiratory nuclei by Vglut2+ noradrenergic fibers. Thus, the anatomical substrates are present for noradrenergic based Vglut2 signaling to either play a direct role in breathing control or, upon perturbation, to indirectly affect breathing through disrupted metabolic or cardiovascular control. We have included supplemental table 1 that summarizes central noradrenergic Vglut2+ innervations of respiratory and autonomic nuclei. Additionally, Ultrastructural evidence shows asymmetric synaptic contacts assuming glutamatergic transmission between C1 neurons and LC, A1, A2 and the dorsal motor nucleus of the vagus (DMV) (Milner et al., 1989; Abbott et al., 2012; Holloway et al., 2013; DePuy et al., 2013).

Functionally, electrophysiological evidence showed that photostimulating C1 neurons activate LC, A1, A2 noradrenergic neurons monosynaptically by releasing glutamate (Holloway et al., 2013; DePuy et al., 2013) and optogenetic stimulation of LC neurons excite the downstream parabrachial nucleus (PBN) neurons by releasing glutamate. Thus, at least the glutamatergic signaling from C1 and LC noradrenergic neurons (two noradrenergic nuclei that have been shown to play a role in breathing control) is evident at the cellular level under normal conditions. Other evidence, highlighted in our manuscript, is more circumstantial.

Reviewer #2 (Public Review):

The authors characterized the recombinase-based cumulative fate maps for vesicular glutamate transporters (Vglut1, Vglut2 and Vglut3) expression and compared those maps to their real-time expression profiles in central NA neurons by RNA in situ hybridization in adult mice. Authors have revealed a new and intriguing expression pattern for Vglut2, along with an entirely uncharted co-expression domain for Vglut3 within central noradrenergic neurons. Interestingly, and in contrast to previous studies, the authors demonstrated that glutamatergic signaling in central noradrenergic neurons does not exert any influence on breathing and metabolic control either under normoxic/normocapnic conditions or after chemoreflex stimulation. Also, they showed for the first-time the Vglut3-expressing NA population in C2/A2 nuclei. In addition, they were also able to demonstrate Vglut2 expression in anterior NA populations, such as LC neurons, by using more refined techniques, unlike previous studies.

A major strength of the study is the use of a set of techniques to investigate the participation of NA-based glutamatergic signaling in breathing and metabolic control. The authors provided a full characterization of the recombinase-based cumulative fate maps for Vglut transporters. They performed real-time mRNA expression of Vglut transporters in central NA neurons of adult mice. Further, they evaluated the effect of knocking down Vglut2 expression in NA neurons using a DBH-Cre; Vglut2cKO mice on breathing and control in unanesthetized mice. Finally, they injected the AAV virus containing Cre-dependent Td tomato into LC of v-Glut2 Cre mice to verify the VGlut2 expression in LC-NA neurons. A very positive aspect of the article is that the authors combined ventilation with metabolic measurements. This integration holds particular significance, especially when delving into the exploration of respiratory chemosensitivity. Furthermore, the sample size of the experiments is excellent.

Despite the clear strengths of the paper, some weaknesses exist. It is not clear in the manuscript if the experiments were performed in males and females and if the data were combined. I believe that the study would have benefited from a more comprehensive analysis exploring the sex specific differences. The reason I think this is particularly relevant is the developmental disorders mentioned by the authors, such as SIDS and Rett syndrome, which could potentially arise from disruptions in central noradrenergic (NA) function, exhibit varying degrees of sex predominance. Moreover, some of the noradrenergic cell groups are sexually dimorphic. For instance, female Wistar rats exhibit a larger LC size and more LC-NA neurons than male subjects (Pinos et al., 2001; Garcia-Falgueras et al., 2005). More recently, a detailed transcriptional profiling investigation has unveiled the identities of over 3,000 genes in the LC. This revelation has highlighted significant sexual dimorphisms, with more than 100 genes exhibiting differential expression within LC-NA neurons at the transcript level. Furthermore, this investigation has convincingly showcased that these distinct gene expression patterns have the capacity to elicit disparate behavioral responses between sexes (Mulvey et al., 2018). Therefore, the authors should compare the fate maps, Vglut transporters in males and females, at least considering LC-NA neurons. Even in the absence of identified sex differences, this information retains significant importance.

All experiments contained both males and females as described in the original submission. In our analysis of breathing and metabolism, sex was included in the analysis and no significant phenotypic difference was observed. For the fate map and in situ experiments, we did not see obvious differences in the expression patterns in the three glutamate transporters between females and males, though the group size is small. Though all the anatomical and phenotypic data in this manuscript are presented as combined graphs, we have differentially labeled our data points by sex. The reviewer does raise important questions regarding possible sexual dimorphisms in the central noradrenergic system and whether such dimorphisms may extend to glutamate transporter co-expression. Our thorough interrogation of respiratory-metabolic parameters fails to reveal any sex specific differences in control or experimental mice. Thus, it is unclear if any of the previously described and cited dimorphisms are functionally relevant in this setting. Given the large differences in the real time expression and cumulative fate maps of Vglut2, a worthwhile interrogation of differential glutamate transporter expression would be best served by longitudinal studies with large group sizes across age as it is not clear what underlies the dynamic VGlut2 expression changes. Such changes may at times be greater in males and other times in females, driven by experience or physiological challenges etc., but resulting in averaged cumulative fatemaps that are similar between sexes. Such a longitudinal quantitative study of real-time and fatemapped cell populations across the central NA system would be of a scale that is beyond the scope of this report, especially when no phenotypic changes have been observed in our respiratory data.

An important point well raised by the authors is that although suggestive, these experiments do not definitively rule out that NA-Vglut2 based glutamatergic signaling has a role in breathing control. Subsequent experiments will be necessary to validate this hypothesis.

As noted, we discuss that we only address requirement, not sufficiency, of NA Vglut2 in breathing. Functional sufficiency experiments usually involve increasing the relevant output. However, these experiments can lead to non-specific, pleiotropic effects that would be difficult to disambiguate, even if done with high cellular specificity. Viral or genetic overexpression of Vglut2 in NA neurons may be a feasible approach. Conditional ablation of TH or DBH with concurrent chemo or optogenetic stimulation may also be informative. These approaches would require significant investments in mouse model generation and suffer additional experimental limitations.

An improvement could be made in terms of measuring body temperature. Opting for implanted sensors over rectal probes would circumvent the need to open the chamber, thereby preventing alterations in gas composition during respiratory measurements. Further, what happens to body temperature phenotype in these animals under different gas exposures? These data should be included in the Tables.

While surgical implantation of sensors would provide a more direct assessment of temperature, it requires components that were not available at the time of the study and addresses a question (temperature changes during a time course of gas exposure) that go beyond the scope of the current work focused on respiratory response. As we have done for prior experiments (Martinez et al., 2019; Ray et al., 2011), the body temperature was measured immediately before and after measuring breathing only. Our flow through system using inline gas sensors (AEI P-61B CO2 sensor and AEI N-22M O2 sensor) ensure that gas challenges were constant and consistent across all measurements. Any disruption in gas composition would have been noted by our software analysis system, Breathe Easy, and the data rejected. We did not observe any such perturbations.

Is it plausible that another neurotransmitter within NA neurons might be released in higher amounts in DBH-Cre; Vglut2 cKO mice to compensate for the deficiency in glutamate and prevent changes in ventilation?

We agree that compensation is always a possibility at the synaptic, cellular, and circuit levels that may involve a variety of transcriptional, translational, cellular, and circuit mechanisms (i.e., synaptic strength). This could be interrogated by combining multiple conditional alleles and recombinase drivers for various transmitters and receptors, but would, in our experience, take multiple years for the requisite breeding to be completed.

Continuing along the same line of inquiry is there a possibility that Vglut2 cKO from NA neurons not only eliminates glutamate release but also reduces NA release? A similar mechanism was previously found in VGLUT2 cKO from DA neurons in previous studies (Alsio et al., 2011; Fortin et al., 2012; Hnasko et al., 2010). Additionally, does glutamate play a role in the vesicular loading of NA? Therefore, could the lack of effect on breathing be explained by the lack of noradrenaline and not glutamate?

These are all excellent points, but prior studies suggest that reductions in NA signaling would itself have an apparent effect (Zanella et al., 2006; Kuo et al., 2016). Although several studies showed that LC and C1 NA neurons co-release noradrenaline and glutamate, no direct evidence yet makes clear that glutamate facilitates NA release or vice versa. However, it would be of great interest to test if reduced or lack of NA compensated for loss of glutamate in the future. We do fully acknowledge that compensation in the manuscript that any number of compensatory events could be at play in these findings.

Reviewer #3 (Public Review):

Summary:

The authors, Y Chang and colleagues, have performed elegant studies in transgenic mouse models that were designed to examine glutamatergic transmission in noradrenergic neurons, with a focus on respiratory regulation. They generated 3 different transgenic lines, in which a red fluorophore was expressed in dopamine-B-hydroxylase (DBH; noradrenergic and adrenergic neurons) neurons that did not express a vesicular glutamate transporter (Vglut) and a green fluorophore in DBH neurons that did express one of either Vglut1, Vglut2 or Vglut3.

Further experiments generated a transgenic mouse with knockout of Vglut2 in DBH neurons. The authors used plethysmography to measure respiratory parameters in conscious, unrestrained mice in response to various challenges.

Strengths:

The distribution of the Vglut expression is broadly in agreement with other studies, but with the addition of some novel Vglut3 expression. Validation of the transgenic results, using in situ hybridization histochemistry to examine mRNA expression, revealed potential modulation of Vglut2 expression during phases of development. This dataset is comprehensive, wellpresented and very useful.

In the physiological studies the authors observed that neither baseline respiratory parameters, nor respiratory responses to hypercapnea (5, 7, 10% CO2) or hypoxia (10% O2) were different between knockout mice and littermate controls. The studies are well-designed and comprehensive. They provide observations that are supportive of previous reports using similar methodology.

Weaknesses:

In relation to the expression of Vglut2, the authors conclude that modulation of expression occurs, such that in adulthood there are differences in expression patterns in some (nor)adrenergic cell groups. Altered sensitivity is provided as an explanation for different results between studies examining mRNA expression. These are likely explanations; however, the conclusion would really be definitive with inclusion of a conditional cre expressing mouse. Given the effort taken to generate this dataset, it seems to me that taking that extra step would be of value for the overall understanding of glutamatergic expression in these catecholaminergic neurons

The seemingly dynamic Vglut2 expression pattern across the NA system is intriguing. As noted in our comments to reviewer 2, a robust age dependent interrogation would require a large magnitude study. The reviewer correctly points out that a temporally controlled recombinase fate mapping experiment would offer greater insight into the dynamic expression of Vglut2. We strongly agree with that idea and did work to develop a Vglut2-CreER targeted allele that, despite our many other successes in mouse genetic engineering (Lusk et al., 2022; Sun and Ray, 2016), did not succeed on the first attempt. We aim to complete the line in the near future so that we may better understand the Vglut2 expression pattern in central noradrenergic neurons in a time-specific manner and sex specific manner.

The respiratory physiology is very convincing and provides clear support for the view that Vglut2 is not required for modulation of the respiratory parameters measured and the reflex responses tested. It is stated that this is surprising. However, comparison with the data from Abbott et al., Eur J Neurosci (2014) in which the same transgenic approach was used, shows that they also observed no change in baseline breathing frequency. Differences were observed with strong, coordinated optogenetic stimulation, but, as discussed in this manuscript, it is not clear what physiological function this is relevant to. It just shows that some C1 neurons can use glutamate as a signaling molecule. Further, Holloway et al., Eur J Neurosci (2015), using the same transgenic mouse approach, showed that the respiratory response to optogenetic activation of Phox2 expressing neurons is not altered in DBH-Vglut2 KO mice. The conclusion seems to be that some C1 neuron effects are reliant upon glutamatergic transmission (C1DMV for example), and some not.

We agree that activation of C1 neurons may be sufficient to modulate breathing when artificially stimulated and that such stimulation relies on glutamatergic transmission for its effect. This is why we find our results surprising and important in clarifying for the field that glutamatergic signaling in noradrenergic cells is dispensable for breathing and hypoxic and hypercapnic responses under physiological conditions.

Further contrast is made in this manuscript to the work of Malheiros-Lima and colleagues (eLife 2020) who showed that the activation of abdominal expiratory nerve activity in response to peripheral chemoreceptor activation with cyanide was dependent upon C1 neurons and could be attenuated by blockade of glutamate receptors in the pFRG - i.e. the supposition that glutamate release from C1 neurons was responsible for the function. However, it is interesting to observe that diaphragm EMG responses to hypercapnia (10% CO2) or cyanide, and the expiratory activation to hypercapnia, were not affected by the glutamate receptor blockade. Thus, a very specific response is affected and one that was not measured in the current study.

As we mention above, we do not dispute that glutamate signaling can be manipulated to create a response in non-physiological conditions – we suggest that framing the interpretation around the glutamatergic role in a model that better matches physiological conditions should inform our interpretation. Furthermore, we do include an examination of expiratory flow – which was not impacted by loss of glutamatergic activity in NA neurons – which would be likely to have been impacted if abdominal expiratory nerve activity was modified.

These previous published observations are consistent with the current study which provides a more comprehensive analysis of the role of glutamatergic contributions respiratory physiology. A more nuanced discussion of the data and acknowledgement of the differences, which are not actually at odds, would improve the paper and place the information within a more comprehensive model.

Thank you for the comments. As noted in the original and extended discussion, we respectfully disagree with the perspective that our results align with prior results.

Recommendations for the authors:

The three reviewers believe this is an important study. They have numerous suggestions for improvement of the manuscript (outlined below), but no new experiments are required. The Editor requests some nomenclature changes as indicated in attachment 1.

Reviewer #1 (Recommendations For The Authors):

Abstract/Introduction: Although the need for this study is obvious, it is important that the authors explicitly communicate their working hypothesis < before the start of the work> to the reader. In the current form, it is unclear whether the authors aimed to test the hypothesis that glutamatergic signaling from noradrenergic neurons is important to breathing or whether to test the hypothesis that glutamatergic signaling from noradrenergic neurons is not important to breathing. If it is the latter-it is not important-then the study (related to the breathing measurements) is poorly justified and designed, as additional orthogonal approaches (e.g., actual measurements of glutamatergic signaling at the cellular level) are almost requisite. If the authors' hypothesis was originally based on existing literature suggesting that glutamatergic signaling from noradrenergic neurons is important to breathing, then the experimental design appropriate.

Thank you for the suggestion. The working hypothesis has been added in the abstract (line 2425) and the introduction (line 92-94)), making clear that we initially hypothesized that glutamatergic signaling from noradrenergic neurons is important in breathing.

Results: While the steady state measurements for breathing metrics are clearly important in defining how glutamatergic signaling may contribute to be pulmonary function, the role of glutamatergic signaling may have a greater role in the dynamics of patterns (i.e., regularity of the breathing rhythms) such traits can be described using SD1 and SD2 from Poincare maps, and/or entropy measurements. Such an analysis should be performed.

Thank you for the suggestion. The dynamic patterns of respiratory rate (Vf), tidal volume (VT), minute ventilation (VE), inspiratory duration (TI), expiratory duration (TE), breath cycle duration (TTOT), inspiratory flow rate (VT/TI), expiratory flow rate (VT/TE) have been shown as Poincaré plots and quantified and tested using the SD1 and SD2 statistics in the supplemental figures of Figure 4-7.

Results: Analyses of Inspiratory time (Ti) and flow rate (i.e., Tidal Volume / Ti) should be assessed and included.

Thank you for the suggestion. Inspiratory duration (Ti), expiratory duration (TE), breath cycle duration (TTOT), inspiratory flow rate (VT/Ti), and expiratory flow rate (VT/TE) have been included in the Figures 4-7.

Results/Methods: If similar analytical approaches were used in the current study as to that in Lusk et al. 2022, it appears that data was discontinuously sampled, rejecting periods of movement and only including periods of quiescent breathing. Were the periods of quiescent breathing different? Information should be provided to describe the total sampling duration included.

For room air, the entire gas condition was used for data analysis. For hypercapnia (5% CO2, 7% CO2, 10% CO2), only the last 5 minutes of the gas challenge period was used for data analysis. For hypoxia (10% O2), we analyzed the breathing trace of three 5-minute epochs following initiation of the gas exposure separately, e.g., epoch 1 = 5-10min, epoch 2 = 10-15min, and epoch 3 = 15-20min. All breaths included as quiescent breathing were analyzed in the aggregate for each group and experimental condition, we did not compare individual periods of quiescent breathing within or across an animal(s)/group(s)/experimental condition(s). We have added the details in the Materials and Methods (line 637-642).

Results: As mice were conscious in this study, were sniff periods (transient periods of fast breathing, i.e.,>8Hz) included in the analysis?

No, only regular quiescent breathing periods were included in the analysis.

Discussion: The authors need to discuss the limitations of their findings.

• How should the reader interpret the findings? Concluding that glutamatergic signaling is dispensable implies that it occurs in room air, hypoxia, and hypercapnia.

We have edited our discussion for clarity to highlight our conclusions that Vglut2-based glutamatergic signaling from noradrenergic neurons is ultimately dispensable for baseline breathing and hypercapnia and hypoxic chemoreflex in unanesthetized and unrestrained mice.

• Assuming that glutamatergic signaling is active during the conditions tested, then the authors should discuss what may be the potential compensations.

We have provided additional discussion surrounding potential compensatory events that may have taken place and could result in the unchanged phenotype in the experimental group.

• The authors need to discuss how age and state of consciousness may play a role in their finds. The current discussion gives the impression that their findings are broadly applicable in all cases, but the lack of differences in this study may not hold true under different conditions.

The study was done in adult (6–8-week-old) unanesthetized and unrestrained mice. In the discussion (line 472-474), we highlight that in our unpublished results, loss of NA-expressed Vglut2 does not change the survival curve in P7 neonate mice undergoing repeated bouts of autoresuscitation until death. Thus, we believed that Vglut2-based glutamatergic signaling in central NA neurons is dispensable for baseline breathing and the hypercapnic and hypoxic chemoreflexes in unanesthetized and unrestrained mice across different ages. Otherwise, we do not imply that we have interrogated any other aspects of breathing in our discussion.

Methods: Further description of the analysis window for the respiratory metrics should be provided. Were breath values for each condition taken throughout the entire condition? This is particularly important for hypoxia, where the stereotypical respiratory response is biphasic.

For room air, the entire gas condition was used for data analysis. For hypercapnia (5% CO2, 7% CO2, 10% CO2), only the last 5min of the gas challenge period was used for data analysis. For hypoxia (10% O2), we analyzed the breathing trace of three 5min time periods separately including 5-10min, 10-15min, and 15-20min during the hypoxic challenge as noted in our original manuscript, we graph and assess three 5min epochs during hypoxic exposure to capture the dynamic nature of the hypoxic ventilatory response. We have added the details in the Materials and Methods (line 637-642).

Methods: How was consciousness determined?

The conscious mice mentioned in the manuscript refer to the mice without anesthesia. We have replaced “awake” and “conscious” with “unanesthetized” in the text.

Reviewer #2 (Recommendations For The Authors):

Since no EEG/EMG recording was performed it would be more appropriate to remove "awake" and "conscious" throughout the manuscript and include the term "unanesthetized".

Thank you for the suggestion. “Awake” and “conscious” have been replaced by “unanesthetized” in the text.

Line 545: Why 32C? Isn't this temperature too high for animals?

30-32°C is the thermoneutral zone for mice. It is the range of ambient temperature where mice can maintain a stable core temperature with their minimal metabolic rate (Gordon, 1985). Whole-body plethysmography uses the barometric technique to detect pressure oscillations caused by changes in temperature and humidity with each breathing act when an animal sits in a sealed chamber (Mortola et al., 2013). Thus, maintaining the chamber temperature near the thermoneutral zone during the plethysmography assay is required to maintain constancy in respiratory and metabolic parameters from trial to trial as well as to maintain linearity of ventilatory pressure changes due to humidification, rarefaction, and thermal expansion and contraction during inspiration and expiration (Ray et al., 2011). The chamber temperature that has been used for adult plethysmography has been set across a range 30-34°C (Hodges et al., 2008; Ray et al., 2011; Hennessy et al., 2017). We use 32°C in this manuscript which is consistent with previously published literature from other groups and our own work (Sun et al., 2017; Lusk et al., 2022).

I would include the units of the physiological variables in the tables.

Thank you for the suggestion. The units of the physiological variables have been added in all the tables.

Reviewer #3 (Recommendations For The Authors):

Why is the C3 group not considered in this study?

The C3 adrenergic group, best characterized in rat, is only seen in rodents but not in many other species including primates (including human) (Kitahama et al., 1994). Thus, the C3 group is not the focus of this study where we aim to discuss if glutamate derived from noradrenergic neurons could be the potential therapeutic target of human respiratory disorders. The C3 adrenergic group is typically described as a population containing only about 30 neurons. We have added the fate map data and the adult expression pattern for the three vesicular glutamate transporters for the C3 group in the figure 1 and 2 supplements for reference.

Sub CD/CV does not appear to be defined in the manuscript.

Thank you for the point. The definition of sub CD/CV has been added in the text (line 126).

The data on line 131-133 is interesting but could be described more effectively and clearly.

Thank you for the suggestion. The text has been modified accordingly.

The end of the paragraph at lines 140 onwards is rather repeated in the paragraph that starts at line 146.

The repeated text has been removed accordingly.

Whilst anterior and posterior are correct anatomical terms, for a quadraped, rostral and caudal are more widely used - particularly in the brainstem field. Is there a particular reason for using anterior/posterior?

We followed the anatomical terminations in the Robertson et al. (2013) where they used anterior/posterior to describe C2/A2 and C1/A1.

On the protocol lines include in Figure 4-7 it would be worth adding the test day. This seems a little strange. Why wait up to one week after the habituation to perform the stimulation. How many mice were left for each day between habituation and experimentation, and does this timing affect responses? Do mice forget the habituation after a period?

Thank you for the point. We have added the test day for plethysmography in figures 4-7. After the 5 days of habituation, we began the plethysmography recordings on the sixth day. A maximum of 6 mice can be assayed for plethysmography per day due to the limited number of barometric flow through plethysmography and metabolic measurement systems we have. Thus, all animals were finished with plethysmography “within” one week of the last day of habituation. This protocol is consistent with our previous published work (Martinez et al., 2019; Lusk et al., 2022; Lusk et al., 2023). For the experiments in this manuscript, mice were assayed within 3 days after habituation. As noted in our methods and figures, each mouse is given as much as 40 mins to acclimate to the chamber (determined by directly observed quiet breathing) before data acquisition. We have no reason or evidence that indicates testing order and thus timing was a factor. The detailed explanation for the plethysmography protocol has been added in the material and methods section (line 606-625).

Please state clearly that each mouse is only exposed to one gas mixture (what I interpret is the case), or could one mouse be exposed to several different stimuli?

Each mouse is only exposed to one gas challenge (5% CO2, 7% CO2, 10% CO2, or 10% O2) in a testing period. Each testing period for an individual mouse was separated by 24hs to allow for a full recovery. The protocol is to put the mouse under room air for 45mins, switch to one gas challenge for 20mins, and switch back to room air for 20mins.

With apologies if I missed this, but did each of the respiratory stimuli produce a statistically significant response in the control mice? For example, the response to 10%O2?

Yes, each respiratory stimuli including 5/7/10% CO2 and 10% O2 produced a statistically significant response in both mutant and control mice. We have labeled the statistical significance in the Figures 4-7. Thank you for pointing this out.

Line 312: Optogenetic stimulation induced an increase from 130 to 180 breaths per min (Abbott et al., EJN 2014). It is surprising that this is called "modest". Baseline respiratory frequency was presented.

Thank you for the point. The word “modest” has been removed and the discussion has been changed accordingly (line 355-360).

Line 338: This discussion is not sufficiently nuanced. It is the increased Dia amplitude (to KCN only, not 10%CO2 ) and the stimulation of active expiration, to both stimuli, that is blocked by kyn in pFRG. There is no effect of breathing frequency. The current study would not detect such differences in active expiration.

Thank you for the suggestion. The discussion has been modified accordingly (line 382-388).

Reviewer #4 (Public Review):

Summary:

Although previous research suggested that noradrenergic glutamatergic signaling could influence respiratory control, the work performed by Chang and colleagues reveals that excitatory (specifically Vglut2) neurons is dynamically and widely expressed throughout the central noradrenergic system, but it is not significantly crucial to change baseline breathing as well the hypercapnia and hypoxia ventilatory responses. The central point that will make a significant change in the field is how NA-glutamate transmission may influence breathing control and the dysfunction of NA neurons in respiratory disorders.

Strengths:

There are several strengths such as the comprehensive analysis of Vglut1, Vglut2, and Vglut3 expression in the central noradrenergic system and the combined measurements of breathing parameters in conscious unrestrained mice.

Other considerations :

These results strongly suggest that glutamate may not be necessary for modulating breathing under normal conditions or even when faced with high levels of carbon dioxide (hypercapnia) or low oxygen levels (hypoxia). This finding is unexpected, considering many studies have underscored glutamate's vital role in respiratory regulation, more so than catecholamines. This leads us to question the significance of catecholamines in controlling respiration. Moreover, if glutamate is not essential for this function, we need to explore its role in other physiological processes such as sympathetic nerve activity (SNA), thermoregulation, and sensory physiology.

eLife assessment

Chang et al. provide glutamate co-expression profiles in the central noradrenergic system and test the requirement of Vglut2-based glutamatergic release in respiratory and metabolic activity under physiologically relevant gas challenges. Their experiments provide compelling evidence that conditional deletion of vesicular glutamate transporters from noradrenergic neurons does not impact steady-state breathing or metabolic activity in room air, hypercapnia, or hypoxia. This study provides an important contribution to our understanding of how noradrenergic neurons regulate respiratory homeostasis in conscious adult mice.

Reviewer #1 (Public Review):

Summary:

Chang et al. provide glutamate co-expression profiles in the central noradrenergic system and test the requirement of Vglut2-based glutamatergic release in respiratory and metabolic activity under physiologically relevant gas challenges. Their experiments show that conditional deletion of Vglut2 in NA neurons does not impact steady-state breathing or metabolic activity in room air, hypercapnia, or hypoxia. Their observations challenge the importance of glutamatergic signaling from Vglut2 expressing NA neurons in normal respiratory homeostasis in conscious adult mice.

Strengths:

The comprehensive Vglut1, Vglut2, and Vglut3 co-expression profiles in the central noradrenergic system and the combined measurements of breathing and oxygen consumption are two major strengths of this study. Observations from these experiments provide previously undescribed insights into (1) expression patterns for subtypes of the vesicular glutamate transporter protein in the noradrenergic system and (2) the dispensable nature of Vglut2-dependent glutamate signaling from noradrenergic neurons to breathing responses to physiologically relevant gas challenges in adult conscious mice.

Weaknesses:

Although the cellular expression profiles for the vesicular glutamate transporters are provided, the study does not document that glutamatergic-based signaling originating from noradrenergic neurons is evident at the cellular level under normal, hypoxic, and/or hypercapnic conditions. The authors effectively recognize this issue and appropriately discuss their findings in this context.

Reviewer #2 (Public Review):

The authors characterized the recombinase-based cumulative fate maps for vesicular glutamate transporters (Vglut1, Vglut2 and Vglut3) expression and compared those maps to their real-time expression profiles in central NA neurons by RNA in situ hybridization in adult mice. Authors have revealed a new and intriguing expression pattern for Vglut2, along with an entirely uncharted co-expression domain for Vglut3 within central noradrenergic neurons. Interestingly, and in contrast to previous studies, the authors demonstrated that glutamatergic signaling in central noradrenergic neurons does not exert any influence on breathing and metabolic control either under normoxic/normocapnic conditions or after chemoreflex stimulation. Also, they showed for the first-time the Vglut3-expressing NA population in C2/A2 nuclei. In addition, they were also able to demonstrate Vglut2 expression in anterior NA populations, such as LC neurons, by using more refined techniques, unlike previous studies.

A major strength of the study is the use of a set of techniques to investigate the participation of NA-based glutamatergic signaling in breathing and metabolic control. The authors provided a full characterization of the recombinase-based cumulative fate maps for Vglut transporters. They performed real-time mRNA expression of Vglut transporters in central NA neurons of adult mice. Further, they evaluated the effect of knocking down Vglut2 expression in NA neurons using a DBH-Cre; Vglut2cKO mice on breathing and control in unanesthetized mice. Finally, they injected the AAV virus containing Cre-dependent Td tomato into LC of v-Glut2 Cre mice to verify the VGlut2 expression in LC-NA neurons. A very positive aspect of the article is that the authors combined ventilation with metabolic measurements. This integration holds particular significance, especially when delving into the exploration of respiratory chemosensitivity. Furthermore, the sample size of the experiments is excellent.<br /> Despite the clear strengths of the paper, some weaknesses exist. It is not clear in the manuscript if the experiments were performed in males and females and if the data were combined. I believe that the study would have benefited from a more comprehensive analysis exploring the sex specific differences. The reason I think this is particularly relevant is the developmental disorders mentioned by the authors, such as SIDS and Rett syndrome, which could potentially arise from disruptions in central noradrenergic (NA) function, exhibit varying degrees of sex predominance. Moreover, some of the noradrenergic cell groups are sexually dimorphic. For instance, female Wistar rats exhibit a larger LC size and more LC-NA neurons than male subjects (Pinos et al., 2001; Garcia-Falgueras et al., 2005). More recently, a detailed transcriptional profiling investigation has unveiled the identities of over 3,000 genes in the LC. This revelation has highlighted significant sexual dimorphisms, with more than 100 genes exhibiting differential expression within LC-NA neurons at the transcript level. Furthermore, this investigation has convincingly showcased that these distinct gene expression patterns have the capacity to elicit disparate behavioral responses between sexes (Mulvey et al., 2018). Therefore, the authors should compare the fate maps, Vglut transporters in males and females, at least considering LC-NA neurons. Even in the absence of identified sex differences, this information retains significant importance.<br /> An important point well raised by the authors is that although suggestive, these experiments do not definitively rule out that NA-Vglut2 based glutamatergic signaling has a role in breathing control. Subsequent experiments will be necessary to validate this hypothesis.

An improvement could be made in terms of measuring body temperature. Opting for implanted sensors over rectal probes would circumvent the need to open the chamber, thereby preventing alterations in gas composition during respiratory measurements. Further, what happens to body temperature phenotype in these animals under different gas exposures? These data should be included in the Tables.

Is it plausible that another neurotransmitter within NA neurons might be released in higher amounts in DBH-Cre; Vglut2 cKO mice to compensate for the deficiency in glutamate and prevent changes in ventilation?

Continuing along the same line of inquiry is there a possibility that Vglut2 cKO from NA neurons not only eliminates glutamate release but also reduces NA release? A similar mechanism was previously found in VGLUT2 cKO from DA neurons in previous studies (Alsio et al., 2011; Fortin et al., 2012; Hnasko et al., 2010). Additionally, does glutamate play a role in the vesicular loading of NA? Therefore, could the lack of effect on breathing be explained by the lack of noradrenaline and not glutamate?

Author response:

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

Reviewer #1:

Summary:

The authors study age-related changes in the excitability and firing properties of sympathetic neurons, which they ascribe to age-related changes in the expression of KCNQ (Kv7, "M-type") K+ currents in rodent sympathetic neurons, whose regulation by GPCRs has been most thoroughly studied for over 40 years.

Strengths:

The strengths include the rigor of the current-clamp and voltage-clamp experiments and the lovely, crisp presentation of the data, The separation of neurons into tonic, phasic and adapting classes is also interesting, and informative. The ability to successfully isolate and dissociate peripheral ganglia from such older animals is also quite rare and commendable! There is much useful detail here.

Thank you for recognizing the effort we put on presenting the data and analyzing the neuronal populations. I also believe the ability to isolate neurons from old animals is worth communicating to the scientific community.

Weaknesses:

Where the manuscript becomes less compelling is in the rapamycin section, which does not provide much in the way of mechanistic insights. As such, the effect is more of an epi-phenomenon of unclear insight, and the authors cannot ascribe a signaling mechanism to it that is supported by data. Thus, this latter part rather undermines the overall impact and central advance of the manuscript. The problem is exacerbated by the controversial and anecdotal nature of the entire mTor/aging field, some of whose findings have very unfortunately had to be recently retracted.

I would strongly recommend to the authors that they end the manuscript with their analysis of the role of M current/KCNQ channels in the numerous age-related changes in sympathetic neuron function that they elegantly report, and save the rapamycin, and possible mTor action, for a separate line of inquiry that the authors could develop in a more thorough and scholarly way.

Whereas the description of the data are very nice and useful, the manuscript does not provide much in the way of mechanistic insights. As such, the effect is more of an epi-phenomenon of unclear insight, and the authors cannot ascribe changes in signaling mechanisms, such as that of M1 mAChRs to the phenomena that is supported by data.

I appreciate the new comment. We had agreed that our rapamycin experiments did not allow to ascribe the mechanism to the signaling pathway of mTOR. The new comment mentions M1 mAChRs signaling as another potential signaling mechanism. Our work centered on determining whether aging altered the function of sympathetic motor neurons and defining the mechanism. We presented evidence showing that the mechanism is a reduction of the M-current. We did not attempt to identify the signaling mechanism linking aging to a reduction in M-current. Therefore, we agree with the reviewer that we do not provide further details on the mechanism and that that remains an open question. However, I find it harsh to say that “the effect is more of an epiphenomenon of unclear insight”. How could we possibly test that the effect of aging on the excitability of these neurons only arises as a secondary effect or that is not causal? How could we test for sufficiency and necessity of aging? How could we modify the state of aging to test for causality? We would have to reverse aging and show that the effect on the excitability is gone. And that is exactly what we tried to do with the rapamycin experiment.

Reviewer #1 (Recommendations For The Authors):

(1) The significance values greater than p < 0.05 do not add anything and distract focus from the results that are meaningful. Fig. 5 is a good example. What does p = 0.7 mean? Or p = 0.6? Does this help the reader with useful information?

I thank Reviewer 1 for raising this question. We have attempted different versions of how we report p values, as we want to make sure to address rigor and transparency in reporting data. As corresponding author, I favor reporting p values for all statistical comparisons. To help the reader identifying what we considered statistically significant, we color coded the p values, with red for p-value<0.05 and black for p-value>0.05. As a reader, seeing a p-value=0.7 allows me to know that the authors performed an analysis comparing these conditions and found the mean not to be different. Not presenting the p-value makes me wonder whether the authors even analyzed those groups. In other words, I value more the ability to analyze the data seeing all p-values than not being distracted by not-significant p-values. This is just my preference.

(2) Fig. 1 is not informative and should be removed.

I thank Reviewer 1 for the suggestion. In previous drafts of the manuscript, this figure was included only as a panel. However, we decided it was better to guide the reader into the scope of our work. This is part of our scientific style and, therefore, we prefer to keep the figure.

(3) The emphasis on a particular muscarinic agonist favored by many ion channel physiologists, oxotremorine, is not meaningful (lines 192, 198). The important point is stimulation of muscarinic AChRs, which physiologically are stimulated by acetylcholine. The particular muscarinic agonist used is unimportant. Unless mandated by eLife, "cholinergic type 1 muscarinic receptors" are usually referred to as M1 mAChRs, or even better is "Gq-coupled M1 mAChRs." I don't think that Kruse and Whitten, 2021 were the first to demonstrate the increase in excitability of sympathetic neurons from stimulation of M1 mAChRs. Please try and cite in a more scholarly fashion.

A) I have modified lines 192 and 198 removing mention to oxotremorine.

B) I have modified the nomenclature used to refer to cholinergic type 1 muscarinic receptors.

C) I cited references on the role of M current on sympathetic motor neuron excitability. I also removed the reference (Kruse and Whitten, 2021) referring only on the temporal correlation between the decrease of KCNQ current with excitability.

(4) The authors may want to use the term "M current" (after defining it) as the current produced by KCNQ2&3-containing channels in sympathetic neurons, and reserve "KCNQ" or "Kv7" currents as those made by cloned KCNQ/Kv7 channels in heterologous systems. A reason for this is to exclude currents KCNQ1-containing channels, which most definitely do not contribute to the "KCNQ" current in these cells. I am not mandating this, but rather suggesting it to conform with the literature.

Thank you for the suggestion. I have modified the text to use the term M current. I maintain the use of KCNQ only when referring to KCNQ channel, such as in the section describing the abundance of KCNQ2.

(5) The section in the text on "Aging reduces KCNQ current" is confusing. Can the authors describe their results and their interpretation more directly?

I am not sure to understand the request. I assumed point 5 and 6 are related and decided to answer point 6.

(6) Please explain the meaning of the increase in KCNQ2 abundance with age in Fig. 6G. How is this increase in KCNQ2 expression consistent with an increase in excitability? The explanation of "The decrease in KCNQ current and the increase in the abundance of KCNQ2 protein suggest a potential compensatory mechanism that occurs during aging, which we are actively investigating in an independent study." is rather odd, considering that the entire thesis of this paper is that changes in excitability and firing properties are underlied by changes in KCNQ2/3 channel expression/density. Suddenly, is this not the case?? What about KCNQ3? It would be very enlightening if the authors would just quantify the ratio of KCNQ2:KCNQ3 subunits in M-type channels in young and old mice using simple TEA dose/response curves (see Shapiro et al., JNS, 2000; Selyanko et al., J. Physiol., Hadley et al., Br. J. Pharm., 2001 and a great many more). It is also surprising that the authors did not assess or probe for differences in mAChR-induced suppression of M current between SCG neurons of young and old mice. This would seem to be a fundamental experiment in this line of inquiry.

A. Please explain the meaning of the increase in KCNQ2 abundance with age in Fig. 6G. How is this increase in KCNQ2 expression consistent with an increase in excitability? The explanation of "The decrease in KCNQ current and the increase in the abundance of KCNQ2 protein suggest a potential compensatory mechanism that occurs during aging, which we are actively investigating in an independent study." is rather odd, considering that the entire thesis of this paper is that changes in excitability and firing properties are underlied by changes in KCNQ2/3 channel expression/density. Suddenly, is this not the case?? Our interpretation is that the decrease in M current is not caused by a decrease in the abundance of KCNQ (2) channels. We do not claim that changes in excitability are underlied by a reduction in the expression or density of KCNQ2 channels. On the contrary, our working hypothesis is that the reduction in M current is caused by changes in traffic, degradation, posttranslational modifications, or cofactors for KCNQ2 or KCNQ3 channels. We have modified the description in the results section to clarify this concept.

B. What about KCNQ3? Unfortunately, we did not find an antibody to detect KCNQ3 channels. I have added a sentence to state this.

C. KCNQ2:KCNQ3 subunits in M-type channels in young and old mice using simple TEA dose/response curves. This is a great idea. Thank you for the suggestion. Is this a necessary experiment for the acceptance of this manuscript?

D. It is also surprising that the authors did not assess or probe for differences in mAChR-induced suppression of M current between SCG neurons of young and old mice. This would seem to be a fundamental experiment in this line of inquiry. Reviewer 1 is correct. We did not assess for differences in the suppression of M current by mAChR activation. We do not see the connection of this experiment with the scope of the current investigation.

(7) Why do the authors use linopirdine instead of XE-991? Both are dirty drugs hardly specific to KCNQ channels at 25 uM concentrations, but linopirdine less so. The Methods section lists the source of XE991 used in the study, not linopirdine. Is there an error?

A. Why do the authors use linopirdine instead of XE-991? After validation of KCNQ2/3 inhibition by Linopirdine, we found the effect on membrane potential recordings to be reproducible. Linopirdine has also been reported to be reversible. We wanted to assess reversibility on the excitability of young neurons. We did not find the effect to be reversible. We performed experiments applying XE-991 while recording the membrane potential. XE-991 did not show a clear effect. I was not surprised by this. It is very likely that the pharmacological inhibition of one channel leads to the activation of other channel types. This is highlighted in the work by Kimm, Khaliq, and Bean, 2015. “Further experiments revealed that inhibiting either BK or Kv2 alone leads to recruitment of additional current through the other channel type during the action potential as a consequence of changes in spike shape.” In fact, it was quite remarkable that the aged and young phenotypes were mimicked by targeting KCNQ pharmacologically.

B. Both are dirty drugs hardly specific to KCNQ channels at 25 uM concentrations, but linopirdine less so. I have added a sentence to point out that linopirdine is less potent than XE-991. It reads: “We want to point out that linopirdine is less potent than XE-991 and that it has been reported to activate TRPV1 channels (Neacsu and Babes, 2010). Despite this limitation, the application of linopirdine to young sympathetic motor neurons led to depolarization and firing of action potentials.”

C. The Methods section lists the source of XE991 used in the study, not linopirdine. Is there an error? Thank you for pointing out this. I have added information for both retigabine and linopirdine in the Methods section, both were missing.

(8) Can the authors use a more scientific explanation of RTG action than "activating KCNQ channels?" For instance, RTG induces both a negative-shift in the voltage-dependance of activation and a voltage-independent increase in the open probability, both of which differing in detail between KCNQ2 and KCNQ3 subunits. The authors are free to use these exact words. Thus, the degree of "activation" is very dependent upon voltage at any voltages negative to the saturating voltages for channel activation.

I have modified the text to reflect your suggestion.

(9) Methods: did the authors really use "poly-l-lysine-coated coverslips?" Almost all investigators use poly-D-lysine as a coating for mammalian tissue-culture cells and more substantial coatings such as poly-D-lysine + laminin or rat-tail collagen for peripheral neurons, to allow firm attachment to the coverslip.

That is correct. We used poly-L-lysine-coated coverslips. Sympathetic motor neurons do not adhere to poly-D-Lysine.

(10) As a suggestion, sampling M-type/KCNQ/Kv7 current at 2 kHz is not advised, as this is far faster than the gating kinetics of the channels. Were the signals filtered?

It is correct. Currents were sampled at 2KHz. Data were low-pass filtered at 3 KHz. Our conditions are not far from what is reported by others. Some sample at 10KHz and even 50 KHz. Others do not report the sample frequency.

Reviewer #2:

Weaknesses:

None, the revised version of the manuscript has addressed all my concerns.

I am glad we were able to satisfy previous concerns.

Reviewer #3:

The main weakness is that this study is a descriptive tabulation of changes in the electrophysiology of neurons in culture, and the effects shown are correlative rather than establishing causality.

Allow me to clarify our previous responses and determine how this aligns with your concerns. In the previous revision, Reviewer 3 wrote: “It is difficult to know from the data presented whether the changes in KCNQ channels are in fact directly responsible for the observed changes in membrane excitability.” And suggested to “use of blockers and activators to provide greater relevance.” I assumed these comments were the main concern and that doing such experiments was enough to satisfy the criticism. It is discouraging to see that our experiments did not satisfy the concerns of the reviewer of being correlative.

If Reviewer 3 is referring to stablishing causality between aging and a reduction in M current, I would like to emphasize that such endeavor is complicated as there is not a clear experiment to solve that issue. Our best attempt was to reverse aging with rapamycin, but the recommendation was to remove those experiments.

… but the specifics of the effects and relevance to intact preparations are unclear. Additional experiments in slice cultures would provide greater significance on the potential relevance of the findings for intact preparations.

I apologize for missing this point in the previous revision. The proposed experiments will require an upward microscope coupled to an electrophysiology rig. Unfortunately, I do not have the equipment to do these experiments.

Summary of recommendations from the three reviewers:

Please make corrections as suggested by reviewer 1 to improve the manuscript. Specifically, reviewer 1 suggests making changes to p values in Figure 5,

It is not clear what the suggested changes are. The comment from Reviewer 1 says: The significance values greater than p < 0.05 do not add anything and distract focus from the results that are meaningful. If the suggested change is to remove p values > 0.05, I have explained my rational for keeping those values. If the Journal has a specific format on how to report p-values, I will be happy to make appropriate changes.

and the importance of citing original scholarly works related to effects of increase in excitability of sympathetic neurons by M1 receptors, and the terminology for M currents and KCNQ currents. These changes will improve the manuscript and are strongly recommended.

I cited original papers on that area, and changed the terminology for M current. I kept KCNQ when referring to the channel protein or abundance.

The section dealing with Aging Reduces KCNQ currents seems to contain a lot of extraneous information especially in the last part of the long paragraph and this section should be rewritten for improved clarity… and - the implications or lack thereof - of the correlation of KCNQ with AP firing rates.

A. I removed extraneous information in that section. It now reads: Previous work by our group and others demonstrated that cholinergic stimulation leads to a decrease in M current and increases the excitability of sympathetic motor neurons at young ages \cite{RN67,RN68,RN69,RN71, RN72, RN73, RN74, RN75}. The molecular determinants of the M current are channels formed by KCNQ2 and KCNQ3 in these neurons \cite{RN76, RN77, RN70}. Thus, Figure 6A shows a voltage response (measured in current-clamp mode) and a consecutive M current recording (measured in voltage-clamp mode) in the same neuron upon stimulation of cholinergic type 1 muscarinic receptors. It illustrates the temporal correlation between the decrease of M current with the increase in excitability and firing of APs upon activation with oxotremorine. This strong dependence led us to hypothesize that aging decreases M current, leading to a depolarized RMP and hyperexcitability (Figure 6B). For these experiments, we measured the RMP and evoked activity using perforated patch, followed by the amplitude of M current using a whole-cell voltage clamp in the same cell. We also measured the membrane capacitance as a proxy for cell size. Interestingly, M current density was smaller by 29\% in middle age (7.5 ± 0.7 pA/pF) and by 55\% in old (4.8 ± 0.7 pA/pF) compared to young (10.6 ± 1.5 pA/pF) neurons (Figure 6C-D). The average capacitance was similar in young (30.8 ± 2.2 pF), middle-aged (27.4 ± 1.2 pF), and old (28.8 ± 2.3 pF) neurons (Figure 6E), suggesting that aging is not associated with changes in cell size of sympathetic motor neurons, and supporting the hypothesis that aging alters the levels of M current. Next, we tested the effect on the abundance of the channels mediating M current. Contrary to our expectation, we observed that KCNQ2 protein levels were 1.5 ± 0.1 -fold higher in old compared to young neurons (Figure 6F-G). Unfortunately, we did not find an antibody to detect consistently KCNQ3 channels. We concluded that the decrease in M current is not caused by a decrease in the abundance of KCNQ2 protein.

B. and - the implications or lack thereof - of the correlation of KCNQ with AP firing rates. I am not sure to understand the request on the section of the correlation of KCNQ with AP firing rate. I divided the long paragraph.

The apparent lack of correlation between KCNQ current and KCNQ2 protein needs to be better explained. This is a central part of the study and this result undercuts the premise of the paper.

Indeed, total KCNQ2 protein abundance increases while M current decreases. We do not claim in our work that changes in excitability are caused by a reduction in the expression or density of KCNQ2 channels. On the contrary, our current working hypothesis is that the reduction in M current is caused by changes in traffic, degradation, posttranslational modifications, or cofactors for KCNQ2 or KCNQ3 channels. I have modified the description in the results section and discussion to clarify this concept.

Additionally, the poor specificity of Linordipine for KCNQ should be pointed out in the limitations.

I pointed this limitation. It reads: We want to point out that linopirdine is less potent than XE-991 and that it has been reported to activate TRPV1 channels (Neacsu and Babes, 2010). Despite this limitation, the application of linopirdine to young sympathetic motor neurons led to depolarization and firing of action potentials.

Finally, the editor notes that the author response should not contain ambiguities in what was addressed in the revision. In the original summary of consolidated revisions that were requested, one clearly and separately stated point (point 4) was that experiments in slice cultures should be strongly considered to extend the significance of the work to an intact brain preparation. The author response letter seems to imply that this was done, but this is not the case. The author response seems to have combined this point with another separate point (point 3) about using KCNQ drugs, and imply that all concerns were addressed. Authors should be clear about what revisions were in fact addressed.

As corresponding author, and direct responsible of the document provided for the reply to the reviewers, I apologize for my mistake. After reviewing this comment, I realized I did not respond to the Major points in the section of the Recommendations for the authors from Reviewer 3. I missed that entire section. My previous responses addressed the Public review of reviewer 3. When doing so, I did not separate the sentences, omitting the request on performing the experiment in slices.

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

Reviewer #1

Summary:

The authors study age-related changes in the excitability and firing properties of sympathetic neurons, which they ascribe to age-related changes in the expression of KCNQ (Kv7, "M-type") K+ currents in rodent sympathetic neurons, whose regulation by GPCRs has been most thoroughly studied for over 40 years. The authors suggest the ingestion of rapamycin may partially reverse the age-related decrease in M-channel expression. With the rapamycin part included, it is unclear how this work will impact the field of age-related neuronal dysfunction, as the mechanistic information is not strong.

Strengths:

The strengths include the rigor of the current-clamp and voltage-clamp experiments, the lovely, crisp presentation of the data, and the expert statistics. The separation of neurons into tonic, phasic, and adapting classes is also interesting, and informative. The writing is also elegant, and crisp. The above is especially true of the manuscript up until the part dealing with the effects of rapamycin, which becomes less compelling.

We appreciate the thoughtful comments and constructive feedback to improve the impact of the manuscript.

Weaknesses:

Where the manuscript becomes less compelling is in the rapamycin section, which does not provide much in the way of mechanistic insights. As such, the effect is more of an epi-phenomenon of unclear insight, and the authors cannot ascribe a signaling mechanism to it that is supported by data. Thus, this latter part rather undermines the overall impact and central advance of the manuscript. The problem is exacerbated by the controversial and anecdotal nature of the entire mTor/aging field, some of whose findings have very unfortunately had to be recently retracted.

I would strongly recommend to the authors that they end the manuscript with their analysis of the role of M current/KCNQ channels in the numerous age-related changes in sympathetic neuron function that they elegantly report, and save the rapamycin, and possible mTor action, for a separate line of inquiry that the authors could develop in a more thorough and scholarly way.

We agree with the reviewer in that we cannot ascribe a signaling mechanism to the reversibility observed with rapamycin. Therefore, we are following the recommendation of the reviewer and have removed the rapamycin section.

We want to emphasize that, in the aging field, any advancement in the knowledge of how drugs such as rapamycin reverse age-associated phenotypes is of crucial importance. These drugs, commonly referred to as aging interventions, include rapamycin, calorie restriction, elamipretide, and metformin. We could have used any of these interventions. And yet, the cellular and molecular mechanisms for each one of these anti-aging drugs are unknown.

We want to note that, although the nature of the mTOR field is controversial, the effect of rapamycin in extending lifespan and improving health is not. At least these authors have not been able to find retracted papers on that subject or notices from the NIA alerting on this issue. We kindly request the reviewer to provide the references related to rapamycin that were retracted so we can evaluate how that affects the rigor of the premise for our future work.

As authors, we also find it important to note that we are confident of our observations regarding the effect of rapamycin, and that we are not removing this section because we are retracting our claims. We will use these data to continue our research of the mechanism behind the effect of aging on sympathetic motor neurons.

Reviewer #2:

Summary:

This research shows compelling and detailed evidence showing that aging influences intrinsic membrane properties of peripheral sympathetic motor neurons such that they become more excitable. Furthermore, the authors present convincing evidence that the oral administration of the anti-aging drug Rapamycin partially reversed hyperexcitability in aged neurons. This study also investigates the molecular mechanisms underlying age-associated hyperexcitability in mouse sympathetic motor neurons. In that regard, the authors found an age-associated reduction of an outward current having properties similar to KCNQ2/Q3 potassium current. They suggested a reduction of KCNQ2/Q3 current density in aged neurons as a potential mechanism behind their overactivity.

Strengths:

Detailed and rigorous analysis of electrical responses of peripheral sympathetic motor neurons using electrophysiology (perforated patch and whole-cell recordings). Most of the conclusions of this paper are well supported by the data.

We thank the reviewer for valuing our effort to present a detailed and rigorous analysis.

Weaknesses:

(1) The identity of the age-associated reduced current as KCNQ2/Q3 is not corroborated by pharmacology (blocking the current with the specific blocker XE-991).

We have performed experiments using blockers of KCNQ channels. See responses below.

(2) The manuscript does not include a direct test of the reduction of KCNQ current as the mechanism behind age-induced hyperexcitability.

Thank you for raising this point. We have performed experiments blocking KCNQ channels with Linopiridine in young neurons and found that the pharmacological reduction of KCNQ current was enough to depolarize the cell and, in some cases, elicit the firing of action potentials. We present the results in a new figure. We also added the description in the Results section.

Reviewer #3:

This is a descriptive study of membrane excitability and Na+ and K+ current amplitudes of sympathetic motor neurons in culture. The main findings of the study are that neurons isolated from aged animals show increased membrane excitability manifested as increased firing rates in response to electrical stimulation and changes in related membrane properties including depolarized resting membrane potential, increased rheobase, and spontaneous firing. By contrast, neuron cultures from young mice show little to no spontaneous firing and relatively low firing rates in response to current injection. These changes in excitability correlate with significant reductions in the magnitude of KCNQ currents in aged neurons compared to young neurons. Treating cultures with the immunosuppressive drug, rapamycin, which has known antiaging effects in model animals appears to reverse the firing rates in aged neurons and enhance KCNQ current. The authors conclude that aging promotes hyperexcitability of sympathetic motor neurons.

The electrophysiological cataloging of the neuronal properties is generally well done, and the experiments are performed using perforated patch recordings which preserve the internal constituents of neurons, providing confidence that the effects seen are not due to washout of regulators from the cells.

The main weakness is that this study is a descriptive tabulation of changes in the electrophysiology of neurons in culture, and the effects shown are correlative rather than establishing causality. It is difficult to know from the data presented whether the changes in KCNQ channels are in fact directly responsible for the observed changes in membrane excitability.

We appreciate the constructive criticism. In an attempt to assess whether changes in KCNQ are in fact directly responsible for the changes in membrane excitability, we have performed experiments blocking KCNQ channels with Linopirdine in young neurons and found that the pharmacological reduction of KCNQ current was enough to depolarize the cell and, in some cases, elicit the firing of action potentials. Conversely, we activated KCNQ channels in old neurons with retigabine and found that the pharmacological activation was enough to hyperpolarize the membrane potential and stop the firing of action potentials. This effect was reversible. These two experiments provide solid evidence to our statement that age-associated reduction of KCNQ activity is responsible for the hyperexcited state in sympathetic motor neurons. We present the results in a new figure (Figure 8). We also added the description in the Results section.

Furthermore, a notable omission seems to be the analysis of Ca2+ currents which have been widely linked to alterations in membrane properties in aging.

We thank the reviewer for the comment. We did omit to include data on our studies of calcium currents. We agree that the study of the effect of calcium currents is relevant as it can influence the afterhyperpolarization. Furthermore, we believe that potential effects on calcium currents need to be studied in relation to other physiological processes that depend on calcium, including excitation-transcription coupling, calcium handling, and neurotransmitter release. Adding this information to this manuscript would only contribute to the tabulation of effects that we observe in sympathetic motor neurons with aging. As our main goal was to determine the ion channels responsible for the hyperexcited state, voltage-gated calcium channels or other calcium sources could have reflected a more indirect mechanism as compared to changes in sodium or potassium currents. We will continue our investigation on calcium currents and report our observations in the future, but for now, we have decided to leave it out of this work.

As well, additional experiments in slice cultures would provide greater significance on the potential relevance of the findings for intact preparations. Finally, experiments using KCNQ blockers and activators could provide greater relevance that the observed changes in KCNQ are indeed connected to changes in membrane excitability.

We are happy to report that we have performed these experiments and that the results strengthen the conclusion that changes in KCNQ are connected to changes in membrane excitability.

Recommendations for the authors:

We recommend the following essential revisions summarized from the reviews:

(1) Is the change in KCNQ current responsible for the altered membrane excitability? What happens to membrane excitability when KCNQ is partially blocked (see reviewer 2 comment below)? Conversely, what happens to the excitability of aged neurons if KCNQ is activated (e.g., with retigabine)? (see reviewer 3 comment below). Results of these important experiments are needed to support the argument that KCNQ underlies the alterations in firing and membrane excitability.

We have responded to this point. Thank you for the suggested experiments. In summary, the new experiments show that blocking KCNQ channels in young neurons lead to depolarization, and in some cases, the firing of action potentials. Conversely, the activation of KCNQ channels in aged neurons leads to hyperpolarization and a cease of firing. We have added a new figure and reported the results in the Results section.

(2) Rapamycin experiments are underdeveloped and weak. These should be further developed by examining the effects of KCNQ blockers to see if their effects on membrane excitability are reversed. Also, see comment 2 from reviewer 1.

We have followed the recommendation by reviewer 1 and removed the section on rapamycin.

(3) The study should examine voltage-gated calcium currents to determine potential changes in these currents with aging. See reviewer 3 comments.

We thank the reviewer for the comment. We performed preliminary experiments and found that aging impacts calcium currents. However, we omitted to include the data. In our opinion, the changes in calcium currents are outside the scope of this work, as the changes could be related to physiological processes that go beyond the control of firing. Effects on calcium currents need to be studied in relation to other physiological processes that depend on calcium, including excitation-transcription coupling, calcium handling, and neurotransmitter release. The study of the relationship between changes in calcium currents and those physiological processes would require multiple experiments and detailed analysis. We will continue our investigation on calcium currents and report our observations in the future, but for now, we have decided to leave it out of this work.

We have also edited suggestions in the Figures and Legends.

(2) In Fig.4 panel H, Y-axis must be # AP at 100 pA.

We corrected the axis in Figure 4H.

(3) In Legend Fig. 5, the number of cells for each subpopulation (n) needs to be corrected. In plots F-I, n= 9, 7, and 3 seem to be the number of adapting cells for 12-, 64- and 115w-old, respectively, instead of the number of single, phasic, and old cells for 12-week-old mice. A similar correction seems to be needed for 64-week-old and 115-week-old.

We corrected the n number in Figure 5.

(4) In Figure 6 panel C, it would be helpful for a reader to align the voltage protocol depicted with the current shown.

We have aligned the voltage protocol to the current traces.

(5) In the legend of Figure 7, the description of panel A ends with "Magnitude of voltage step to elicit each trace is shown in black", however in panel A there is no voltage depiction. In the description of panel D, "N = X animals, n=x cells" must be corrected.

We have modified the legend to clarify. It now reads: “Text at the right of each current trace corresponds to the voltage used to elicit that current.”

New Figure 8

Author response image 1.

Pharmacological inhibition and activation of KCNQ channels mimic the age-dependent phenotype. A. Membrane potential recordings from two young neurons treated with 25 μM linopirdine during the time illustrated by the light gray box. No holding current was applied. B. Left: Summary of the resting membrane potential measured before (light orange) and after (dark orange) the application of linopirdine. Right: Summary of the depolarization produced by linopirdine calculated by subtracting the post-drug voltage from the pre-drug voltage (V). Data points are from N = 2 animals, n = 8 cells, 14-week-old mice. C. Membrane potential recordings from two aged neurons treated with 10 μM retigabine during the time illustrated by the light gray box. No holding current was applied. D. Left: Summary of the resting membrane potential measured before (light purple) and after (dark purple) the application of retigabine. Right: Summary of the hyperpolarization produced by retigabine calculated by subtracting the post-drug voltage from the pre-drug voltage (V). Data points are from N = 2 animals, n = 7 cells, 120-week-old mice. P-values are shown at the top of the graphs.

Reviewer #3 (Public Review):

This study described changes in membrane excitability and Na+ and K+ current amplitudes of sympathetic motor neurons in culture. The findings indicate that neurons isolated from aged animals show increased membrane excitability manifested as increased firing rates in response to electrical stimulation and changes in related membrane properties including depolarized resting membrane potential, increased rheobase, and spontaneous firing. By contrast, neuron cultures from young mice show little to no spontaneous firing and relatively low firing rates in response to current injection. These changes in excitability correlate with reductions in the magnitude of KCNQ currents in neurons cultured from aged mice compared to neurons from cultured from young mice. The authors conclude that aging promotes hyperexcitability of sympathetic motor neurons through changes in KCNQ channels.

The electrophysiological cataloging of the neuronal properties is well done, and the experiments are performed using perforated patch recordings which preserves the internal constituents of neurons, providing confidence that the effects seen are not due to washout of regulators from the cells. The main weakness is that this study is a descriptive tabulation of changes in the electrophysiology of neurons in culture, and the effects shown are correlative rather than establishing causality. Pharmacological support is provided indicating that blockade or enhancement of KCNQ reverses the changes in excitability, but the specifics of the effects and relevance to intact preparations are unclear. Additional experiments in slice cultures would provide greater significance on the potential relevance of the findings for intact preparations.

eLife assessment

This study presents valuable observations indicating that the excitability of cultured sympathetic motor neurons increases in neurons cultured from aged mice, and is inversely correlated with the amplitude of KCNQ currents. The alterations in membrane excitability are relevant for aging-related changes in neuronal membrane properties. While the study documents interesting changes in membrane excitability in cultured neurons with aging, the mechanisms underlying these changes are not clear and physiological relevance of the results to the intact circuits is incomplete.

Reviewer #1 (Public Review):

Summary:

The authors study age-related changes in the excitability and firing properties of sympathetic neurons, which they ascribe to age-related changes in the expression of KCNQ (Kv7, "M-type") K+ currents in rodent sympathetic neurons, whose regulation by GPCRs has been most thoroughly studied for over 40 years.

Strengths:

The strengths include the rigor of the current-clamp and voltage-clamp experiments and the lovely, crisp presentation of the data, The separation of neurons into tonic, phasic and adapting classes is also interesting, and informative. The ability to successfully isolate and dissociate peripheral ganglia from such older animals is also quite rare and commendable! There is much useful detail here.

Weaknesses:

Whereas the description of the data are very nice and useful, the manuscript does not provide much in the way of mechanistic insights. As such, the effect is more of an epi-phenomenon of unclear insight, and the authors cannot ascribe changes in signaling mechanisms, such as that of M1 mAChRs to the phenomena that is supported by data.

Reviewer #2 (Public Review):

Summary:

This research shows compelling and detailed evidence showing that aging influences intrinsic membrane properties of peripheral sympathetic motor neurons, which become hyperexcitable. The authors found that sympathetic motor neurons from old mice exhibit increased firing rates (spontaneous and evoked), more depolarized membrane resting potential, and increased rheobase. Furthermore, the study investigates cellular mechanisms underlying age-associated hyperexcitability and shows solid evidence supporting that a decreased activity of KCNQ channels during aging is a major contributor to the increased excitability of sympathetic old neurons. All conclusions of this paper are well supported by the data.

Strengths:

Detailed and rigorous analysis of electrical responses of peripheral sympathetic motor neurons using electrophysiology (perforated patch and whole-cell recordings). The study identifies a decrease in KCNQ current as a cellular mechanism behind age-induced hyperexcitability in sympathetic motor neurons.

Weaknesses:

None, the revised version of the manuscript has addressed all my concerns.

Author response:

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

eLife assessment

In this important paper, Blin and colleagues develop a high-throughput behavioral assay to test spontaneous swimming and olfactory preference in individual Mexican cavefish larvae. The authors present compelling evidence that the surface and cave morphs of the fish show different olfactory preferences and odor sensitivities and that individual fish show substantial variability in their spontaneous activity that is relevant for olfactory behaviour. The paper will be of interest to neurobiologists working on the evolution of behaviour, olfaction, and the individuality of behaviour.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors posed a research question about how an animal integrates sensory information to optimize its behavioral outputs and how this process evolved. Their data (behavioral output analysis with detailed categories in response to the different odors in different concentrations by comparing surface and cave populations and their hybrid) partially answer this tough question. They built a new low-disturbance system to answer the question. They also found that the personality of individual fish is a good predictor of behavioral outputs against odor response. They concluded that cavefish evolved to specialize their response to alanine and histidine while surface fish are more general responders, which was supported by their data.

Strengths:

With their new system, the authors could generate clearer results without mechanical disturbances. The authors characterize multiple measurements to score the odor response behaviors, and also brought a new personality analysis. Their conclusion that cavefish evolved as a specialist to sense alanine and histidine among 6 tested amino acids was well supported by their data.

Weaknesses:

The authors posed a big research question: How do animals evolve the processes of sensory integration to optimize their behavioral outputs? I personally feel that, to answer the questions about how sensory integration generates proper (evolved) behavior, the authors at least need to show the ecological relevance of their response. For the alanine/histidine preference in cavefish, they need data for the alanine and other amino acid concentrations in the local cave water and compare them with those of surface water.

We agree with the reviewer. This is why, in the Discussion section, we had written: “…Such significant variations in odor preferences or value may be adaptive and relate to the differences in the environmental and ecological conditions in which these different animals live. However, the reason why Pachón cavefish have become “alanine specialists” remains a mystery and prompts analysis of the chemical ecology of their natural habitat. Of note, we have not found an odor that would be repulsive for Astyanax so far, and this may relate to their opportunist, omnivorous and detritivore regime (Espinasa et al., 2017; Marandel et al., 2020).” This is also why we currently develop field work projects aimed at clarifying this question. However, such experiments and analyses are challenging, practically and technically. We hope we can reach some conclusions in the future.

To complete the discussion we have also added an important hypothesis: “Alternatively, specialization for alanine may not need to be specific for an olfactory cue present only, or frequently, or in high amounts in caves. Bat guano for example, which is probably the main source of food in the Pachón cave, must contain many amino acids. Enhanced recognition of one of them - in the present case alanine but evolution may have randomly acted for enhanced recognition of another amino acid – should suffice to confer cavefish with augmented sensitivity to their main source of nutriment.”

Also, as for "personality matters", I read that personality explains a large variation in surface fish. Also, thigmotaxis or wall-following cavefish individuals are exceeded to respond well to odorants compared with circling and random swimming cavefish individuals. However, I failed to understand the authors' point about how much percentages of the odorant-response variations are explained (PVE) by personality. Association (= correlation) was good to show as the authors presented, but showing proper PVE or the effect size of personality to predict the behavioral outputs is important to conclude "personality is matter"; otherwise, the conclusion is not so supported.

From the above, I recommend the authors reconsider the title also their research questions well. At this moment, I feel that the authors' conclusions and their research questions are a little too exaggerated, with less supportive evidence.

Thank you for this interesting suggestion, which we have fully taken into consideration. We have therefore now calculated and plotted PVE (the percentage of variation explained on the olfactory score) as a function of swimming speed or as a function of swimming pattern. The results are shown in modified Figure 8 of our revised ms and they suggest that the personality (here, swimming patterns or swimming speed) indeed predicts the olfactory response skills. Therefore, we would like to keep our title as we provide support for the fact that “personality matters”.

Also, for the statistical method, Fisher's exact test is not appropriate for the compositional data (such as Figure 2B). The authors may quickly check it at https://en.wikipedia.org/wiki/Compositional_data or https://www.annualreviews.org/doi/pdf/10.1146/annurev-statistics-042720-124436.

The authors may want to use centered log transformation or other appropriate transformations (Rpackage could be: https://doi.org/10.1016/j.cageo.2006.11.017). According to changing the statistical tests, the authors' conclusion may not be supported.

Actually, in most cases, the distributions are so different (as seen by the completely different colors in the distribution graphs) that there is little doubt that swimming behaviors are indeed different between surface and cavefish, or between ‘before’ and ‘after’ odor stimulation. However, it is true that Fisher’s exact test is not fully appropriate because data can be considered as compositional type. For this kind of data, centered log transformation have been suggested. However, our dataset contains many zeros, and this is a case where log transformations have difficulty handling.

To help us dealing with our data, the reviewer proposed to consider the paper by Greenacre (2021) (https://www.annualreviews.org/doi/pdf/10.1146/annurev-statistics-042720-124436). In his paper, Greenacre clearly wrote: "Zeros in compositional data are the Achilles heel of the logratio approach (LRA)."

Therefore, we have now tested our data using CA (Correspondence Analysis), that can deal with table containing many zeros and is a trustable alternative to LRA (Cook-Thibeau, 2021; Greenacre, 2011).

The results of CA analysis are shown in Supplemental figure 8 and they fully confirm the difference in baseline swimming patterns between morphs as well as changes (or absence of changes) in behavioral patterns after odor stimulation suggested by the colored bar plots in main figures, with confidence ellipses overlapping or not overlapping, depending on cases. Therefore, the CA method fully confirms and even strengthens our initial interpretations.

Finally, we have kept our initial graphical representation in the ms (color-coded bar plots; the complete color code is now given in Suppl. Fig7), and CA results are shown in Suppl. Figure 8 and added in text.

Reviewer #2 (Public Review):

In their submitted manuscript, Blin et al. describe differences in the olfactory-driven behaviors of river-dwelling surface forms and cave-dwelling blind forms of the Mexican tetra, Astyanax mexicanus. They provide a dataset of unprecedented detail, that compares not only the behaviors of the two morphs but also that of a significant number of F2 hybrids, therefore also demonstrating that many of the differences observed between the two populations have a clear (and probably relatively simple) genetic underpinning.

To complete the monumental task of behaviorally testing 425 six-week-old Astyanax larvae, the authors created a setup that allows for the simultaneous behavioral monitoring of multiple larvae and the infusion of different odorants without introducing physical perturbations into the system, thus biasing the responses of cavefish that are particularly fine-tuned for this sensory modality. During the optimization of their protocol, the authors also found that for cave-dwelling forms one hour of habituation was insufficient and a full 24 hours were necessary to allow them to revert to their natural behavior. It is also noteworthy that this extremely large dataset can help us see that population averages of different morphs can mask quite significant variations in individual behaviors.

Testing with different amino-acids (applied as relevant food-related odorant cues) shows that cavefish are alanine- and histidine-specialists, while surface fish elicit the strongest behavioral responses to cysteine. It is interesting that the two forms also react differently after odor detection: while cave-dwelling fish decrease their locomotory activity, surface fish increase it. These differences are probably related to different foraging strategies used by the two populations, although, as the observations were made in the dark, it would be also interesting to see if surface fish elicit the same changes in light as well.

Thank you for these nice comments.

Further work will be needed to pinpoint the exact nature of the genetic changes that underlie the differences between the two forms. Such experimental work will also reveal how natural selection acted on existing behavioral variations already present in the SF population.

Yes. Searching for genetic underpinnings of the sensory-driven behavioral differences is our current endeavor through a QTL study and we should be able to report it in the near future.

It will be equally interesting, however, to understand what lies behind the large individual variation of behaviors observed both in the case surface and cave populations. Are these differences purely genetic, or perhaps environmental cues also contribute to their development? Does stochasticity provided by the developmental process has also a role in this? Answering these questions will reveal if the evolvability of Astyanax behavior was an important factor in the repeated successful colonization of underground caves.

Yes. We will also access (at least partially) responses to most of these questions in our current QTL study.

Reviewer #3 (Public Review):

Summary:

The paper explores chemosensory behaviour in surface and cave morphs and F2 hybrids in the Mexican cavefish Astyanax mexicanus. The authors develop a new behavioural assay for the longterm imaging of individual fish in a parallel high-throughput setup. The authors first demonstrate that the different morphs show different basal exploratory swimming patterns and that these patterns are stable for individual fish. Next, the authors test the attraction of fish to various concentrations of alanine and other amino acids. They find that the cave morph is a lot more sensitive to chemicals and shows directional chemotaxis along a diffusion gradient of amino acids. For surface fish, although they can detect the chemicals, they do not show marked chemotaxis behaviour and have an overall lower sensitivity. These differences have been reported previously but the authors report longer-term observations on many individual fish of both morphs and their F2 hybrids. The data also indicate that the observed behavior is a quantitative genetic trait. The approach presented will allow the mapping of genes' contribution to these traits. The work will be of general interest to behavioural neuroscientists and those interested in olfactory behaviours and the individual variability in behavioural patterns.

Strengths:

A particular strength of this paper is the development of a new and improved setup for the behavioural imaging of individual fish for extended periods and under chemosensory stimulation. The authors show that cavefish need up to 24 h of habituation to display a behavioural pattern that is consistent and unlikely to be due to the stressed state of the animals. The setup also uses relatively large tanks that allow the build-up of chemical gradients that are apparently present for at least 30 min.

The paper is well written, and the presentation of the data and the analyses are clear and to a high standard.

Thank you for these nice comments.

Weaknesses:

One point that would benefit from some clarification or additional experiments is the diffusion of chemicals within the behavioural chamber. The behavioural data suggest that the chemical gradient is stable for up to 30 min, which is quite surprising. It would be great if the authors could quantify e.g. by the use of a dye the diffusion and stability of chemical gradients.

OK. We had tested the diffusion of dyes in our previous setup and we also did in the present one (not shown). We think that, due to differences of molecular weight and hydrophobicity between the tested dyes and the amino acid molecules we are using, their diffusion does not constitute a proper read-out of actual amino acid diffusion. We anticipate that amino acid diffusion is extremely complex in the test box, possibly with odor plumes diffusing and evolving in non-gradient patterns, in the 3 dimensions of the box, and potentially further modified by the fish swimming through it, the flow coming from the opposite water injection side and the borders of the box. This is the reason why we have designed the assay with contrasting “odor side” and “water control side”. Moreover, our question here is not to determine the exact concentration of amino acid to which the fish respond, but to compare the responses in cavefish, surface fish and F2 hybrids. Finally and importantly, we have performed dose/response experiments whereby varying concentrations have been presented for 3 of the 6 amino acids tested, and these experiments clearly show a difference in the threshold of response of the different morphs.

The paper starts with a statement that reflects a simplified input-output (sensory-motor) view of the organisation of nervous systems. "Their brains perceive the external world via their sensory systems, compute information and generate appropriate behavioral outputs." The authors' data also clearly show that this is a biased perspective. There is a lot of spontaneous organised activity even in fish that are not exposed to sensory stimulation. This sentence should be reworded, e.g. "The nervous system generates autonomous activity that is modified by sensory systems to adapt the behavioural pattern to the external world." or something along these lines.

Done

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In addition to my comments in the "weakness" section above, here are my other comments.

How many times fish were repeatedly assayed and what the order (alanine followed by cysteine, etc) was, is not clear (Pg 24, Materials and Methods). I am afraid that fish memorize the prior experience to get better/worse their response to the higher conc of alanine, etc. Please clarify this point.

Many fish were tested in different conditions on consecutive days, indeed. Most often, control experiments (eg, water/nothing; water/water; nothing/nothing) were followed by odor testing. In such cases, there is no risk that fish memorize prior experience and that such previous experience interferes with response to odor. In other instances, fish were tested with a low concentration of one amino acid, followed by a high concentration of another amino acid, which is also on the safe side. Of note, on consecutive days, the odors were always perfused on alternate sides of the test box, to avoid possibility of spatial memory. Finally, in the few cases where increasing concentrations of the same amino acids were perfused consecutively, 1) they were perfused on alternate sides, 2) if the fish does not detect a low concentration below threshold / does not respond, then prior experience should not interfere for responding to higher concentrations, and 3) we have evidence (unpublished, current studies) that when a fish is given increasing concentrations of the same amino acid above detection threshold, then the behavioral response is stable and reproducible (eg does not decrease or increase).

Minor points:

Thygmotaxis and wall following.

Classically, thigmotaxis and wall following are treated as the same (sharma et al., 2009; https://pubmed.ncbi.nlm.nih.gov/19093125/) but the authors discriminate it in thigmotaxis at X-axis and Y-axis because fish repeatedly swam back and forth on x-axis wall or y-axis wall. I understand the authors' point to discriminate WF and T but present them with more explanations (what the differences between them) in the introduction and result sections.

Done

Pg5 "genetic architecture" in the introduction.

"Genetic architecture" analysis needs a more genomic survey, such as GWAS, QTL mapping, and Hi-C. Phenotype differences in F2 generation can be stated as "genetic factor(s)" "genetic component(s)", etc. please revise.

Done

Pg10 At the serine treatment, the authors concluded that "...suggesting that their detection threshold for serine is lower than for alanine." I believe that the 'threshold for serine is higher' according to the authors' data. Their threshold-related statement is correct in Pg21 "as SF olfactory concentration detection threshold are higher than CF,..." So the statement on page 10 is a just mistake, I think. Please revise.

Done (mistake indeed)

Pg11 After explaining Fig5, the statement "In sum, the responses of the different fish types to different concentrations of different amino acids were diverse and may reflect complex, case-bycase, behavioral outputs" does not convey any information. Please revise.

OK. Done : “In sum, the different fish types show diverse responses to different concentrations of different amino acids.”

For the personality analysis (Fig 7)

The index value needs more explanation. I read the materials and methods three times but am still confused. From the equation, the index does not seem to exceed 1.0, unless the "before score" was a negative value, and the "after score" value was positive. I could not get why the authors set a score of 1.5 as the threshold for the cumulative score of these different behavior index values (= individual score). Please provide more description. Currently, I am skeptical about this index value in Fig 7.

Done, in results and methods.

Pg15 the discussion section

Please discuss well the difference between the authors' finding (cavefish respond 10^-4M for position and surface fish responded 10^-4 for thig-Y; Fig 4AB), and those in Hinaux et al. 2016 (cavefish responded 10^-10M alanine but surface fish responded 10^-5M or higher). It seems that surface fish could respond to the low conc of alanine as cavefish do, which is opposed to the finding in Hinaux 2016.

The increase in NbrtY at population level for surface fish with 10-4M alanine (~10-6M in box) was most probably due to only a few individuals. Contrarily to cavefish, all other parameters were unchanged in surface fish for this concentration. Moreover, at individual level, only 3.2% of surface fish had significant olfactory scores (to be compared to 81.3% for cavefish). Thus, we think that globally this result does not contradict our previous findings in Hinaux et al (2016), and solely represent the natural, unexplained variations inherent to the analysis of complex animal behaviors – even when we attempt to use the highest standards of controlled conditions.

Of note, in the revised version, we have now included a full dose/response analysis for alanine concentration ranging from 10-2M to 10-10M, on cavefish. Alanine 10-5M has significant effects (now shown in Suppl Fig2 and indicated in text; a column has been added for 10-5M in Summary Table 1). Lower concentrations have milder effects (described in text) but confirm the very low detection threshold of cavefish for this amino acid.

Pg19, "In sum, CF foraging strategy has evolved in response to the serious challenge of finding food in the dark"

My point is the same as explained in the 'weakness' section above: how this behavior is effective in the cave life, if they conclude so? Please explain or revise this statement.

The present manuscript reports on experiments performed in “artificial” and controlled laboratory conditions. We are fully aware that these conditions are probably distantly related to conditions encountered in the wild. Note that we had written in original version (page 20) “…for 6-week old juveniles in a rectangular box - but the link may be more elusive when considering a fish swimming in a natural, complex environment.” As the reviewer may know, we also perform field studies in a more ethological approach of animal behaviors, thus we may be able to discuss this point more accurately in the future.

Pg20 "To our knowledge, this is the first time individual variations are taken into consideration in Astyanax behavioral studies."

This is wrong. Please see Fernandes et al., 2022. (https://pubmed.ncbi.nlm.nih.gov/36575431/).

OK. The sentence is wrong if taken in its absolute sense, i.e., considering inter-individual variations of a given parameter (e.g., number of neuromasts per individual or number of approaches to vibrating rod in Fernandez et al, 2022). In this same sense, Astyanax QTL studies on behaviors in the past also took into account variations among F2 individuals. Here, we wanted to stress that personality was taken into consideration. The sentence has been changed: “To our knowledge, this is the first time individual temperament is taken into consideration in Astyanax behavioral studies.”

Figure 2B and others.

The order of categories (R, R-TX, etc) should match in all columns (SF, F2, and CF). Currently, the category orders seem random or the larger ratio categories at the bottom, which is quite difficult to compare between SF, F2, and CF. Also, the writings in Fig 2A (times, Y-axis labels, etc), and the bargraphs' writings are quite difficult to read in Fig 2B, Fig 3B 4H, 5GN, 6EFG. Also, no need to show fish ID in Fig 2C in the current way, but identify the fish data points of the fish in Fig 2D (SF#40, CF#65, and F2#26) in Fig 2C if the authors want to show fish ID numbers in the boxplots. Fish ID numbers in other boxplot figures are recommended to be removed too.

We have thought a lot on how to best represent the distributions of swimming patterns in graphs such as Fig 2B and others. The difficulty is due to the existence of many combinations (33 possibilities in total, see new Suppl Fig7), which are never the same in different plots/conditions because individual tested fish are different. We decided that that the best way was to represent, from bottom to top, the most used to the less used swimming patterns, and to use a color code that matches at best the different combinations. It was impossible to give the full color code on each figure, therefore it was simplified, and we believe that the results are well conveyed on the graphs. We would like to keep it as it is. To respond (partially) to the reviewer’s concern, we have now added a full color code description in a new Supplemental Figure 7 (associated to Methods).

Size of lettering has been modified in all pattern graphs like Fig2A. Thanks for the suggestion, it reads better now.

Finally, we would like to keep the fish ID numbers because this contributes to conveying the message of the paper, that individuality matters.

Raw data files were not easy to read in Excel or LibreOffice. Please convert them into the csv format to support the rigor in the authors' conclusion.

We do not understand this request. Our very large dataset must be analysed with R, not excel for stats or for plotting and pattern analysis. However, raw data files can be opened in excel with format conversion.

Reviewer #2 (Recommendations For The Authors):

I think most of the experimental procedures (with few exceptions, see below) are well-defined and nicely described, so the majority of my suggestions will be related to the visualization of the data. I think the authors have done a great job in presenting this complex dataset, but there are still some smaller tweaks that could be used to increase the legibility of the presented data.

First and perhaps foremost, a better definition of the swimming pattern subsets is needed. I have no problem understanding the main behavioral types, but whereas the color codes for these suggest that there is continuous variance within each pattern, it is not clear (at least to me), what particular aspect(s) of the behaviors vary. Also, whereas the sidebars/legends suggest a continuum within these behaviors, the bar charts themselves clearly present binned data. I did not find a detailed description of how the binning was done. As this has been - according the Methods section - a manual process, more clarity about the details of the binning would be welcome. I would also suggest using binned color codes for the legends as well.

Done, in Results and Methods. We hope it is now clear that there is no “continuum”, rather multiple combinations of discrete swimming patterns. The gradient aspect in color code in figures has been removed to avoid the idea of continuum. According to the chosen color code, WF is in red, R in blue, T in yellow and C in green. Then, combination are represented by colors in between, for example, R+WF is purple. We have now added a full color code description for the swimming patterns and their combinations in a new Supplemental Figure 7 (associated to Methods).

Also, to better explain the definition of the swimming patterns and the graphical representation, it now reads (in Methods):

“The determination of baseline swimming patterns and swimming patterns after odor injection was performed manually based on graphical representations such as in Figure 2A or Figure 3A. Four distinctive baseline behaviors clearly emerged: random swim (R; defined as haphazard swimming with no clear pattern, covering entirely or partly the surface of the arena), wall following (WF; defined as the fish continuously following along the 4 sides of the box and turning around it, in a clockwise or counterclockwise fashion), large or small circles (C; self explanatory), and thigmotactism (T, along the X- or the Y-axis of the box; defined as the fish swimming back and forth along one of the 4 sides of the box). On graphical representations of swimming pattern distributions, we used the following color code: R in blue, WF in red, C in green, T in yellow. Of note, many fish swam according to combination(s) of these four elementary swimming patterns (see descriptions in the legends of Supplemental figures, showing many examples). To fully represent the diversity and the combinations of swimming patterns used by individual fish, we used an additional color code derived from the “basic” color code described above and where, for example R+WF is purple. The complete combinatorial color code is shown in Suppl. Fig7.”

It would be also easier to comprehend the stacked bar charts, presenting the particular swimming patterns in each population, if the order of different swimming patterns was the same for all the plots (e.g. the frequency of WF always presented at the bottom, R on the top, and C and T in the middle). This would bring consistency and would highlight existing differences between SF, CF, and F2s. Furthermore, such a change would also make it much easier to see (and compare) shifts in behaviors.

We have thought a lot on how to best represent the distributions of swimming patterns in graphs such as Fig 2B and others. The difficulty is due to the existence of many combinations, which are never the same in different plots/conditions because the individual fish tested are different. We decided to keep it as it currently stands, because we think re-doing all the graphs and figures would not significantly improve the representation. In fact, we think that the differences between morphs (dominant blue in SF, dominant red in CF) and between conditions (bar charts next to each other) are easy to interpret at first glance in the vast majority of cases. Moreover, they are now completed by CA analyses (Suppl Figure 8).

While the color coding of the timeline in the "3D" plots presented for individual animals is a nice feature, at the moment it is slightly confusing, as the authors use the same color palette as for the stacked bar charts, representing the proportionality of the particular swimming patterns. As the y-axis is already representing "time" here, the color coding is not even really necessary. If the authors would like to use a color scheme for aesthetic reasons, I would suggest using another palette, such as "grey" or "viridis".

We would like to keep the graphical aspect of our figures as they are, for aesthetic reasons. To avoid confusion with stacked bar chart color code, we have added a sentence in Methods and in the legend of Figure 2, where the colors first appear:

“The complete combinatorial color code is shown in Suppl. Figure 7. Of note, in all figures, the swimming pattern color code does not relate whatsoever with the time color code used in the 2D plus time representation of swimming tracks such as in Figure 2A”.

I would also suggest changing the boxplots to violin-plots. Figure 7 clearly shows bimodality for F2 scores (something, as the authors themselves note, not entirely surprising given the probably poligenic nature of the trait), but looking at SF and CF scores I think there are also clear hints for non-normal distributions. If non-normal distribution of traits is the norm, violin-plots would capture the variance in the data in a more digestible way. (The existence of differently behaving cohorts within the population of both SF and CF forms would also help to highlight the large pre-existing variance, something that was probably exploited by natural selection as well, as mentioned briefly in the Discussion by the authors, too.)

The bimodal distribution of scores shown by F2s in Figure 7B is indeed probably due to the polygenic nature of the trait. However, such distribution is rather the exception than the norm. Moreover, the boxplot representations we have used throughout figures include all the individual points, and outliers can be identified as they have the fish ID number next to them. This allows the reader to grasp the variance of the data. Again, redoing all graphs and figures would constitute a lot of work, for little gain in term of conveying the results. Therefore, we choose not to change the boxplot for violin plots.

The summary data of individual scores in Table 1B shows some intriguing patterns, that warrant a bit further discussion, in my opinion. For example, we can see opposite trends in scores of SF and CF forms with increasing alanine concentration. Is there an easy explanation for this? Also, in the case of serine, the CF scores do not seem to respond in a dose-dependent manner and puzzlingly at 10^(-3)M serine concentration F2 scores are above those of both grandparental populations.

That is true. However, we have no simple explanation for this. To begin responding to this question, we have now performed full dose/responses expts for alanine (concentrations tested from 10-2M to 10-10M on cavefish; confirm that CF are bona fide “alanine specialists”) and for serine (10-2M to 104M tested on both morphs; confirm that both morphs respond well to this amino acid). These complementary results are now included in text and figures (partially) and in the summary table 1.

If anything is known about this, I would also welcome some discussion on how thigmotactic behavior, a marker of stress in SF, could have evolved to become the normal behavior of CF forms, with lower cortisol levels and, therefore lower anxiety.

We actually think thigmotactism is a marker of stress in both morphs. See Pierre et al, JEB 2020, Figure S3A: in both SF and CF thigmotaxis behavior decreases after long habituation times. In our hands, the only difference between the two morphs is that surface fish (at 5 month of age) express stress by thigmotactism but also freezing and rapid erratic movements, while cavefish have a more restricted stress repertoire.

This is why in the present paper we have carefully made the distinction between thigmotactism (= possible stress readout) and wall following (= exploratory behavior). Our finding that WF and large circles confers better olfactory response scores to cavefish is in strong support of the different nature of these two swimming patterns. Then, why is swimming along the 4 walls of a tank fundamentally different from swimming along one wall? The question is open, although the number of changes of direction is probably an important parameter: in WF the fish always swims forward in the same direction, while in T the fish constantly changes direction when reaching the corner of the tank – which is similar to erratic swim in stressed surface fish.

Finally two smaller suggestions:

• When referring to multiple panels on the same figure it would be better to format the reference as "Figure 4D-G" instead of "Figure 4DEFG";

Done

• On page 4, where the introduction reads as "although adults have a similar olfactory rosette with 2025 lamellae", in my opinion, it would be better to state that "while adults of the two forms have a similar olfactory rosette with 20-25 lamellae".

Done

Reviewer #3 (Recommendations For The Authors):

Consider moving Figure 3 to be a supplement of Figure 4. This figure shows a water control and therefore best supplements the alanine experiment.

We would like to keep this figure as a main figure: we consider it very important to establish the validity of our behavioral setup at the beginning of the ms, and to establish that in all the following figures we are recording bona fide olfactory responses.

"sensory changes in mecano-sensory and gustatory systems " - mechano-sensory.

Done

Figure 2 legend: "(3) the right track is the 3D plus time (color-coded)" - shouldn't it be 2D plus time or 3D (x,y, time).

True! Thanks for noting this, corrected.

Figure 4 legend "E, Change in swimming patterns" should be H.

Done

"suggesting that their detection threshold for serine is lower than for alanine" - higher?

Done

In the behavioural plots, I assume that the "mean position" value represents the mean position along the X-axis of the chamber - this should be clarified and the axis label updated accordingly.

That is correct and has been updated in Methods and Figures and legends.

"speed, back and forth trips in X and Y, position and pattern changes (see Methods; Figure 7A)." - here it would be helpful to add an explanation like "to define an olfactory score for individual fish."

This has been changed in Results and more detailed explanations on score calculations are now given in Methods.

"possess enhanced mecanosensory lateral line" - mechanosensory.

Done

eLife assessment

In this important paper, Blin and colleagues develop a high-throughput behavioral assay to test spontaneous swimming and olfactory preference in individual Mexican cavefish larvae. The authors present compelling evidence that the surface and cave morphs of the fish show different olfactory preferences and odor sensitivities and that individual fish show substantial variability in their spontaneous activity that is relevant for olfactory behaviour. The paper will be of interest to neurobiologists working on the evolution of behaviour, olfaction, and the individuality of behaviour.

Joint Public Review:

Summary:

The paper explores chemosensory behaviour in surface and cave morphs and F2 hybrids in the Mexican cave fish Astyanax mexicanus. The authors develop a new behavioural assay for the long-term imaging of individual fish in a parallel high-throughput setup. The authors first demonstrate that the different morphs show different basal exploratory swimming patterns and that these patterns are stable for individual fish. Next, the authors test the attraction of fish to various concentrations of alanine and other amino acids. They find that the cave morph is a lot more sensitive to chemicals and shows directional chemotaxis along a diffusion gradient of amino acids. Surface fish, although can detect the chemicals, do not show marked chemotaxis behaviour and have an overall lower sensitivity. These differences have been reported previously but the authors report longer-term observations on many individual fish of both morphs and their F2 hybrids. The data also indicate that the observed behaviour is a quantitative genetic trait. The approach presented will allow the mapping of genes contribution to these traits. The work will be of general interest to behavioural neuroscientists and those interested in olfactory behaviours and the individual variability in behavioural patterns.

Strengths:

The authors provide a large dataset of swimming behaviour for surface fish and cave fish and also their F2 hybrids, demonstrating large differences in chemosensory behaviour and indicating that this is a quantitative genetic trait.

One strength of the paper is the development of a new and improved setup for the behavioural imaging of individual fish for extended periods and under chemosensory stimulation. The authors show that cave fish need up to 24 h of habituation to display a behavioural pattern that is consistent and unlikely to be due to the stressed state of the animals. The setup also uses relatively large tanks that allows the build-up of chemical gradients.

With their new system, the authors could generate cleaner results without mechanical disturbances. The authors characterize multiple measurements to score the odour response behaviours and also developed a new personality analysis. Their conclusion that cave fish evolved as a specialist to sense alanine and histidine among 6 tested amino acids was well supported by their data.

Weaknesses:

Further work will be needed to pinpoint the nature of the genetic changes and neurobiological mechanisms that underlie the differences between the two forms and the large individual variation of behaviours.<br /> The authors did not measure the concentrations of alanine and other amino acids in the local cave water and surface water.

Author response:

Reviewer #1 (Public Review):

(1) Deleting ICP34.5 from the HSV construct has a very strong effect on HIV reactivation. Why is no eGFP readout given in Figure 1C as for WT HSV? The mechanism underlying increased activation by deleting ICP34.5 is only partially explored. Overexpression of ICP34.5 has a much smaller effect (reduction in reactivation) than deletion of ICP34.5 (strong activation); so the story seems incomplete.

Thank you for your comment. (1) In Figure 1c, "HSV-wt" refers to the virus rescued from pBAC—GFP-HSV (as mentioned in the “Method” section), which carries GFP itself. Therefore, detecting GFP cannot distinguish between HSV infection and HIV reactivation. Hence, we assess the reactivation effect by measuring the mRNA levels of HIV LTR. (2) Our data indicate that overexpression of ICP34.5 inhibits the reactivation of the HIV latent reservoir, but this effect is not equivalent to the activation observed in HSV-1 with ICP34.5 deletion. There are some possible reasons: one is that the overexpression of ICP34.5 by lentivirus is randomly integrated into the genome of J-Lat cell line, which will potentially activate HIV latency to some extent. The other is that ICP34.5 mainly inhibited HIV reactivation through modulation of host NF-κB or HSF1 pathways, while PMA, TNF-a, and HSV-1 with deleted ICP34.5 can reactivate HIV latency by other mechanisms that have yet to be determined. Thereby, exerting a synergistic small inhibitory effect. We will further discuss this issue in the revised version. Thank you.

(2) No toxicity data are given for deleting ICP34.5. How specific is the effect for HIV reactivation? An RNA seq analysis is required to show the effect on cellular genes.

Thank you for your comment. We plan to conduct several experiments to demonstrate a reduction in HSV-1 replication after ICP34.5 deletion: (1) Detect the growth curve of HSV-1 deleted with ICP34.5 in Vero cells. The virus growth curve of HSV-1 with deleted ICP34.5 may be lower than that of wild-type HSV-1, which could demonstrate a reduction in HSV-1 replication after ICP34.5 deletion. (2) Detect the level of inflammatory factors in tumor cells after infection with HSV-1 deleted with ICP34.5.

We believe that the effect is specific, as we previously tested poxviruses and adenoviruses and found no activation of the latent reservoir. We consider the activation observed with HSV-1 virus and HSV-1 with deleted ICP34.5 to be specific. We will supplement relevant data in the revised version.

In addition, we will provide the corresponding RNA-seq data to assess its effect on cellular genes.

(3) The primate groups are too small and the results to variable to make averages. In Figure 5, the group with ART and saline has two slow rebounders. It is not correct to average those with a single quick rebounder. Here the interpretation is NOT supported by the data.

We agree with you that this is a pilot study of limited numbers of rhesus macaques. There were only 3 monkeys per group in this study, but our results were encouraging. Although the number of macaques was relatively limited, these nine macaques were distributed very carefully based on age, sex, weight and genotype. All SIV-infected macaques used in this study had a long history of SIV infection and had several courses of ART therapy, which mimics treatment of chronic HIV-1 infection in humans. These macaques were infected with SIVmac239 for more than 5 years, and highly pathogenic SIV-infected macaques have been well-validated as a stringent model to recapitulate HIV-1 pathogenesis and persistence during ART therapy in humans. Indeed, in our rhesus model, ART treatment effectively suppressed SIV infection to undetectable levels in plasma, and upon ART discontinuation, virus rapidly rebounded, which is very similar with that in ART-treated HIV patients. Our further studies will be expanded the scale of animals and then to preclinical and clinical study in our next projects. Thank you for your understanding.

Discussion

HSV vectors are mainly used in cancer treatment partially due to induced inflammation. Whether these are suitable to cure PLWH without major symptoms is a bit questionable to me and should at least be argued for.

We will provide more data about the safety assessment of HSV-1 vector in SIV-infected macaques, and also further discuss the potential of inflammatory HSV vector in PLWH in the revised manuscript.

Reviewer #2 (Public Review):

(1) While the mechanism of ICP34.5 interaction and modulation of the NF-kB and HSF1 pathways are shown, this only proves ICP34.5 interactions but does not give away the mechanism of how the HSV-deltaICP-34.5 vector purges HIV-1 latency. What other components of the vector are required for latency reversal? Perhaps serial deletion experiments of the other ORFs in the HSV-deltaICP-34.5 vector might be revealing.

We agree with your suggestion. In fact, we are currently further exploring some viral genes of HSV-1 that play a role in activation. We have found that the ICP0 gene of HSV-1 virus can activate HIV, and the specific mechanism is under investigation.

(2) The efficacy of the HSV vaccine vectors was evaluated in Rhesus Macaque model animals. Animals were chronically infected with SIV (a parent of HIV), treated with ART, challenged with bi-functional HSV vaccine or controls, and discontinued treatment, and the resulting virus burden and immune responses were monitored. The animals showed SIV Gag and Env-specific immune responses, and delayed virus rebound (however rebound is still there), and below-detection viral DNA copies. What would make a more convincing argument to this reviewer will be data to demonstrate that after the bi-functional vaccine, the animals show overall reduction in the number of circulating latent cells. The feasibility of obtaining such a result is not clearly demonstrated.

Thank you for your suggestion. We will plan to conduct IPDA experiments to further supplement data on the overall reduction in circulating latent cell numbers in animals.

(3) The authors state that the reduced virus rebound detected following bi-functional vaccine delivery is due to latent genomes becoming activated and steady-state neutralization of these viruses by antibody response. This needs to be demonstrated. Perhaps cell-culture experiments from specimens taken from animals might help address this issue. In lab cultures one could create environments without antibody responses, under these conditions one would expect a higher level of viral loads to be released in response to the vaccine in question.

We plan to use primary cells for related experiments to further validate the results of the cell experiments.

(4) How do the authors imagine neutralizing HIV-1 envelope epitopes by a similar strategy? A discussion of this point may also help.

Thank you for your comments. In fact, our study adopts the "shock and kill" strategy, with a focus on the "kill" aspect leaning towards T-cell therapy. Although the vaccine in the paper also utilizes Env antigen, we believe these antibodies are insufficient for neutralizing the mutated SIV virus. We strongly agree with your suggestion that in HIV/AIDS treatment, effective T-cell killing combined with broad-spectrum neutralizing antibodies would be more effective. This aligns with our findings, as our treatment has partially delayed viral rebound but with a relatively short duration of suppression. This may indicate insufficient killing activity. In future research, we will further consider the role of broad-spectrum neutralizing antibodies. Our revised manuscript will elaborate on this in the discussion section.

(5) I thought the empty HSV-vector control also elicited somewhat delayed kinetics in virus rebound and neutralization, can the authors comment on why this is the case?

We agree with you that the HSV-1 empty vector does exhibit somewhat a delayed rebound. The reason is that our treatment simultaneously utilizes both the HSV vector vaccine and ART therapy. Although the empty HSV-vector cannot elicit SIV-specific CTL response, it effectively activates the latent SIV reservoirs and then these activated virions can be partially killed by ART, Therefore, even without carrying antigens, the slight delay may be achieved.

Reviewer #1 (Public Review):

Summary:

The authors constructed a novel HSV-based therapeutic vaccine to cure SIV in a primate model. The novel HSV vector is deleted for ICP34.5. Evidence is given that this protein blocks HIV reactivation by interference with the NFkappaB pathway. The deleted construct supposedly would reactivate SIV from latency. The SIV genes carried by the vector ought to elicit a strong immune response. Together the HSV vector would elicit a shock and kill effect. This is tested in a primate model.

Strengths and weaknesses:

(1) Deleting ICP34.5 from the HSV construct has a very strong effect on HIV reactivation. Why is no eGFP readout given in Figure 1C as for WT HSV? The mechanism underlying increased activation by deleting ICP34.5 is only partially explored. Overexpression of ICP34.5 has a much smaller effect (reduction in reactivation) than deletion of ICP34.5 (strong activation); so the story seems incomplete.

(2) No toxicity data are given for deleting ICP34.5. How specific is the effect for HIV reactivation? An RNA seq analysis is required to show the effect on cellular genes.

(3) The primate groups are too small and the results to variable to make averages. In Figure 5, the group with ART and saline has two slow rebounders. It is not correct to average those with a single quick rebounder. Here the interpretation is NOT supported by the data.

Discussion

HSV vectors are mainly used in cancer treatment partially due to induced inflammation. Whether these are suitable to cure PLWH without major symptoms is a bit questionable to me and should at least be argued for.

eLife assessment

In this useful study, the authors tested a novel approach to eradicate the HIV reservoir by constructing a herpes simplex virus (HSV)-based therapeutic vaccine. The approach was tested in experimental infections of chronically SIV-infected, antiretroviral therapy (ART)-treated macaques with extent of rebound after ART interruption as a measure of the size of the HIV reservoir. While mean viremia at rebound was lower in the HSV vaccine-treated group, the evidence presented appear to be be incomplete because the group size was small and the viral load at rebound was highly variable.

Reviewer #2 (Public Review):

Summary:

In this article, Wen et. al. describe the development of a 'proof-of-concept' bi-functional vector based on HSV-deltaICP-34.5's ability to purge latent HIV-1 and SIV genomes from cells. They show that co-infection of latent J-lat T-cell lines with an HSV-deltaICP-34.5 vector can reactivate HIV-1 from a latent state. Over- or stable expression of ICP 34.5 ORF in these cells can arrest latent HIV-1 genomes from transcription, even in the presence of latency reversal agents. ICP34.5 can co-IP with- and de-phosphorylate IKKa/b to block its interaction with NF-k/B transcription factor. Additionally, ICP34.5 can interact with HSF1 which was identified by mass-spec. Thus, the authors propose that the latency reversal effect of HSV-deltaICP-34.5 in co-infected JLat cells is due to modulatory effects on the IKKa/b-NF-kB and PP1-HSF-1 pathway.

Next, the authors cleverly construct a bifunctional HSV-based vector with deleted ICP34.5 and 47 ORFs to purge latency and avoid immunological refluxes, and additionally, expand the application of this construct as a vaccine by introducing SIV genes. They use this 'vaccine' in mouse models and show the expected SIV-immune responses. Experiments in rhesus macaques (RM), further elicit the potential for their approach to reactivate SIV genomes and at the same time block their replication by antibodies. What was interesting in the SIV experiments is that the dual-functional vector vaccine containing sPD1- and SIV Gag/Env ORFs effectively delayed SIV rebound in RMs and in some cases almost neutralized viral DNA copy detection in serum. Very promising indeed, however, there are some questions I wish the authors had explored to get answers to, detailed below.

Overall, this is an elegant and timely work demonstrating the feasibility of reducing virus rebound in animals, with the potential to expand to clinical studies. The work was well-written, and sections were clearly discussed.

Strengths:

The work is well designed, rationale explained, and written very clearly for lay readers.

Claims are adequately supported by evidence and well-designed experiments including controls.

Weaknesses:

(1) While the mechanism of ICP34.5 interaction and modulation of the NF-kB and HSF1 pathways are shown, this only proves ICP34.5 interactions but does not give away the mechanism of how the HSV-deltaICP-34.5 vector purges HIV-1 latency. What other components of the vector are required for latency reversal? Perhaps serial deletion experiments of the other ORFs in the HSV-deltaICP-34.5 vector might be revealing.

(2) The efficacy of the HSV vaccine vectors was evaluated in Rhesus Macaque model animals. Animals were chronically infected with SIV (a parent of HIV), treated with ART, challenged with bi-functional HSV vaccine or controls, and discontinued treatment, and the resulting virus burden and immune responses were monitored. The animals showed SIV Gag and Env-specific immune responses, and delayed virus rebound (however rebound is still there), and below-detection viral DNA copies. What would make a more convincing argument to this reviewer will be data to demonstrate that after the bi-functional vaccine, the animals show overall reduction in the number of circulating latent cells. The feasibility of obtaining such a result is not clearly demonstrated.

(3) The authors state that the reduced virus rebound detected following bi-functional vaccine delivery is due to latent genomes becoming activated and steady-state neutralization of these viruses by antibody response. This needs to be demonstrated. Perhaps cell-culture experiments from specimens taken from animals might help address this issue. In lab cultures one could create environments without antibody responses, under these conditions one would expect a higher level of viral loads to be released in response to the vaccine in question.

(4) How do the authors imagine neutralizing HIV-1 envelope epitopes by a similar strategy? A discussion of this point may also help.

(5) I thought the empty HSV-vector control also elicited somewhat delayed kinetics in virus rebound and neutralization, can the authors comment on why this is the case?

Author response:

We would like to thank the eLife Editors and Reviewers for their positive assessment and constructive comments, and for the opportunity to revise our manuscript. We greatly appreciate the Reviewers’ recommendations and believe that they will further improve our manuscript.

In revising the manuscript, our primary focus will be enhancing the clarity surrounding testing procedures and addressing corrections for multiple comparisons. Additionally, we intend to offer more explicit information about the statistical tests employed, along with the details about the number of models/comparisons for each test. We will also include an extended discussion on potential limitations of the dopaminergic receptor mapping methods used, addressing the Reviewers’ comments relating to the quality of PET imaging with different dopaminergic tracers in mesiotemporal regions such as the hippocampus. While the code used for connectopic mapping is publicly available through the ConGrads toolbox, we will provide the additional code we have used for data processing and analysis, visualization of hippocampal gradients, and the cortical projections. The data used in the current study is not publicly available due to ethical considerations concerning data sharing, but can be shared upon reasonable request from the senior author. Additional plans include clarifying and discussing which findings were successfully replicated, and addressing Reviewers’ suggestions for using other openly available cohorts for replication, and implementing alternative coordinate systems to quantify connectivity change along gradients.

eLife assessment

This fundamental work demonstrates the importance of considering overlapping modes of functional organization (i.e. gradients) in the hippocampus, showing associations between with aging, dopaminergic receptor distribution and episodic memory. The evidence supporting the conclusions is solid, although some clarifications about testing procedures and a discussion of the limitations of the dopaminergic receptor mapping techniques employed should be provided along with analysis code. The work will be of broad interest to basic and clinical neuroscientists.

Reviewer #1 (Public Review):

The authors studied how hippocampal connectivity gradients across the lifespan, and how these relate to memory function and neurotransmitter distributions. They observed older age with less distinct transitions and observed an association between gradient de-differentiation and cognitive decline.

This is overall an innovative and interesting study to assess gradient alterations across the lifespan and its associations to cognition.

The paper is well-written, and the methods appear sound and thoughtful. There are several strengths, including the inclusion of two independent cohorts, the use of gradient mapping and alignment techniques, and an overall sound statistical and analysis framework. There are several areas for potential improvements in the paper, and these are listed below:

(1) The reported D1 associations appear a bit post-hoc in the current work and I was unclear why the authors specifically focussed on dopamine here, as other transmitter systems are similar present at the level of the hippocampus and implicated in aging.

Moreover, the authors may be aware that multiple PET tracers are somewhat challenged in the mesiotemporal region. Is this the case for the D1 receptor as well? The hippocampus is a small and complex structure, and PET more of a low res technique so one would want to highlight and discuss the limitations of the correlations with PET maps here and/or evaluate whether the analysis adds necessary findings to the study.

From my (perhaps somewhat biased) perspective, it might be valuable to instead or in addition look at measures of hippocampal microstructure and how these relate to the functional aging effects. This could be done, if available, using data from the same subjects (eg based on quantitative MRI contrasts and/or structural MRI) and/or using contextualization findings as implemented in eg hippomaps.readthedocs.io

(2) Can the authors clarify why they did not replicate based on cohorts that are more widely used in the community and open access, such as CamCAN and/or HCP-Aging? It might connect their results with other studies if an attempt was made to also show that findings persist in either of these repositories.

(3) The authors applied TSM and related these parameters to topographic changes in the gradients. I was wondering whether and how such an approach controls for autocorrelation present in both the PET map and gradients. Could the authors clarify?

(4) The TSM approach quantifies the gradients in terms of x/y/z direction in a cartesian coordinate system. Wouldn't a shape intrinsic coordinate system in the hippocampus also be interesting, and perhaps even be more efficient to look at here (see eg DeKraker 2022 eLife or Paquola et al 2020 eLife)?

Reviewer #2 (Public Review):

Summary:

This paper derives the first three functional gradients in the left and right hippocampus across two datasets. These gradient maps are then compared to dopamine receptor maps obtained with PET, associated with age, and linked to memory. Results reveal links between dopamine maps and gradient 2, age with gradients 1 and 2, and memory performance.

Strengths:

This paper investigates how hippocampal gradients relate to aging, memory, and dopamine receptors, which are interesting and important questions. A strength of the paper is that some of the findings were replicated in a separate sample.

Weaknesses

The paper would benefit from added clarification on the number of models/comparisons for each test. Furthermore, it would be helpful to clarify whether or not multiple comparison correction was performed and - if so - what type or - if not - to provide a justification. The manuscript would furthermore benefit from code sharing and clarifying which results did/did not replicate.

Reviewer #3 (Public Review):

Summary:

In this study, the authors analyzed the complex functional organization of the hippocampus using two separate adult lifespan datasets. They investigated how individual variations in the detailed connectivity patterns within the hippocampus relate to behavioral and molecular traits. The findings confirm three overlapping hippocampal gradients and reveal that each is linked to established functional patterns in the cortex, the arrangement of dopamine receptors within the hippocampus, and differences in memory abilities among individuals. By employing multivariate data analysis techniques, they identified older adults who display a hippocampal gradient pattern resembling that of younger individuals and exhibit better memory performance compared to their age-matched peers. This underscores the behavioral importance of maintaining a specific functional organization within the hippocampus as people age.

Strengths:

The evidence supporting the conclusions is overall compelling, based on a unique dataset, rich set of carefully unpacked results, and an in-depth data analysis. Possible confounds are carefully considered and ruled out.

Weaknesses:

No major weaknesses. The transparency of the statistical analyses could be improved by explicitly (1) stating what tests and corrections (if any) were performed, and (2) justifying the elected statistical approaches. Further, some of the findings related to the DA markers are borderline statistically significant and therefore perhaps less compelling but they line up nicely with results obtained using experimental animals and I expect the small effect sizes to be largely related to the quality and specificity of the PET data rather than the derived functional connectivity gradients.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript "comparative transcriptomics reveal a novel tardigrade specific DNA binding protein induced in response to ionizing radiation" aims to provide insights into the mediators and mechanisms underlying tardigrade radiation tolerance. The authors start by assessing the effect of ionizing radiation (IR) on the tardigrade lab species, H. exemplaris, as well as the ability of this organism to recover from this stress - specifically, they look at DNA double and single-strand breaks. They go on to characterize the response of H. exemplaris and two other tardigrade species to IR at the transcriptomic level. Excitingly, the authors identify a novel gene/protein called TDR1 (tardigrade DNA damage response protein 1). They carefully assess the induction of expression/enrichment of this gene/protein using a combination of transcriptomics and biochemistry - even going so far as to use a translational inhibitor to confirm the de novo production of this protein. TDR1 binds DNA in vitro and co-localizes with DNA in tardigrades.

Reverse genetics in tardigrades is difficult, thus the authors use a heterologous system (human cells) to express TDR1 in. They find that when transiently expressed TDR1 helps improve human cell resistance to IR.

This work is a masterclass in integrative biology incorporating a holistic set of approaches spanning next-gen sequencing, organismal biology, biochemistry, and cell biology. I find very little to critique in their experimental approaches.

Strengths:

(1) Use of trans/interdisciplinary approaches ('omics, molecular biology, biochemistry, organismal biology)

(2) Careful probing of TDR1 expression/enrichment

(3) Identification of a completely novel protein seemingly involved in tardigrade radio-tolerance.

(4) Use of multiple, diverse, tardigrade species of 'omics comparison.

Weaknesses:

(1) No reverse genetics in tardigrades - all insights into TDR1 function from heterologous cell culture system.

(2) Weak discussion of Dsup's role in preventing DNA damage in light of DNA damage levels measured in this manuscript.

(3) Missing sequence data which is essential for making a complete review of the work.

Overall, I find this to be one of the more compelling papers on tardigrade stress-tolerance I have read. I believe there are points still that the authors should address, but I think the editor would do well to give the authors a chance to address these points as I find this manuscript highly insightful and novel.

We thank the reviewer for his comments.

We agree that it will be important to further investigate the role of Dsup in radio-tolerance. We briefly mentioned this point in the discussion (p14). Our findings show that tardigrades undergo DNA damage at levels roughly similar to radio-sensitive organisms and therefore support a major role for DNA repair in the maintenance of genome integrity after exposure to IR. Nevertheless, we believe that more precise quantification of DNA damage may still reveal a contribution of genome protection to radio-tolerance of tardigrades compared to radio-sensitive organisms. Dsup loss of function experiments in tardigrades would clearly be the best way to assess this possibility. In the absence of experiments directly addressing the function of Dsup, we prefer to refrain from drawing any firm conclusion on prevention of DNA damage by Dsup and thus to keep a more open position. In any case, as discussed in the text, we note that Dsup has only been reported in Hypsibioidea and other molecular players, such as TDR1, are likely involved in radio-tolerance in other tardigrade species.

The sequence data can be accessed at the NCBI SRA database with Bioproject ID PRJNA997229.

Reviewer #3 (Public Review):

Summary:

This paper describes transcriptomes from three tardigrade species with or without treatment with ionizing radiation (IR). The authors show that IR produces numerous single-strand and double-strand breaks as expected and that these are substantially repaired within 4-8 hours. Treatment with IR induces strong upregulation of transcripts from numerous DNA repair proteins including Dsup specific to the Hypsobioidea superfamily. Transcripts from the newly described protein TDR1 with homologs in both Hypsibioidea and Macrobiotoidea supefamilies are also strongly upregulated. They show that TDR1 transcription produces newly translated TDR1 protein, which can bind DNA and co-localizes with DNA in the nucleus. At higher concentrations, TDR appears to form aggregates with DNA, which might be relevant to a possible function in DNA damage repair. When introduced into human U2OS cells treated with bleomycin, TDR1 reduces the number of double-strand breaks as detected by gamma H2A spots. This paper will be of interest to the DNA repair field and to radiobiologists.

Strengths:

The paper is well-written and provides solid evidence of the upregulation of DNA repair enzymes after irradiation of tardigrades, as well as upregulation of the TRD1 protein. The reduction of gamma-H2A.X spots in U2OS cells after expression of TRD1 supports a role in DNA damage.

Weaknesses:

Genetic tools are still being developed in tardigrades, so there is no mutant phenotype to support a DNA repair function for TRD1, but this may be available soon.

We thank the reviewer for his comments.

Reviewer #4 (Public Review):

The manuscript brings convincing results regarding genes involved in the radio-resistance of tardigrades. It is nicely written and the authors used different techniques to study these genes. There are sometimes problems with the structure of the manuscript but these could be easily solved. According to me, there are also some points which should be clarified in the result sections. The discussion section is clear but could be more detailed, although some results were actually discussed in the results section. I wish that the authors would go deeper in the comparison with other IR-resistant eucaryotes. Overall, this is a very nice study and of interest to researchers studying molecular mechanisms of ionizing radiation resistance.

I have two small suggestions regarding the content of the study itself.

(1) I think the study would benefit from the analyses of a gene tree (if feasible) in order to verify if TDR1 is indeed tardigrade-specific.

(2) It would be appreciated to indicate the expression level of the different genes discussed in the study, using, for example, transcript per millions (TPMs).Recommendations for the authors: please note that you control which revisions to undertake from the public reviews and recommendations for the authors

We thank the reviewer for his comments.

(1) To identify TDR1 homologous sequences in non-tardigrade species, we conducted extensive homology searches using multiple homology-based approaches (Blastp and Diamond against the NCBI non-redundant protein sequences (nr) database and hmmsearch against the EBI reference proteomes), which failed to identify TDR1 homologs in non-tardigrade ecdysozoans, thus strongly supporting that TDR1 is indeed tardigrade-specific.

To be clearer in the manuscript, we now state the absence of hits for TDR1 in non-tardigrade ecdysozoans. Given the absence of homologs in non-tardigrade species, it is not possible to make a gene tree with non-tardigrade species.

(2) To further document expression levels (which were already available from the Tables in the initial submission), we added MAplots (representing log2foldchange and logNormalized read counts) in the supplementary materials (Supp Figure 3 and Supp Figure 8). These additional figures clearly document that the DNA repair genes discussed in the main text and TDR1 are highly expressed genes after IR and after Bleomycin treatment.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

We thank the reviewer for his comments.

(1) It has always seemed strange to me that tardigrades accumulate just as much DNA damage as any other organism when irradiated and yet their Dsup protein is supposed to shield and protect their DNA from damage. Perhaps this is an appropriate time for this idea to be reconsidered given the Dsup was NOT induced by IR in this study and the authors found that their animals incurred just as much damage as other biological systems. While Dsup is clearly not the focus of this manuscript, it is the protein most associated with tardigrade radio-tolerance and I would argue this new paper would call into question previous conclusions made about Dsup.

We agree that it will be important to further investigate the role of Dsup in radio-tolerance. We briefly mentioned this point in the discussion (p14). Our findings show that tardigrades undergo DNA damage at levels roughly similar to radio-sensitive organisms and therefore support a major role for DNA repair in the maintenance of genome integrity after exposure to IR. Nevertheless, we believe that more precise quantification of DNA damage may still reveal a contribution of genome protection to radio-tolerance of tardigrades compared to radio-sensitive organisms. Dsup loss of function experiments in tardigrades would clearly be the best way to assess this possibility. In the absence of experiments directly addressing the function of Dsup, we prefer to refrain from drawing any firm conclusion on prevention of DNA damage by Dsup and thus to keep a more open position. In any case, as discussed in the text, we note that Dsup has only been reported in Hypsibioidea and other molecular players, such as TDR1, are likely involved in radio-tolerance in other tardigrade species.

(2) While reverse genetics are difficult in tardigrades, they are not impossible, and RNAi can be used to good effect in these animals. In fact several authors on this manuscript have used RNAi to examine the necessity of genes in tardigrade stress tolerance in the past. Was an attempt made to RNAi TDR1? If not, why? With the large amount of work that the authors put into showing the sufficiency of TDR1 for increasing radiotolerance in cell culture, one would think looking at necessity in tardigrades would be of great interest. If RNAi was performed, what were the results? Even a negative result here is informative since a protein can be sufficient but not necessary for a function - if this were the case it would mean tardigrades have some redundant mechanism(s) for surviving radiation exposure beyond TDR1.

We have attempted RNAi experiments targeting TDR1 or a mix of DNA repair genes (including XRCC5) and examined response to a bleomycin treatment of 2 weeks. Unfortunately, we could not distinguish any difference between uninjected animals and animals injected with TDR1 dsRNAs , or the mix of DNA repair genes dsRNAs. We concluded that, bleomycin treatment, that we used because it is much easier to perform than irradiation, was perhaps not the best way to assay a potential impact of RNAi on survival since it required long term treatment for several days during which the effect of RNAi may have waned. Another attempt was therefore made injecting with TDR1 or control GFP dsRNAs and exposing animals to a 2000Gy IR treatment. We noticed that the viability was lower after injection with GFP dsRNAs than with TDR1 dsRNAs (likely due to problems we had with the injection needle during injections). The next day, animals were irradiated and we observed after 24h that animals injected with GFP dsRNAs exhibited higher lethality rates than animals injected with TDR1 dsRNAs or uninjected animals. We found that this set of experiments were not conclusive. Our current experimental set up will make it difficult to distinguish lethality due to injections from lethality due to potentially decreased resistance to IR. In particular, many key controls are difficult to make (in particular, we could not confirm the efficiency of target gene knockdown, as it is very challenging given the low amount of biological material available and the poor expression of these genes without irradiation). From a practical point of view, performing these experiments is thus very challenging. We nevertheless agree that, in future work, further experimentation is needed to examine the impact of knock-down by RNAi of TDR1 or of other genes such as DNA repair genes or Dsup, in tardigrade DNA repair and survival after IR. Gene knock-out with CRISPR-Cas9 is a very promising alternative to RNAi given that studies in mutant lines will eliminate the confounding effect of lethality due to injections.

(3) Regarding the U2OS experiments. I have several questions/points of clarification:

a. Were survival/proliferation levels tested or only H2AX foci? I think that showing decreased H2AX foci (fewer double-stranded breaks) correlates with higher survival rates would be important.

In the experiments reported in Figure 6, cells were transiently transfected with expression vectors and we did not examine the impact on survival rates. U2OS cells are resistant to high doses of Bleomycin and testing survival would require longer exposure at much higher concentrations (Buscemi et al, 2014, PMID: 25486478). In order to try and better address an impact on cell survival, we therefore generated populations of cells stably expressing the candidate tardigrade proteins fused to GFP. Despite trying different experiment conditions for treatment with Bleomycin, we could not detect a reproducibly significant benefit on cell survival for any of the tardigrade proteins tested, including RvDsup which was used as a positive control (since it was previously reported to improve cell survival in response to X-rays). One possibility is that the analysis should be performed in clones and not in populations of cells with heterogeneous expression levels of the tardigrade protein tested. For example, expression levels of the tardigrade protein needed to reduce the number of phospho-H2AX foci in response to DNA damage may interfere with cell division. We note that in the original Dsup paper, the benefit of RvDsup on cell survival was reported in specific transgenic clones. Experiments in different biological systems have also started to document toxic effects of RvDsup expression, illustrating the challenge, when performing experiments in heterologous systems, to achieve suitable expression levels of the tested protein. Trying to perform such a finer analysis, in our opinion, would go beyond the scope of our manuscript and will be best addressed in future studies. We are therefore careful in the text not to make any claim on the benefit of TDR1 expression on cell survival in response to Bleomycin in human cultured cells.

(b) From the methods I am a bit confused as to how the images were treated/foci quantified. With the automatic segmentation and foci identification, is this done through the entire Z-series or a single layer? If the latter then I am not sure the results are meaningful, since we do not know how many foci might be present in other layers of the nuclei analyzed. If the former, please clarify this in the method since it is a very important consideration.

We have acquired images throughout the entire Z-series and edited the text to make it more clear ; We now write: “ Z-stacks were maximum projected and analyzed with Zen Blue software (v2.3)...”. To limit the time needed for image analysis, we have generated an artificial image by projecting the entire Z-series into a single image and counted foci in that single maximum projection image. Although there are potential drawbacks, such as potentially only counting one focus when two foci are superposed along the Z axis, this approach overcomes the limitations of quantification from a single layer. We further ensured statistical robustness of the analysis by performing quantification from several independent fields of the labelled cells and several independent biological replicates (n>=3 as now specified in the legend of figure 6a).

(c) RvDsup reduced levels of HXA1 foci in these experiments, however, HeDsup was not found to be enriched in the transcriptomic analysis performed here. Was there a reason HeDsup was not used in the cell-based experiments? One could argue that RvDsup is from a different species of tardigrade, but it is a bit concerning that an ortholog of a protein found NOT to be induced by radiation exposure seems to perform as well (if not better) than some versions of TDR1.

RvDsup is the protein initially shown to increase survival of human HEK293 cells treated with X-rays and reduce the number of phospho-H2AX foci induced: it was therefore used as a positive control in our experiments. The sequence of HeDsup is only poorly similar to RvDsup (with 26% identity) and activity of HeDsup in cultured cells has not been reported before. We therefore believe that HeDsup is not well suited to provide a positive control for the experiments performed in our manuscript.

(d) From the methods, it seems that cells were treated with Bleomycin and then immediately fixed without any sort of recovery time. In this short timeframe, the presence of TDR1 appears to be enough to deal with a substantial amount of double-stranded breaks (as evidenced by the reduced number of HXA1 foci). Does this make sense? How quickly could one expect DNA repair machinery to make significant progress in resolving damaged DNA? This response seems much faster than what was observed in tardigrades. Perhaps the authors to comment on this.

Kinetic studies in human cells show extremely rapid repair of DNA double-strand breaks. Sensing of DNA double strand breaks by PARP proteins takes place within seconds after irradiation by IR (Pandey and Black, 2021, PMID: 33674152). NHEJ is then observed to take place by formation of 53BP1 foci within 15 minutes (Schultz et al, 2000, PMID: 11134068). The number of phospho-H2AX and 53BP1 foci peaks at 30 minutes and starts declining thereafter, showing that at a significant number of sites, DNA repair is proceeding very rapidly (by NHEJ). Although we are not aware of any studies of DNA repair kinetics in U2OS cells after addition of Bleomycin, DNA damage must be instantaneous and further take place during exposure to the drug in parallel to DNA repair, which would be expected to have similar kinetics than after irradiation with IR.

In our experiments, several mechanisms may be involved in reducing the number of phospho-H2AX foci induced by Bleomycin, such as DNA protection (for Dsup expression) or stimulation of DNA repair (for RNF146 expression). For TDR1, the molecular mechanism involved remains to be determined. Given our finding that TDR1 can form aggregates with DNA, an additional possibility is that clustering of phospho-H2AX foci is induced.

(4) I could not find the sequences of the TDR1 proteins studied here. I did find the cDNA sequence of HeTDR1 in the final supplementary file, but not the other TDR1 orthologs. In the place where it appeared the TDR1 sequences from other tardigrades should be there were very short segments of the HETDR1 sequence. All sequences of proteins used in this study should be easily accessible to the reader and reviewers as it is not possible to review this work without accessing the sequences.

Our apologies for the inappropriate documentation of TDR1 sequences in the original manuscript. As requested, we have now included the TDR1 sequences in the Supplementary Table 4.

(5) Likewise, the RNA sequence data is said to be deposited in NCBI under PRJNA997229, but I do not find this available on NCBI.

The RNA sequence data was deposited in NCBI under the indicated reference before submission of the manuscript. The data has now been released and is fully available on NCBI.

(6) A few typographical errors: e.g., Page 10 - sentence 4 has two periods ". ." or page 14 which has an open parenthesis that is not closed.

These typos have been corrected in the revised manuscript.

Reviewer #3 (Recommendations For The Authors):

We thank the reviewer for his comments.

In Figure 4C, what fraction of the 50 genes upregulated in all species and treatments are DNA repair genes? Is there any other notable commonality between these 50 genes? The bulk of upregulated genes are specific to a species and to treatment with IR or bleomycin. What fraction of DNA repair genes are specific to a species or treatment?

The results in Figure 4C on the 50 putative orthologous genes upregulated in all species and treatments are further detailed in supp Figure 10. The legend to supp Figure 10 now provides the requested information: 14/50 genes are DNA repair genes and the other notable commonality is that 21/50 are “stress response genes”. We did not further breakdown the analysis to evaluate the fraction of DNA repair genes specific to a species or treatment. It will be interesting to gather data in more species to hed light on the evolutionary history of DNA repair gene regulation in response to IR.

How does the suite of upregulated tardigrade DNA repair proteins after IR or bleomycin compare with DNA or repair proteins upregulated under similar treatments in human cells? Are they quantitatively or qualitatively different, or both?

There is a great wealth of studies documenting genes differentially expressed in human cells in response to IR (e.g. Borras-Fresneda et al, 2016, PMID: 27245205; Rieger and Chu, 2004, PMID: 15356296; Budwoeth et al, 2012, PMID: 23144912 ; Rashi-Elkeles et al, 2011, PMID: 21795128; Jen and Cheung, 2003, PMID: 12915489...). Upregulation of DNA repair and cell cycle genes is commonly found. However, the number of DNA repair genes induced is always very limited and fold stimulation very modest compared to the massive upregulation observed in tardigrades.

On page 14, please explain the acronym BER. Do the authors mean Base Excision Repair? Or something else?

As assumed by the reviewer, the acronym BER stands for Base Excision Repair. The acronym has been removed from the main text and replaced by the full name.

Reviewer #4 (Recommendations For The Authors):

We thank the reviewer for his comments.

Abstract:

The abstract is fine. What was hard to grasp at the beginning is why TDR1 gene was named that way. It should be clearer that this study decided to further focus on that gene, one of the most overexpressed gene after IR, with an unknown function. Then maybe introduce that it was found to be unique to tardigrade and to interact with DNA. Therefore, it was named TDR1.

Introduction:

The introduction has been modified according to the suggestions of Reviewer#4 below. One of the suggested references, Nicolas et al 2023 from the Van Doninck lab, was published while our manuscript was under review and cannot be considered as background information for our study.

1st paragraph:

The study is on tardigrades, I found it strange that the first paragraph is on D. radiodurans. I think it is fine to mention what is known in bacteria and eucaryotes but we should already know what will be the main topic in the first paragraph of the introduction. Some details about D. radiodurans seem less important and distracting from the main topic (3D conformation).

2nd paragraph:

When mentioning radio-resistant eurcaryotes the authors do not mention the larvae of the anhydrobiotic insect Polypedilum vanderplanki. Stating that the mechanisms of resistance are poorly characterized should perhaps be nuanced. There are some recent studies on D. radiodurans (Ujaoney et al., 2017) the insect P. vanderplanki (Ryabova et al., 2017), tardigrades (Kamilari et al., 2019), and rotifers (Nicolas et al., 2023, Moris et al., 2023). Perhaps these papers are worth indicating that if mechanisms are not elucidated yet, recent studies suggest some actors involved in their resistance. Regarding the sentence stating that DNA repair rather than DNA protection plays a predominant role in the radio-resistance of bdelloid rotifers should also be nuanced. Indeed, many chaperones, antioxidants were mentioned to play a role in the radio-resistance of bdelloid rotifers (Moris et al., 2023). The authors mentioned the reference Hespeels et al., 2023 which is not found in their list of references, I am not sure which paper they refer to. The last sentence of the second paragraph does not mean much. I am not sure what the authors want to state with this. Perhaps they should specify if they mean that the function of many other genes overexpressed after IR remains unknown.

Still, in the second paragraph, the authors focus on rotifers. They also do not mention what is known in the insect P. vanderplanki, which should be added. They still do not mention tardigrades. I think it is nice to first start with eucaryotes and then focus on tardigrades but as I mentioned before it would help to understand the aim of the paper if the first paragraph mentioned briefly the tardigrades and then could go into detail in the third paragraph.

3rd paragraph:

The sentence starting "with over 1400 species" best to remove from it "but they can differ in their resistance" and start the next sentence with that.

4th paragraph:

Very clear, we finally understand what is the focus of the manuscript.

5th paragraph:

Very clear. The authors should mention the names of the three studied species. Here, A. antarcticus is missing. The sentence "Further analyses in H. exemplaris... showed that TDR1 protein is present and upregulated". The authors should mention in which conditions the protein is upregulated. In that paragraph the authors mention phospho-H2AX: it might be good to introduce its functions before in the introduction (it is mentioned in the second sentence of the results: best to move it to the introduction).

Results:

There are a few sentences in this section which rather discuss the results than describe them. I think the manuscript might gain in quality if these interpretations of the results are moved into the discussion section. That would make the result section more concise and the discussion enriched.

For instance, I suggest to move these sentences into the discussion:

• "the finding of persistent DSBs in gonads at 72h.... likely explains...".

• "suggesting that (i) DNA synthesis..."

• " Phospho-H2AX....also suggested"

• "Moreover, expression of TDR1-GFP..., supporting the potential role of TDR1 proteins..."

• "our results suggest that RNF146 upreguation could contribute..."

• "AMNP gene g12777 was shown to increase...Based on our results, it is possible that..."

Interpretations mentioned here above were always introduced cautiously (-"suggesting that (i) DNA synthesis..." ; -" Phospho-H2AX....also suggested" ; -"Moreover, expression of TDR1-GFP..., supporting the potential role of TDR1 proteins..." ; -"our results suggest that RNF146 upreguation could contribute..." ). These cautious interpretations were usually important in deciding next steps of the work. We therefore believe it is important to mention these interpretations in the results section to clearly expose the milestones marking the progression of the study.

For some results, they were directly discussed in the results section for the sake of concision (for example -"the finding of persistent DSBs in gonads at 72h.... likely explains..."; -"AMNP gene g12777 was shown to increase...Based on our results, it is possible that..." ) since, in our opinion, there was no need to mention them again in the main discussion.

Some other parts could be good to be moved into the introduction:

• "Previous studies have indicated that irradiation with IR increases expression of Rad51,..." none of the actors involved in DNA repair are mentioned in the introduction. Also, change resistant into resistance

• "A. antarcticus ..., known for its resistant to high doses of UV....

We have moved these parts to the introduction as recommended.

It was in O. areolatus.... that the first demonstration..."

This piece of information is somewhat anecdotical. We choose to keep it it here in the results section. This information on the radio-resistance of the species P. areolatus is only relevant at this specific step of the study because it encouraged us to consider that P. fairbanksi, which we isolated fortuitously, would be a good model species for studying radio-resistance of tardigrades.

Here are some additional comments/suggestions on the result section:

1st section

• Remove the Gross et al., 2018 from the sentence "using confocal microscopy", it looks otherwise that these results are from their study, not yours.

We have changed the text to make it clear that this is indeed a finding of Gross et al which was previously made in non-irradiated tardigrades. We replicated this finding, which showed that the protocol was working appropriately, and that we could use this control result for comparison with irradiated animals. We apologize for this confusion.

The text now states: “Using confocal microscopy, we could detect DNA synthesis in replicating intestinal cells of control animals, as previously shown by (Gross et al. 2018).”

2nd section

• It is confusing what has been found induced by IR and/or by Bleomycin.

• I think it might help if the authors first present what is induced after IR, then write if it is similar after Bleomycin. Especially since they start to do it in the first paragraph of that section. However, they only mention TDR1 in the second paragraph dedicated to Bleomycin treatment which is confusing as it is also overexpressed after IR. It is also not clear if RNF146 is also induced by Bleomycin.

As recommended, the text presents first what is induced after IR and then what is induced by Bleomycin in the following paragraph. When reporting results with Bleomycin, we have provided a global assessment of what is common to both treatments in Supp Figure 3 and in Supp Table 3. In this figure, we also specifically highlighted several key genes of DNA repair induced by both treatments. These are also mentioned in the text (p8) to illustrate the point that many key DNA repair genes are common to both treatments. We have now added RNF146 to that list as recommended.

• Regarding TDR1, it is not clear when introduced in the text as "promising candidate" why it is the case. It is clear in the figures but perhaps the authors should explain why they chose these genes for further analyses: high log2foldchange and expression level for instance. Regarding that last comment, it would be interesting to have an idea about the expression level of the genes with high log2foldchange. In Figures 2, 3, and 4 the pvalue and log2foldchange are represented but not the expression level (ideally Transcript per Millions). These values would give an additional idea on the importance of that gene. While looking at the figures, it is unclear why you did not further characterize other genes with high log2foldchange (some with even hints of their function): the mentioned RNF146, macroH2A1 (not even mentioned in the results), some genes unannotated in the figures with likely unknown functions,

When selecting genes of interest, we did indeed take into account high expression levels. To more clearly document expression levels (which were already available from the Tables), we added MAplots (representing log2foldchange and logNormalized read counts) in the supplementary materials (Supp Figure 3 and Supp Figure 8).

• It is also unclear at that stage why you named it "Tardigrade DNA damage response protein", as it is characterized as DNA repair/damage proteins by specific GO id or is it based on your downstream analyses, I think it might be worth to quickly mention the reason of that name.

The name illustrates two points which were already characteristic at this point in time of the study i.e. 1) it is a tardigrade specific protein and 2) it is induced in response to DNA damage.

• Regarding the BLAST analyses the protein was searched in C. elegans, D. melanogaster and H. sapiens. Why only these three species? What were the threshold evalues used for these analyses. As mentioned in the main comment, it would be worth searching species phylogenetically close to tardigrades to verify if it is well-tardigrade specific. Did you try to make a gene tree, after looking for a conserved domain (using hmmersearch)?

As indicated in the methods section, the “Tardigrade-specific" annotation was determined by absence of hits after high-throughput alignment (with diamond using –ultrasensitive-option) on the NCBI nr database and absence of hits after blast search on C. elegans, D. melanogaster and H. sapiens proteomes as a complementary criterion (the latter blast search was primarily performed to enrich for functional annotations). Based on these criteria, TDR1 was annotated as “Tardigrade-specific”. As stated in the text, we also searched for TDR1 related sequences with 1) blastp (which is more sensitive than diamond) on the NCBI nr database and 2) HMMER on Reference Proteomes, and no hits were found among non-tardigrade ecdysozoans organisms, confirming TDR1 is specific to tardigrades. For Blast search for example, there were five hits in non-ecdysozoans organisms (two cephalochordates, one mollusc and two echinoderma). The blastp and HMMER results are now included in the revised supplementary material (Supp Table 5). These very few hits in species phylogenetically distant from tardigrades cannot be taken to support the existence of TDR1 genes outside tardigrades.

To be clearer in the manuscript, we now state the absence of hits for TDR1 in non-tardigrade ecdysozoans. Given the absence of homologs in non-tardigrade species, it is not possible to make a gene tree with non-tardigrade species.

• Page 9: "Proteins extracts from H. exemplaris... at 4h and 24h..." I think this sentence can be removed as this is mentioned again 2 paragraphs after: "...we conducted an unbiased proteome analysis... at 4h..." The log2foldchange threshold mentioned for the proteomic analyses is 0.3: why this threshold, was it chosen randomly?

This is threshold is commonly used when considering log2foldchange with the technology used in our study, an isobaric multiplexed quantitative proteomic strategy which is known to compress ratios (Hogrebe et al. 2018).

• Page 10:

It would be good for more clarity to indicate at the beginning of the new section which species were investigated after IR or Bleomycin treatment.

TDR1 homologs in the other tardigrade species were identified based on what? Best reciprocal hit?

As indicated in the methods section of the manuscript, we searched for homologs in other tardigrade species by BLAST. A best reciprocal hit approach was not performed to try to determine which homologs might be orthologs. In particular, most TDR1 homologs identified are known from transcriptome assemblies and high-contiguity genome assemblies are needed to more confidently identify orthology (using synteny). The results of the BLASTP search are now provided as supplementary material (Supp Table 5).

Preliminary experiments indicated that A. antarcticus and P. fairbanski survived exposure to 1000 Gy: is there a supplementary graph showing this?

We have corrected the text to avoid any confusion. We have not rigorously examined the dose-dependent survival of P. fairbanksi in response to irradiation. Text was changed to: “We found by visual inspection of animals after IR that A. antarcticus and P. fairbanksi readily survived exposure to 1000 Gy.”

• Page 11:

"A set of 50 genes was upregulated in the three species": please be precise if only after IR.

Done

These genes cannot be the same as they are from different species. Did the author mean that they are coding for similar proteins? It might be good to give some more details even if the supplementary figure is mentioned.

Obviously, these genes are putative orthologs. We have changed the text to:

” a set of 50 putative orthologous genes was upregulated in response to IR in all three species”

Discussion:

• General comment: the discussion is focused mainly on TDR1, it would be nice to also discuss the other results: DNA repair genes, RNF146.

A whole paragraph is devoted to discussion of results on DNA repair genes and RNF146. We have extended that discussion following on the suggestion of the reviewer. In particular, we have explicitly mentioned the apparent paradox that XRCC5 and XRCC6, which are among the most highly stimulated genes at the mRNA level, only display modest upregulation at the protein level. Although further studies would be needed to examine the mechanisms involved, we propose that upregulation of RNF146, whose human homolog has been shown to drive degradation of PARylated XRCC5 and XRCC6 proteins in response to IR (Kang et al. 2011), may be responsible for higher degradation rates and may thus counterbalance increased levels of protein synthesis.

• Pulse field electrophoresis would be nice to be performed. It has been used to assess DSBs in bdelloid rotifers, is it possible in tardigrades?

As stated in the discussion, we believe that it would be challenging to perform pulse field electrophoresis in tardigrades. However, if possible, these experiments would certainly bring invaluable information to complement our analysis of DNA damage induced by IR.

• "By comparative transcriptomics": please rephrase that sentence.

• Proteins acting early in DNA repair: I am not sure I understand this sentence. Actors as ligases act not at the beginning of the repair pathways.

Well noted. We have removed ligases from the list.

• It is confusing that the authors mention NHEJ and double-strand break repair pathways as different pathways. There are 2 main pathways to repair DBSs: NHEJ and HR. It would be nice to add a reference to the sentence "PARP proteins act as sensors of DNA damage etc."

A typo in the sentence gave rise to the misleading suggestion that NHEJ is not a double strand repair pathway. It has been corrected.

A reference has been added for PARP proteins.

• It would be nice if the authors can explain deeper their suggestion that degradation of DNA repair actors is essential for tardigrade IR resistance.

We have expanded this part of the discussion and hope that it is clearer.

“For XRCC5 and XRCC6, our studyestablished, by two independent methods, proteomics and Western blot analysies, that the stimulation at the protein level could be much more modest (6 and 20-fold at most (Supp Figure 6) than at the RNA level (420 and 90 fold respectively). This finding suggests that the abundance of DNA repair proteins does not simply increase massively to quantitatively match high numbers of DNA damages. Interestingly, in response to IR, the RNF146 ubiquitin ligase was also found to be strongly upregulated. RNF146 was previously shown to interact with PARylated XRCC5 and XRCC6 and to target them for degradation by the ubiquitin-proteasome system (Kang et al. 2011). To explain the lower fold stimulation of XRCC5 and XRCC6 at the protein levels, it is therefore tempting to speculate that, XRCC5 and XRCC6 protein levels (and perhaps that of other scaffolding complexes of DNA repair as well) are regulated by a dynamic balance of synthesis, promoted by gene overexpression, and degradation, made possible by RNF146 upregulation. Consistent with this hypothesis, we found that, similar to human RNF146 (Kang et al. 2011), He-RNF146 expression in human cells reduced the number of phospho-H2AX foci detected in response to Bleomycin (Figure 6).”

• Page 15: Please add a reference for the sentence "Functional analysis of promotor sequences in transgenic tardigrades etc."

The reference has been added to fix this omission.

Material and Methods:

Small comments:

• 40 μm mesh: space missing

• 100 μm mesh: space missing

• (for Bleomycin)): parenthesis missing

• remove "as indicated in the text"

• The investigated time points after radiation need to be clearly stated in the method section. It is also unclear in the IR and Bleomycin section which tardigrades were treated with what. Not all were treated with Bleomycin.

The small comments above have been fixed in the revised version of the manuscript.

• Page 21: please precise the coverage of the RNA sequencing

Statistics on mapping of RNAseq reads are now provided in Supp Table 10.

• Page 22: Was any read trimming performed? Anything about the quality check of the reads?

Trimming was conducted using trimmomatic (v0.39) and quality check using FastQC (v. ?) This information has been added to the Methods section.

• Were the analyses confirmed by a second approach: for instance, EdgeR? Deseq2 and EdgeR do not always have the same results. For more robust analyses it is advised to use both.

Differential transcriptome analyses were conducted with DESeq2 only. The robustness of our identification of differentially expressed genes in response to IR stems from performing comparative analyses in three different species, rather than from using two bioinformatics pipelines in a single species. We also note that benchmarking reported in the initial DEseq2 paper showed that identification of differentially expressed genes with large log fold changes (which, as reported in our manuscript, is characteristic of many DNA repair genes in response to IR) is very consistent between DEseq2 and EdgeR.

Figures:

• Figure 2: Legend vertical dotted line does not indicate log2foldchange value of 4 in all panels: it would be good to indicate for panels a and c as well.

Figure 2has been improved following on the suggestions of the reviewer. Dotted lines now show log2foldchange value of 2 in all panels (ie Fold Change of 4 as mentioned in the main text).

• Figure 2C: There are a few points with high log2foldchange which are not annotated: was it because nothing was found in the blast research? If yes, it would be good to indicate their functions. If not, it would be good to mention in the discussion that there are some genes with still unknown functions which might play an important role in the resistance of tardigrades to IR.

The few points which are not annotated in figure 2c can now be found in Supp Table 3 Some of them have no hit in Blast search, some others such as BV898_09662 or BV898_07145 have hits on DNA repair genes as RBBP8/CtIP or XRCC6 respectively but are not annnotated as such by eggnog in KEGG pathway.

• Figure 4C: Why not have included the response of P. fairbanski to bleomycin? I guess it was not done, but it is unclear in the results and methods sections.

P.fairbanksi response to bleomycin wasn’t assessed as we didn’t get enough animals to run the study. The method section has been modified to precise this point.

Reviewer #1 (Public Review):

Summary:

The manuscript aims to provide insights into the mediators and mechanisms underlying tardigrade radiation tolerance. The authors start by assessing the effect of ionizing radiation (IR) on the tardigrade lab species, H. exemplaris, as well as the ability of this organism to recover from this stress - specifically they look at DNA double and single strand breaks. They go on to characterize the response of H. exemplaris and two other tardigrade species to IR at the transcriptomic level. Excitingly, the authors identify a novel gene/protein called TDR1 (tardigrade DNA damage response protein 1). They carefully assess the induction of expression/enrichment of this gene/protein using a combination of transcriptomics and biochemistry - even going so far as to use a translational inhibitor to confirm the de novo production of this protein. TDR1 binds DNA in vitro and co-localizes with DNA in tardigrades.

Reverse genetics in tardigrades is difficult, thus the authors use a heterologous system (human cells) to express TDR1 in. They find that when transiently expressed TDR1 helps improve human cell resistance to IR.

This work is a masterclass in integrative biology incorporating a holistic set of approaches spanning next-gen sequencing, organismal biology, biochemistry, and cell biology. I think the importance of the findings is suitable and honestly, I find very little to critique in their experimental approaches.

Overall, I find this to be one of the more compelling papers on tardigrade stress-tolerance I have read.